do private prisons a ect criminal sentencing?above evidence, it seems of course likely that legal...
TRANSCRIPT
Do Private Prisons Affect Criminal Sentencing?∗
Christian Dippel† Michael Poyker‡
June 18, 2020
Abstract
Using a newly constructed complete monthly panel of private and public state prisons,
we ask whether private prisons impact judges’ sentencing decisions in their state. We
employ two identification strategies, a difference-in-difference strategy comparing court-
pairs that straddle state-borders, and an event study. We find that the opening of
private prisons has a large effect on sentence lengths shortly after opening but this
effect dissipates once the prison is at capacity. Public prison openings have no such
effects, suggesting that private prisons have an impact on criminal sentencing that
public ones do not.
Keywords: Private Prisons, Criminal Sentencing
JEL Codes: D72, H76, K41,
∗We are grateful to Anna Harvey, Daniel Nagin, Joseph Stiglitz, and conference and seminar participants at CELS, ColumbiaUniversity, MPSA, the Urban Institute, UCLA, and SIOE, for valuable comments. We thank Sean Keegan and Afriti Rahim forexcellent research assistance, and the Sentencing Commissions of Alabama Arkansas, Colorado, Georgia, Kentucky, Maryland,Minnesota, Mississippi, Nevada, North Carolina, Oregon, Tennessee, Texas, Virginia, and Washington for share their sentencingdata with us. Dippel is grateful for financial support from a Center for American Politics and Public Policy Research Fellowshipfor this project.†University of California, Los Angeles, and NBER.‡Columbia University.
1 Introduction
Of the fourteen candidates for the Democratic Party presidential nomination in December 2019,
twelve had explicit platforms to eliminate all private prisons, a position also shared by the Clinton
campaign in the 2016 race.1 This unified position is explained by two primary concerns that override
the appeal of private prisons’ lower costs of incarceration. The first concern is that private prisons
shirk on non-contractible dimensions of quality, e.g. lower-quality rehabilitation programs which
lead to higher rates of recidivism (Inspector General, 2016; Eisen, 2017). The second concern is that
private prisons may have a negative impact on the application of justice or on judicial institutions
(Mattera, Khan, LeRoy, and Davis, 2001; Ashton and Petteruti, 2011; Shapiro, 2011; Hartney and
Glesmann, 2012; Mason, 2012). In its most deleterious form, this concern was manifested in the
2011 “kids for cash” scandal, in which two Pennsylvania judges took bribes from private detention
facilities in exchange for harsher juvenile sentences.2
While the first concern has been analyzed both theoretically (Hart, Shleifer, and Vishny, 1997)
and empirically (Bayer and Pozen, 2005; Thomas, 2005; Spivak and Sharp, 2008; Mukherjee, 2019),
the second concern has not yet been the subject of any causally identified empirical analysis.
Our study provides the first rigorous analysis of this question — whether private prisons impact
sentencing decisions — based on a newly constructed monthly panel dataset of the geo-location
and capacity of the universe of all private and public state prisons from 1980 to today. We combine
these data with newly collected data on criminal sentencing in thirteen states’ trial courts.3 We
focus on state trial courts because, unlike federal courts, convicts from state courts are sent to the
same state’s prisons. Furthermore, trial courts are the states’ primary courts of general jurisdiction,
and as such handle the vast majority of all criminal cases in the U.S.
For identification, we conduct a generalized difference-in-difference strategy in a contiguous-
border court-pair (CBCP) sample. This means we rely on within-state changes in private-prison
capacity (driven by openings and closings, but equally by capacity expansions and contractions of
1 As of December 2nd, see www.politico.com/2020-election/candidates-views-on-the-issues/criminal-
justice-reform/private-prisons/.2 The growth of the private prison system in the last three decades has coincided with a huge increase in the
U.S. prison population: in the roughly three decades since the first private prison in the U.S. opened in 1984, theimprisoned population has increased by 194 percent relative to a general population increase of 36 percent (Bureauof Justice Statistics, 1984, 2015).
3 Data on state-court sentencing is handled by each state separately, many of whom have not digitized their datayet. Obtaining data for 13 states was the result of a three year process of requesting data from every single state.
1
prisons), and compare the resulting changes in sentencing across states only within neighboring
trial court pairs on either side of a state border. By focusing only on CBCPs, we are able to
account for local heterogeneity and local unobserved trends in criminal activity, policing, and the
local residents’ attitudes, all of which may correlate with criminal sentencing.4
We find that a 0.42 percent increase in private prison capacity (the average associated with a
newly opened prison in the data) increases sentence lengths in that state’s courts by roughly one
percent, or 12 days, compared to adjacent courts that are in neighboring states and not affected by
the prison capacity change. The effect is robust to many variations of spatial, time, and judge fixed
effects. The baseline effect includes probations (zero-sentences) and thus combines the intensive
margin of sentence length with the extensive margin of going to prison. When we drop probation
observations, the intensive margin effect of a 0.40 percent increase in private prison capacity is an
increase in sentence length of 10 days. We find no such effect of capacity changes in public prisons
on sentencing.
The changes in private prison capacity and public prison capacity that the difference-in-difference
strategy identifies are frequent and consist of a mix between smaller adjustments and large open-
ings. Because of this, we need an event study design focused on major changes to get enough power
to investigate the timing of the effect of private prison changes. While the effects in the CBCP
strategy are estimated over the full post-period of all prison capacity changes, the event study
investigates the sharp events of prison openings and closings. For this purpose, the data contain 40
private prison openings (including three privatizations of public prisons) 13 private prison closings,
42 public prison openings, and 27 public prison closings (exclusive of three privatizations). The
event study setup shows that the opening of a private prison leads to a three-month increase in
sentence length for cases decided within the first two months after the opening, but a precisely
estimated zero-effect thereafter. In other words, defendants who happen to stand trial shortly after
a private prison opens can expect to be sentenced to three additional months relative to otherwise
identical defendants who stand trial for the same crime a few weeks earlier or later. A back-of-
the-envelope calculation shows that it takes two-and-a-half months for new convictions in a states’
courts to fill the capacity of the average newly opened private prison. In short, private prisons
4 The identification-advantages of state border discontinuities have been explored, among others, in the contextof labor market regulation (Dube, Lester, and Reich, 2010), manufacturing (Holmes, 1998), and banking (Huang,2008).
2
appear to have an effect on sentencing precisely as long as they have vacant capacity. There are no
pre-trends in sentencing before a private (or public) prison is opened. Interestingly, however, pri-
vate prison closings are preceded by a strong negative pre-trend (sentences getting shorter), which
may be anticipatory: defendants are not sent to facilities that are closing soon. There are no such
pre-trends before public prison closings. Finally, public prison openings and closings have precisely
estimated zero-effects on sentencing, despite being very similar in magnitude (i.e., average capacity
change) to private prison ones.
How, then, do private prisons impact judges’ sentencing decisions? There are two potential
explanations. The first—more deleterious— explanation is that private prison companies may
directly influence judges, for example through campaign contributions or even outright bribes as
in the “kids for cash” scandal. A second possibility is that judges internalize the cost-savings
associated with private prisons, consistent with other evidence that judges trade off benefits of
longer sentences (primarily lowered recidivism) against their fiscal burden (Ouss, 2018; Mueller-
Smith and Schnepel, 2019).5 The cost-savings motive resonates particularly with the core effect
being concentrated in the two months after a prison’s opening because most states guarantee
private prisons to pay for an occupancy of between three-quarters to ninety percent of their bed
capacity (In the Public Interest, 2013), effectively reducing the marginal fiscal burden of an inmate
to zero up to this guaranteed occupancy. (Of course, this identity of our estimated effect-length
and the cited back-of-the-envelope cost-savings calculation could be co-incidental. We cannot rule
out that the salience of a newly opened private prison simply wears off in a judge’s mind after two
months.) We can measure cost savings from state laws governing private prison contracts. We find
that private prisons indeed have more pronounced effects on sentencing when their cost-savings
are larger (which should also reduce rents from direct influence), both in the CBCP difference-in-
difference identification strategy and in the event study.
A ‘direct influence’ channel of private prisons to judges is inherently more difficult to measure.
However, the literature on ‘electoral sentencing cycles’ suggests an indirect test for such influence.
It shows that electoral competition leads judges to levy harsher sentences in the lead-up to elec-
tions (Huber and Gordon, 2004; Berdejo and Yuchtman, 2013; Dippel and Poyker, 2019; Abrams,
Galbiati, Henry, and Philippe, 2019). The presence of such cycles implies that ‘direct influence’
5 Of course, judges may also internalize the costs to defendants.
3
by private prisons should be most important when judges are seeking re-election (by way of cam-
paign contributions). This suggests the testable hypothesis that under the ‘direct-influence’ story,
private prisons should have more pronounced effects on sentencing when judges are coming up for
re-election. We find considerable evidence for the presence of ‘electoral sentencing cycles’ in our
data, but we find no evidence that the effect of private prisons on sentencing varies with these
cycles. Overall, the evidence is thus more consistent with the cost-savings explanation than with
the direct-influence explanation fore the main effect we document.
Our paper contributes to a literature on judicial decision making, and in particular the “extra-
legal considerations” of judges (Posner 2008, p8-11). Amongst these are the fiscal costs of incarcer-
ation (Ouss, 2018), prisons’ capacity constraints (Mueller-Smith and Schnepel, 2019), defendants’
race (Steffensmeier and Demuth, 2000; Abrams, Bertrand, and Mullainathan, 2012; Park, 2014),
media scrutiny (Lim, Silveira, and Snyder, 2016), judges’ own characteristics like gender, ethnicity
and party affiliation (Lim and Snyder, 2015; Lim, Snyder, and Stromberg, 2015), their re-election
concerns (Huber and Gordon, 2004; Berdejo and Yuchtman, 2013; Abrams et al., 2019), and even
their emotions on the day (Eren and Mocan, 2018). We show that the presence of private prisons
needs be added to the list of extra-legal considerations, and that their impact is most likely ex-
plained by judges’ considering the fiscal costs of incarceration.6 Although a ‘direct influence’ effect
would be yet more deleterious, the ‘costs savings motive’ on its own also raises equity concerns
about the effect of private prisons on the application of justice in U.S. courts. Notwithstanding the
above evidence, it seems of course likely that legal sentencing considerations will usually dominate
extra-legal ones, especially for more severe cases. Owens (2011), for example, finds that judges
tend to follow their states’ truth-in-sentencing (TIS) guidelines for violent offenders even in cases
where they have the discretion to reduce incarcerations costs by not following these guidelines.
In our data, the effect is likely to be coming from medium-severity crimes because there are no
high-security private prisons.
6 Galinato and Rohla (2018) investigate the same question as us through the lens of a game-theoretic model, inwhich judges care about prison capacity constraints as well as bribes from private prisons. They provide evidence infavor of the direct influence mechanism but they lack a plausible identification strategy and the right data, becausethey use an “off the shelf” sample of federal criminal trials from the federal U.S. Sentencing Commission (USSC).Like us, they relate sentence length to the presence of private prisons in the same state, but this approach is notvalid in the USSC data because (i) there is no spatial relation between the location of a federal court and where inthe federal prison system a convict is sent to, and because (ii) the USSC includes no data on a crime’s severity andthe defendant’s criminal history.
4
There is a closely related literature on the consequences of judicial decision making for defendant
outcomes (Kling, 2006; Di Tella and Schargrodsky, 2013; Galasso and Schankerman, 2014; Aizer
and Doyle Jr, 2015; Dobbie, Goldin, and Yang, 2018; Mueller-Smith and Schnepel, 2019; Norris,
Pecenco, and Weaver, 2019; Bhuller, Dahl, Løken, and Mogstad, 2020).7 In this literature, we relate
closely to Mukherjee (2019). Focusing on Mississippi, and using changes in private prison capacity
over time as an instrument for whether an individual serves time in a private prison, Mukherjee
finds that this increases a convict’s total time incarcerated (holding fixed the sentence) because
private prison inmates receive more infractions, thus delaying parole. This pro-longed incarceration
wipes out half the savings from the lower cost of private prisons. Concerningly, Mukherjee finds
that longer incarceration in private prisons does not reduce recidivism upon release, which runs
counter to existing evidence that longer incarceration does in general reduce recidivism (Owens,
2009; Kuziemko, 2013; Hansen, 2015; Bhuller et al., 2020). This is explained by the lower quality of
rehabilitation programs in private prisons, providing prima facie evidence for the concern originally
formalized in Hart et al. (1997). Mukherjee’s and our findings amplify one another with regards
to equity concerns because they suggest that defendants who happen to stand trial shortly after a
private prison opens can expect to not only receive longer sentences but also serve a larger portion
of these sentences, while potentially receiving lower-quality rehabilitative programs.
2 Data Sources and Construction of Samples
2.1 Prison Data
The U.S. private prison industry began in the early 1980s, when the rising cost of state-run prisons
started becoming a fiscal problem for state governments.8 The first privately run corrections facility,
Hamilton County Jail in Tennessee, was opened in 1984 (visible in the top-panel of Figure 1). It
was run by Corrections Corporation of America (CCA). Only a year later, CCA proposed to take
over the entire prison system of Tennessee. This did not happen, but 1984 nonetheless marked the
start of a rapid expansion of the private prison industry.
7 For identification, most of these papers use judge fixed effects coupled with random assignment of judges tocases. Because of the need to link sentencing data to other defendant outcome data, these papers typically use dataon just a single county or at most one state. In contrast, we use data for 13 states.
8 There was a 19th century history of private prisons in the United States dating back to the first private prison’sestablishment in San Quentin in 1852. See (McKelvey, 1936, ch.1-2).
5
The monthly panel dataset of private and public state prisons we use in this paper was con-
structed from several sources. First, we use the the 1979, 1984, 1990, 1995, 2000, 2005, and 2012
waves of the ‘Census of State and Federal Adult Correctional Facilities’ (CSFACF). Those censuses
record for all U.S. prisons when they opened, whether they are private or public, their capacity
(measured in beds) and when it was changed, and if they house male, female, or both convicts. We
focus only on state prisons. We then used each state’s Departments of Correction website to update
the base data to include prisons after 2005.9 The top-panel of Figure 1 displays the evolution of
PrivateCct and PublicCct, i.e., the capacity (in beds) of private and public prisons, in Tennessee.
Capacity can change because of the expansion, contraction or closing of existing facilities, or the
opening of new ones. Bigger capacity changes (above 200 beds) are almost always the result of
openings or closings. The time range is determined by the availability of the sentencing data, which
we discuss next.
2.2 The Sentencing Data
We focus on state trial courts’ sentencing decisions in felony offenses.10 Private prisons in our data
are for male prisoners only, and we therefore focus our analysis on the effect of male prisons on the
sentencing of male defendants (which generates a natural placebo exercise of looking at sentences of
female defendants). Each state maintains their own sentencing data, and we separately requested
these data from every states’ Sentencing Commissions and Departments of Corrections. Many
states do not maintain an organized electronic repository of their court cases, or do not share it.
Nonetheless, we were able to obtain sentencing data from 15 states: Alabama, Arkansas, Colorado,
Georgia, Kentucky, Maryland, Minnesota, Mississippi, Nevada, North Carolina, Oregon, Tennessee,
Texas, Virginia, and Washington. Obtaining these data from each state separately took several
years and the process was quite idiosyncratic. Appendix A.2 provides details on how we obtained
the sentencing data in each state. Colorado and Minnesota are the only states in our data that
do not have a neighboring state within the sample, which reduces the effective number of states
to 13 in our contiguous-border court-pairs (CBCP) identification strategy. Figure 2 shows these 13
states (in light blue) as well as the counties on their borders (in dark blue), which are discussed in
9 Details in Appendix A.1.10 This excludes courts of limited jurisdiction, such as family courts and traffic courts, and, excludes crimes of
minor severity amongst the courts of general jurisdiction.
6
Figure 1: Private and Public Prison Capacity in Tennessee and Mississippi
Panel A: Prison Capacity Variation in Tennessee
020
0040
0060
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00#
Beds
(priv
ate
pris
ons)
040
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Beds
(pub
lic p
rison
s) (D
ashe
d Li
ne)
1982 1986 1990 1994 1998 2002 2006 2010 2014Year
TN
Panel B: Prison Capacity Variation in Mississippi
020
0040
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(priv
ate
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ons)
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000
# Be
ds (p
ublic
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(Das
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)
1990 1992 1994 1996 1998 2000 2002 2004 2006 2008 2010 2012 2014Year
MS
Notes: The top-panel shows the evolution of the capacity of private and public prisons in Tennessee. The bottom-panel shows the evolution of the capacity of private and public prisons in Mississippi, where our data are very similarto Figure 1 in Mukherjee (2019). The dashed (red) line is the state-specific time-series of public prison capacity(number of beds). The solid (blue) line is the state-specific time-series of private prison capacity (number of beds).The time range in each state is determined by sentencing data availability. Tennessee has openings in 1984, 1992, 1997,2002, and 2016. (The figure includes the opening of the very first privately operated state-run prison in Tennessee’sHamilton County in 1984.) Mississippi has private prison openings in 1996, 1998, 1999, 2000, 2001, 2004, and 2008,and closings in 2002 and 2013.
7
Figure 2: The Border-Pair Data
Notes: This figure shows the 13 states (in light blue) in our sample, and the 252 border-counties thin this sample (indark blue).
Section 2.3.
2.3 Border-Pair Sample Construction
Why prison-capacity changes are state-wide changes: The location of prisons, both public
and private is determined in state legislatures. Locations are selected with economic considerations
in mind, typically in structurally weak areas and with a view towards providing local employment
opportunities (Mattera et al. 2001, p.7, Chirakijja 2018, p.6). Often such structurally weak areas
actively compete in lobbying the state legislature for the construction of a prison (private or public)
in their county. For example, Mattera et al. (2001, p.22) recounts how the collapse of the oil boom in
the late 90s, and the resulting dearth of local jobs, was a driving factor in allocating the construction
of an Oklahoma private prison to the town of Hinton. Similar examples abound in the same and in
other sources. The location of a newly opened prison is therefore endogenous to local factors that
could also impact local crime and therefore sentencing. This implies that using a court’s distance
to a private prison as a source of variation is endogenous, despite its intuitive.11
Once we think of PrivateCct and PublicCct as state-level changes, the contiguous-border court-
pair (CBCP) sample offers the cleanest spatial comparison because it is amenable to non-parametrically
11 For completeness, we do report regressions where the treatment is a distance-weighted sum of private prisoncapacities in a state in Table A4.
8
controlling for unobserved local trends (Dube et al., 2010; Holmes, 1998; Huang, 2008).12 In our
setting, this means trends in criminal activity, policing and in the local electorate’s demand for
sentencing. Trial court districts in our data are always the same as counties. Our CBCP identi-
fication sample therefore consists of all the county-pairs in our data that straddle a state border.
This amounts to 252 border counties out of of total of 417 counties in our 13 states. These border
counties are mapped to 237 distinct county-pairs.
Table 1: Contiguous-Border County-Pairs
Segment 1 2 1 2 #pairs y-start y-end #years
1 OR WA 10 11 20 2004 2015 112 OR NV 3 2 4 2004 2015 113 AR MS 5 6 10 1990 2016 264 AL MS 10 12 21 2002 2016 145 TN MS 5 6 10 1990 2016 266 AR TN 2 4 6 1980 2017 377 TN GA 4 6 9 2010 2016 68 NC GA 4 4 7 2010 2016 69 AL GA 11 17 27 2010 2016 6
10 TN NC 9 10 18 2006 2016 1011 TN VA 5 5 9 2007 2016 912 MD VA 8 10 17 2007 2016 913 NC VA 15 14 28 2007 2016 914 KY VA 4 4 7 2007 2016 915 AL TN 4 7 10 2002 2016 1416 TN KY 14 17 30 2002 2017 1517 AR TX 2 2 4 2010 2016 6
Total 237
Pairs #counties Sentencing overlap
13
Notes: This table decomposes the sample of 237 border-counties into 17 state-border segments. The table clarifieshow many border-segments are linked to each state, and which segments are dropped when a state is dropped fromthe analysis, as the robustness check reported in Figure 3 will do. The table also clarifies what years of sentencingdata are used in each border segment, where the constraint on each segment is the state with less available sentencingdata.
We provide a detailed breakdown of the number of counties and pairs on each state-border
segment in Table 1. This table clarifies how many border-segments are linked to each state, and
also reports on the years covered by each state’s sentencing data, with varying coverage of the years
1980 to 2017. Tennessee, for example, is the most ‘connected’ state in our data, sharing border-
12 See Dube et al. (2010) for a taxonomy of the differences between identifying the effect of state-level policychanges in a “full sample” of all counties vs identifying the same changes in a border-county sample.
9
segments with seven states (segments # 5, 6, 7, 10, 11, 15, 16). also clarifies how many years of
sentencing data are used for each border segment: The years covered by each state’s sentencing data
vary somewhat, ranging from 1980 to 2017, and the years included in a border-pair are determined
by the state with less sentencing data coverage. For example, Tennessee’s data sentencing data
goes back to the 1980s. There are 26 years of data in its border-pairs with Mississippi (segment
#5), whose data also go back to 1990. By contrast, there are only 6 years of data in its border-pairs
with Georgia (segment #7), whose sentencing data only goes back to 2010. The years included in a
county-pair are determined by the state with less sentencing data coverage. For example, there are
26 years of data in Tennessee’s border-segment with Mississippi, because Mississippi’s data cover
1990–2016 and Tennessee’s cover 1980–2016.
While the advantages of border-discontinuities in terms of statistical identification do not re-
ally depend on this, the generalizability of the results will be higher if the border counties are
representative of all counties in a state on observable characteristics. Table A2 shows that the
socio-economic characteristics of border-court counties are not statistically different from all other
counties in the same states. Further, Figure A2 provides an illustration of the identifying variation
in a border-segment, using as an example the border-segment shared by Georgia and Tennessee.
3 The Effect of Private Prisons on Criminal Sentencing
Section 3.1 presents the results of the generalized difference-in-difference estimation strategy in
the CBCP sample described in Section 2.3, where we regress sentence length on changes in private
and public prison capacity, as well as defendant and crime characteristics. In Section 3.2, we focus
only on sharp openings and closings of private and public prisons in an event study framework.
Section 3.3 provides suggestive evidence on the mechanisms.
3.1 The Effect of Private Prisons on Sentencing
The empirical specification we will estimate is
log(sentence)i(ct) = βT · log(PrivateC)st+βT’ · log(PublicC)st+βX ·Xi+µc+µp(c)tµst++εicts, (1)
10
where case i is heard in court c at time t. We use log(·) as shorthand for the inverse hyperbolic
sin which can be interpreted in the same way as the log function but allows us to keep zero values
in private prison capacity.13 Xi are characteristics of the crime and of the defendant. The CBCP
design is reflected in the combination of a fixed effect µc that absorbs fixed county-differences in
local social, political and economic conditions, state-specific time-trends or period fixed effects µst
that control for change in the policing, laws and judicial system, and court-pair time-trends or
period fixed effects µp(c) that absorb unobserved changes in local social, political and economic
conditions.
Panel A in Table 2 presents the baseline results of estimating equation (1). Specifications get
incrementally more demanding across columns: Column I reports results for the specification with
(time-invariant) court-pair fixed effects µp(c) and state-specific year- and fiscal-year fixed effects
µst.14 Column II adds defendant characteristics subsumed in Xi. In particular, we include for a
dummy for recidivism, age, age squared, and race (Asian, Black, Hispanic, and Native American).
Column III adds controls the severity of the crime, also subsumed in Xi.15 Column IV uses
pair-specific year fixed effects as a more flexible version of µp(c)t. Finally, column V adds pair-
specific time controls µp(c)t in the form of a pair-specific linear trend that increments in months.
Finally, column VI adds a specification with judge fixed effects. Unfortunately, we only have
judge identifiers in nine of the 13 states’ sentencing data.16 Nonetheless, judge fixed effects are
an important robustness check given the large “judge fixed effect” literature. It is reassuring that
judge fixed effects add considerably to the regressions’ R-squared but do not move our coefficient of
interest. A 0.42 percent increase in private prison capacity (equal the average state-wide capacity
increase from a newly opened prison in our data) increases sentence lengths by roughly 12 days
(a roughly one-percent increase, 0.42 × 0.021, multiplied by a mean sentence length of 45 months)
compared to adjacent courts that are in neighboring states and not affected by the prison capacity
change. This point estimate is precisely estimated and also practically unchanged in magnitude
13See Burbidge, Magee, and Robb (1988); Card and DellaVigna (2017).14 Calendar years are important because legislation (which can affect sentencing) usually changes on the 1st of
January. Fiscal years are important because many transfer programs that can affect crime (like Supplemental NutritionAssistance Programs) change with fiscal years. Fiscal years in our data end on March 31st, June 30th or September30th.
15 States report crime severity in varying ways, using ordinal scales or cardinal scales. To combine these differentclassification schemes into a single regression we turn them into state-specific sets of fixed effects.
16 In states without judge identifiers we use the court fixed effect as a placeholder.
11
Table 2: The Effect of Private Prisons on Sentence Length
I II III IV V VIPanel A: baseline Dependent variable: Sentence (log months)Log private prison capacity 0.022** 0.021** 0.020** 0.018** 0.020** 0.021*
[0.0208] [0.0336] [0.0311] [0.0322] [0.0432] [0.0583]
Log public prison capacity -0.166 -0.133 -0.094 -0.113 -0.159 -0.142[0.5986] [0.6353] [0.7507] [0.7408] [0.6320] [0.6955]
R-squared 0.379 0.390 0.455 0.468 0.468 0.474Observations 765,338 765,338 765,338 765,338 765,338 765,338
Panel B: exclude probation
Log private prison capacity 0.014*** 0.013*** 0.012*** 0.012*** 0.014*** 0.013***[0.0000] [0.0000] [0.0000] [0.0000] [0.0000] [0.0000]
Log public prison capacity -0.326 -0.309 -0.297 -0.361 -0.343 -0.346[0.1410] [0.1097] [0.1017] [0.1567] [0.1549] [0.1570]
R-squared 0.380 0.392 0.515 0.530 0.530 0.535Observations 570,674 570,674 570,674 570,674 570,674 570,674
Panel C: Dependent variable: D(Incarceration / No Probation)
Log private prison capacity 0.002 0.002 0.002 0.002 0.002 0.002[0.3201] [0.3679] [0.3866] [0.4486] [0.4285] [0.4714]
Log public prison capacity 0.028 0.032 0.035 0.040 0.022 -0.142[0.5426] [0.4860] [0.5000] [0.5027] [0.6802] [0.6955]
R-squared 0.258 0.263 0.293 0.309 0.309 0.313Observations 765,338 765,338 765,338 765,338 765,338 765,338
Panel D: full sample
Log private prison capacity 0.002 0.002 0.000 0.002 0.002 0.003[0.7237] [0.6456] [0.9275] [0.7146] [0.7105] [0.6044]
R-squared 0.368 0.382 0.437 0.448 0.448 0.452Observations 3,544,144 3,544,144 3,544,144 3,544,144 3,544,144 3,544,144
Panel E: full sample, exclude probation
Log private prison capacity 0.003** 0.003** 0.000 0.001 0.001 0.002[0.0182] [0.0297] [0.9008] [0.6325] [0.6220] [0.1631]
R-squared 0.382 0.389 0.501 0.514 0.514 0.521Observations 2,699,237 2,699,237 2,688,027 2,688,033 2,687,664 2,684,438Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: court FEs: court-borderpair x year (Panel A-C) FEs: court x year (Panel D-E)
Linear trend: state x calendar-month FEs: judge
Notes: (a) The fixed effects taxonomy pertains to the CBCP sample in panels A–C. In the full sample in panelsD–E, court-borderpair fixed effects are replaced with court (=county) fixed effects. (b) We report p-values in squarebrackets. In Panels A–C, standard errors are two-way clustered on state and border segment. In Panels D–E, standarderrors are two-way clustered on state and county level. *** p<0.01, ** p<0.05, * p<0.1
12
Figure 3: Robustness of the Results in Table 2
0 .01 .02 .03 .04 .05
AL ARGA KYMD MSNC NVOR TNTX VAWA
With Probations0 .005 .01 .015 .02 .025
AL ARGA KYMD MSNC NVOR TNTX VAWA
Coefficients for beds in private prisons
.005 .01 .015 .02
AL ARGA KYMD MSNC NVOR TNTX VAWA
No Probations
Notes: This figure reports on the point-estimate and 95th-percent confidence band that results when re-estimatingthe specification in Column VI of Table 2, dropping one state at a time. The (red) vertical line is the baseline pointestimate. The results are sorted top-to-bottom in alphabetical order, i.e., omit AL, then AR, then GA, etc.
across columns. In contrast, the point estimate on PublicCst is never close to conventional statistical
significance.
Panel A combines potential effects of private prisons at the intensive margin (longer sentences)
and at the extensive-margin (being sent to prison). In Panel B, we isolate the intensive margin
by dropping cases that received probation.17 As expected, the point estimate is smaller for only
the intensive margin, but it remains equally stable across columns and is even more precisely
estimated than in Panel A. On the intensive margin alone, a 0.42 percent increase in private prison
capacity increases sentence lengths by roughly 10 days (a 0.42 × 0.013 increase, multiplied by a
mean sentence length of 60 months). Panel C isolates the extensive margin. The point estimate
follows from the composition of the total effect (0.021) into its intensive- and extensive margins
(0.013 + 0.002 × log(60)). It is, however, very imprecisely estimated.
Figure 3 verifies that our results are not driven by just one state or a small set of states.
Dropping one state at a time, the estimated coefficient always stays close to the baseline estimate
and always remains statistically significant. Dropping either of Alabama or Tennessee cuts the
coefficient in half, but also increases its precision considerably.18 The reason for this is that the
border-segments of Alabama and Tennessee come closest to generating an extensive margin effect
17 Figure A3 displays the distribution of sentence lengths with and without probations.18 Dropping Alabama drops three border-segments from the analysis (with Mississippi, Georgia, and Tennessee).
Dropping Tennessee drops seven of the 17 border-segments in Table 1.
13
on the probability of going to prison, which is part of the total effect estimated in the data with
probations (see Figure A4). When we focus on the intensive margin only in the right panel, the
effect of dropping Alabama or Tennessee is much less pronounced.
Robustness and other checks: Tables A3–A8 in the appendix conduct additional robustness
checks: Table A3 re-estimates the core results using the National Correctional Reporting System
(NCRS) data, and finds similar effects. Table A4 reports on regressions where treatment is a
state’s distance-weighted sum of private prison capacities. These estimations are subject to serious
endogeneity concerns discussed in Section 2.3, and results fall in between CBCP and full sample in
magnitude and significance. Table A5 reports on results when cases are aggregated at the court-
month level. In Table A6 we omit the most severe cases and re-estimate the baseline specification.
The results are smaller in magnitude (consistent with dropping the most severe crimes), but they
get stronger in terms of statistical significance: We view this as an important check in relation to the
findings in Owens (2011) that judges presiding over violent offences do not lower their sentences
if they are given discretion over TIS-guidelines. One possible interpretation of this is that the
potential cost-savings motives that will emerge as the most likely mechanism in our paper may not
apply (or be salient) when it comes to severe crimes.19 Table A7 checks on specifications where
we use the ratio of private over public prison beds as a regressor. The results are sign-consistent
(positive) but not statistically significant. Finally, Table A8 verifies that neither case load nor case
characteristics change with changes in our regressor of interest. In short, there is no evidence that
case selection in the courts confounds our estimation.
Placebo checks: Table 3 reports on two more important validity checks. Panel A of Table 3
reports on a placebo test that ensures our results are not driven by confounding factors. We re-
estimate this baseline effect for female defendants because private prisons in our data are entirely
for male inmates. There is therefore no inmate-transfer between male and female private prisons,
and private prisons for male inmates should therefore not impact the sentencing decisions of female
defendants, whatever the mechanism is that links private prisons to sentencing. Indeed, we find no
effect of expanding male private prisons on female sentencing length. We show no effect on female
defendents (almost all private prisons in our data are for male prisoners only),
19 Private prisons are not high-security prisons, so it is also true that (perceived or real) cost-savings from privateprisons are less likely to apply to defendants in severe crimes.
14
Panel B shifts the time-period of the treatment. With state-year fixed effects µst included,
identification of our baseline estimates in Table 2 comes from within-state within-year variation.
To check that this variation truly estimates the effect of changes in PrivateCst, rather than within-
year trends, we counter-factually shift the time of all changes in private prison capacity to month
t+3, t+6, and t+9, and to month t−3, t−6, and t−9, always evaluated relative to a state-specific
year fixed effect.
Table 3: Placebo Specifications
I II III IV V VIPanel A: female defendants Dependent variable: Sentence (log months)Log private prison capacity 0.004 0.003 0.004 0.009 0.012 0.011
[0.7706] [0.8111] [0.7898] [0.4127] [0.1947] [0.1621]
Log public prison capacity 1.135 1.051 0.837 1.032 1.120 0.930[0.3023] [0.3330] [0.3095] [0.1824] [0.1815] [0.3463]
R-squared 0.496 0.507 0.534 0.566 0.566 0.574Observations 141,980 141,980 141,980 141,980 141,980 141,980Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: state x year FEs: court-borderpair FEs: court-borderpair x year
Linear trend: state x calend.-month FEs: judge
Lag, t+3 Lag, t+6 Lag, t+9 Lead, t+3 Lead, t+6 Lead, t+9
Panel B: lags & leads
Log private prison capacity 0.004 -0.008 0.003 0.005 -0.013 0.005 [t-specific] [0.5584] [0.2632] [0.7237] [0.1651] [0.3915] [0.5277]
Log public prison capacity 0.011 -0.070 -0.168 0.017 0.274 -0.051 [t-specific] [0.9308] [0.8257] [0.1599] [0.4003] [0.4630] [0.2308]
R-squared 0.476 0.476 0.476 0.476 0.476 0.476Observations 765,338 765,338 765,338 765,338 765,338 765,338
Notes: Panel A of this Table replicates Panel A of Table 2 but uses only the sample of female defendants. In Panel Ball columns, we take the most demanding specification from the baseline results, i.e., Column VI of Panel A in Table 2.In Columns I–III of Panel B, instead of private and public prison capacities at year-month t we use correspondingvariables at year-month t − 3, t − 6, and t − 9. In Columns IV–VI of Panel B, instead of private and public prisoncapacities at year-month t we use corresponding variables at year-month t + 3, t + 6, and t + 9. In square bracketswe report p-values for standard errors are clustered on state and border segment; *** p<0.01, ** p<0.05, * p<0.1
Remarkably, none of the estimates in Panel B of Table 3 is significant. This suggests the
adjustment in sentencing is quite rapid shortly after the the private prison capacity changes. The
15
abundance of different space-time-varying fixed effects in the core CBCP identification strategy
makes it difficult to get at the time-path of the adjustment with any statistical precision.20 In the
next section, we therefore investigate this question in an event study setup that focuses only sharp
changes in capacities inside a pooled sample of stacked event-windows.
3.2 Event Study Evidence
The results in Section 3.1 identify the smaller (and more frequent) capacity changes of existing
facilities in addition to the sharper capacity changes associated with the opening and closing of
prisons. In this section, we focus only on prison openings and closings because these are the largest
shocks to prison bed capacity (and should be the most salient to judges).21 Our data contain 40
private prison openings including three privatizations of public prisons, 13 private prison closings,
42 public prison openings, and 27 public prison closings (exclusive of the three privatizations). The
regression we run is
yi(ct)k =
−1∑l=l
γl · D(t− Eki = l)it︸ ︷︷ ︸pre-event period
+
l∑l=1
γl · D(t− Eki = l)it︸ ︷︷ ︸post-event period
+βX ·Xi + λk + λst + λc + εicts, (2)
where yi(ct)k is sentence-length of case i inside event window k, and λk is a fixed effect for event
k. We slice the sentencing data into 12-month observation-windows (6 months before and after
each event). All observation windows are then pooled. Because each observation-window receives
its own fixed effect λk the event month’s coefficient is dropped to absorb the event fixed effect (as
the omitted category). All coefficients γl are thus defined relative to the event month. Following
best practice, we bin the end-points using an effect window of 8 month, so that the fourth to sixth
months before and after events each share a coefficient (Borusyak and Jaravel, 2016; Schmidheiny
and Siegloch, 2019).22
Figure 4 in its top-panel reports histograms of the 40 private prison and 42 public prison
openings. Capacity changes associated with these two event-types are very similar in magnitude.
The means are respectively 1,150 and 1,200. Any differences in estimated effects on sentencing
20 We do get enough precision to test for an effect around capacity changes if we use the full data; see Table A9.21 The average change associated with prison openings or closings is 1,150 beds.22 An observation-window of 12 months and effect window of 8 months imply that {l, l} = {−4,+4}, and that γ−4
is identified using sentences in t = {−6,−5,−4}, and γ4 using sentences in t = {4, 5, 6}, away from event k’s date Eki .
16
Figure 4: Event Study Analysis
Panel A: Private Prison Openings (left) and Public Prison Openings (right)
02
46
8Fr
eque
ncy
0 500 1000 1500 2000 2500Changes in private prison capacities
02
46
8Fr
eque
ncy
500 1000 1500 2000 2500 3000Changes in public prison capacities
Panel B: Equation (2) for Private Prison Openings (left) and Public Prison Openings (right)
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Panel C: Equation (2) for Private Prison Closings (left) and Public Prison Closings (right)
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Notes: Panels B and C graph the results of estimating equation (2) for private and public prison openings and closings.Point estimates are reported in Table A10. Figure A6 and Table A11 show results when we exclude probations.
17
across the two event types is therefore not likely to be driven by the events’ magnitudes. The
medium-panel is the core-result, comparing the effect of private prison openings on the left and
public prison openings on the right. The first note-worthy feature is that neither type of opening
exhibits any pre-trends. This suggests the exact timing of the openings is not related to trends in
crime or in sentencing. It is also consistent with the fact that although a prison opening is known
long in advance, there is no reason for sentencing to respond before it actually does open. The
second noteworthy feature is that there no effect at all of public prison openings, but a notable
effect of private prison openings, and it is concentrated in the first two months after the opening.
Sentence lengths are increased by 3.7 months in the first months after an opening, and by 3 months
in the second month after an opening. These point estimates are much more pronounced than
the 14 day estimate implied in Panel A in Table 2. This is because the generalized difference-in-
difference specification (1) averages the effect over an openings’ full post-period and therefore does
not capture the time path of the effect.
The narrowly concentrated effect we find makes sense from the perspective of average event’s
magnitude: a back-of-the-envelope calculation shows that it would take two-and-a-half months
worth of convictions to fill the capacity of the average newly opened private prison if every convict
in a state was sent there after its opening. In short, private prisons appear to have an effect on
sentencing precisely as long as they have vacant capacity.
The bottom panel reports results from the same setup, but comparing the results of closings.
There is again neither a pre-trend or effect for public prisons. There is, however, a notable pre-
trend for private prisons. This is consistent with the fact that closings are anticipated. Unlike with
openings, which are of course also anticipated, sentencing may respond in anticipation specifically
to closings because new inmates are unlikely to be sent to prisons that are about to close.
3.3 Evidence on Mechanisms
One potential explanation for an effect of prison expansions on sentence lengths could be that judges
consider prison capacity per se. For example, Mueller-Smith and Schnepel (2019) argue that over-
crowding drives prosecutors and judges to “divert” people from criminal prosecution. However, a
capacity explanation for the effects we find is inconsistent with the effect being concentrated in
only private prisons because there are as many new public prison openings in our data as private
18
ones, and they are of similar magnitude.23
This leaves two primary explanations. One is the sort of ‘judicial capture’ suggested by the
“kids for cash” scandal, i.e., private prison companies may directly influence judges to levy longer
sentences. A second is that judges internalize the cost-savings associated with incarceration in
private prisons. To make progress on this question, we need direct measures for the two distinct
mechanisms. We can measure the cost of private relative to public prisons because in most states
these are written into the laws governing the contracting with private prisons.24 We define the (per
bed) savings rate from private prisons as
Savings = 1 − Cost in private prisonsCost in public prisons
. (3)
In the states that include judge identifiers we follow the electoral cycle literature (Huber and
Gordon, 2004; Berdejo and Yuchtman, 2013) in defining judge j’s election cycles as a linear running
variable ‘proximity to election’
PtEj(s)t = t/Ts, (4)
that starts at 0 on the day after a general election, is scaled from 0 to 1, and increases by 1/Ts
each day until it equals 1 on the day of the next general election.25 With these measure in hand,
we estimate the following extension of expression (1)
Sentencei(jct) = βT · PrivateCst + βCS · PrivateCst · Savings
+ βPtE · PtEjt + βDI · PtEjt · PrivateCst
+ βT” · PublicCst + βX ·Xi + µs + µp(c) + µst + µj + µp(c)t + εicts,
(5)
where βT and βT” are the same as before, βCS > 0 would be evidence for the cost-savings hypothesis,
βPtE > 0 indicates the presence of electoral sentencing cycles, and βDI > 0 would be evidence for
the direct-influence hypothesis.
Expression (5) nests specifications where we check the two mechanisms. In columns I–V of
23 Table A13 shows that our results are not driven by over-crowding.24 When they are not legislated, we take the measures from reported savings. We check the robustness of results
to capping reported savings at 20 percent. See Table A16.25 Ts is the length of state s’s electoral cycle, i.e., TWA = 4× 365 in Washington where elections are every 4 years,
and TNC = 8× 365 in North Carolina where elections are every 8 years.
19
Tab
le4:
Cos
tS
avin
gsM
otiv
esvs
Ju
dic
ial
Cap
ture
III
III
IVV
VI
VII
VII
IIX
X
Sam
ple:
CB
CP
Ful
lJu
dge-
Sam
ple:
AL
, GA
, NC
, TN
, WA
Log
pri
vate
pri
son
capa
city
0.65
9*0.
241
0.01
00.
206*
0.25
4**
0.34
3**
0.19
4[0
.060
8][0
.305
8][0
.920
8][0
.076
1][0
.013
4][0
.044
2][0
.425
1]
Log
pri
vate
pri
son
capa
city
3.90
1***
1.38
0**
1.07
6*x
shar
e sa
ved
[0.0
060]
[0.0
154]
[0.0
967]
Log
pri
vate
pri
son
capa
city
0.08
4-0
.003
0.19
5in
low
sav
ing
stat
es[0
.346
1][0
.977
4][0
.423
8]
Log
pri
vate
pri
son
capa
city
1.09
8***
0.27
0***
0.42
8**
in h
igh
savi
ng s
tate
s[0
.001
0][0
.000
0][0
.013
3]
Pro
xim
ity
to e
lect
ion
0.92
5***
1.86
21.
898
1.89
9[0
.005
5][0
.301
8][0
.365
1][0
.364
9]
Pro
xim
ity
to e
lect
ion
x-0
.115
-0.1
34-0
.134
Log
pri
vate
pri
son
capa
city
[0.5
667]
[0.5
713]
[0.5
713]
Δ H
igh
and
Low
sav
ings
, p-v
alue
[0.0
040]
***
[0.0
214]
**[0
.098
2]*
R-s
quar
ed0.
310
0.31
00.
310
0.34
10.
341
0.46
90.
469
0.46
90.
464
0.46
4O
bser
vati
ons
765,
338
765,
338
765,
338
3,54
4,14
43,
544,
144
804,
752
804,
752
804,
752
804,
752
804,
752
Log
pub
lic
pris
on c
apac
ity
FE
s: s
tate
x f
isca
l-ye
ar
FE
s: q
uart
er F
E
F
Es:
cou
rt-b
orde
rpai
r
F
Es:
sta
te x
yea
r
FE
s: c
ourt
-bor
derp
air
x ye
ar
D
emog
raph
ic c
ontr
ols
Cas
e co
ntro
ls
F
Es:
judg
e
Dep
ende
nt v
aria
ble:
Sen
tenc
e (m
onth
s)
No
tes:
Inco
lum
ns
IV-X
,th
eco
urt
-bord
er-p
air
fixed
effec
tsb
ecom
esi
mple
court
(=co
unty
)fixed
effec
ts.
Sim
ilarl
yb
ord
er-p
air
yea
rfixed
effec
tsb
ecom
eco
urt
yea
rfixed
effec
tsin
colu
mns
IV–V
III.
Insq
uare
bra
cket
sw
ere
port
p-v
alu
es.
Sta
ndard
erro
rsare
two-w
aycl
ust
ered
on
state
and
bord
erse
gm
ent
inco
lum
ns
I–II
I,tw
o-w
aycl
ust
ered
on
state
and
county
inco
lum
ns
IV–V
,and
two-w
aycl
ust
ered
on
on
cale
ndar-
yea
rand
quart
er-o
f-yea
rin
colu
mns
VI-
X.
***
p<
0.0
1,
**
p<
0.0
5,
*p<
0.1
20
Table 4 we test for the cost-savings mechanisms by omitting βPtE ·PtEjt + βDI ·PtEjt ·PrivateCst.
In columns I–III we use the CBCP sample. Column I is the same as column XI in Panel A of
Table 2, except the outcome is in levels rather than logs.26 Columns II interacts private prisons
with the continuous cost-savings measure in expression (3), Column III instead does a median split
on cost-savings to define ‘high-savings’ and ‘low-savings’ states, with Georgia the median at 9.8%
estimated savings. Both specifications suggest that the effect of private prison capacity changes is
most pronounced in states where the cost savings from private prisons are high. (We also confirm
this when we break the event-study analysis into high-savings and low-savings states in Figure A8.)
Columns IV–V re-estimate II–III for the full sample.
The second half of the table compares this to the evidence for judicial capture. Only the nine
states with judge identifiers in the data can be included. Further, only states where there is at
least some evidence for the electoral sentencing cycles can be included.27 This omits Colorado,
Kentucky, Minnesota, and Virginia. Column VI confirms our baseline effect in this new full sample
of five states. Column VII confirms the presence of electoral sentencing cycles, i.e., βPtE > 0, in
this sample. Column VIII tests for judicial capture: there is no evidence at all that sentencing
cycles are more pronounced in the presence of private prisons. In combination, the evidence in
columns II-III and VIII supports the cost savings story but not the judicial capture story. Because
these are estimated in different samples, we introduce cost savings into the electoral cycle sample
in columns IX–X. The cost-savings coefficients continue to show up significantly, while the judicial
capture coefficient continues not to.28 While this evidence on mechanisms is coarse, the observed
patterns are surprisingly robust in their support of the cost savings explanation for the effect of
private prisons on sentencing.
4 Conclusion
We study whether private prisons impact judges’ criminal sentencing decisions. We find that the
opening of a private prison has large effect on sentence lengths in the prison’s state, but only during
26 The outcomes are in levels here because the interactions that are the regressors of interest are in levels so thatthe objects of interest are not elasticities.
27 The presence of the electoral sentencing cycles varies considerably across states, see e.g. Dippel and Poyker(2019).
28 Table A14 shows that these insights are unchanged when we omit probations from the data. Table A15 showsadditional robustness checks to variations in the fixed effects reported at the bottom of the tables.
21
the first two months after opening. Public prison openings have no such effects. This suggests that
private prisons have short-run effects on the application of justice that public ones do not. This
finding has considerable implications for judicial equity: defendants who happen to stand trial
shortly after a private prison opens can expect to be sentenced to three additional months relative
to otherwise identical defendants who stand trial for the same crime a few weeks earlier or later.
The equity implications of this effect are further accentuated by other research showing that these
defendants may also serve a larger portion of their sentences, with lower-quality rehabilitative care.
The evidence on mechanisms is overall most consistent with the hypothesis that judges respond to
private prisons by levying longer sentences because they consider the lower per-day per-bed fiscal
cost of incarceration in their sentencing decision.
22
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Mueller-Smith, M. and K. T. Schnepel (2019). Diversion in the criminal justice system. Technicalreport, Working Paper.
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25
Appendix A Data Description
Appendix A.1 Prison Data
The prison-year panel dataset was constructed combining several sources. Here, we provide the
description of the process of its creation. The basis of our data construction is the ‘Census of State
and Federal Adult Correctional Facilities’ (CSFACF), which was reported in five-year waves from
1974–2005, and in 2012. We use the 1979, 1984, 1990, 1995, 2000, 2005, and 2012 waves.29 In each
year we see the year when each penitentiary is founded, and if the prison is publicly or privately
managed. We omit all federal prisons from the dataset because we study the state court and prison
system. Refer to the CSFACF waves as 1990 = t0, 1995 = t1, 2000 = t2, 2005 = t3, and call the
most recent date on a state’s sentencing data t4 if t4 > 2005. To construct a panel from these
cross-sections, we pursue the following procedure:
1) Create a list of public and private prisons: We use CSFACF to create the list of
prisons that existed at some point in time between 1980 and 2005. We searched each state’s
departments of corrections site for any prisons built after the last CSFACF wave. We then
verified all codings from CSFACF using the data on prisons available at ENIGMA30 and using
CSFACF’s 2012 census that became available on February 5th, 2020.
2) Coding dates of opening and closing: We know the year of opening of each prison from
the CSFACF. Because we need a monthly variation in prisons capacities we searched each
state’s departments of corrections site and sites of private prison companies for the exact
month of opening/closure.
3) Capacity Changes:
– From the department’s correction sites and CSFACF data we see the exact capacities of
all public and private prisons during opening and closure from 1980 to 2005. We see all
post-2012 capacities of all public and private prisons during opening and closure only
from the department’s correction sites. We are also able to verify our data for 2006–2012
using 2012 census of CSFACF.
29 These data are publicly available under ICPSR code 24642.30 https://app.enigma.io/table/enigma.prisons.all-facilities?row=0&col=0&page=1
26
– In particular, we studied sites of all the private prison companies and collected monthly
prison capacity data for 1980–2017. The data contains even the slightest changes (i.e.,
small expansions) in prison capacities.
– If we see a capacity change from wave to wave in CSFACF dataset that is not opening
and closure we checked department’s correction sites and local media whether there was
a small expansion and at what year-month.
∗ For private prisons we checked all such incidents.
∗ For public prisons, we coded all such changes where the difference between the
number of beds in the waves was above 100 beds. This leaves the possibility of less
measurement error in the private than in public prisons capacity changes. However,
any difference would be very marginal given the discussion above. To address this
concern, we perform one check where we round the capacity of private prisons to the
nearest 100, which rounds away small capacity changes. In other words, we introduce
measurement error into private prison capacity changes that matches roughly the
potential measurement error in public prison capacity changes. Table A17 reports
the results, which are basically unchanged to the core results.
∗ In the event study focused on openings and closings, there will be no difference in
measurement error between private and public prisons.
4) Privatizations: If a prison appears as private in CSFACF wave tτ and public in the tτ−1,
we look up the exact date on the web-sites of the of the private prison companies
5) Out-sourcing of prison capacities to other states: We also checked whether any state
rent-in prison capacities in other states and whether any prison were accepting prisoners from
outside of their home state.
Finally, we geo-locate latitude and longitude data of each prison location using the Google Maps
API.
27
Appendix A.2 Sentencing Data
Sentencing data was collected separately from each state. 15 states were willing to share their
data with us for free or at reasonable cost: Alabama, Arkansas, Colorado, Georgia, Kentucky,
Maryland, Minnesota, Mississippi, Nevada, North Carolina, Oregon, Tennessee, Texas, Virginia,
and Washington. Obtaining these data from each state separately took several years and the process
was quite idiosyncratic.31 We contacted each state with the following initial data request:
The data we are looking for has a court case (or ’sentencing event’) as the unit of observation. In
some states the data is organized by charge (with several charges making up the case or sentencing
event) and that is equally fine. The key data that we need are:
1. date, month and year of sentencing for
2. type of crime,
3. length of sentencing,
4. type of sentencing (low-security, high security, etc),
5. defendant’s sex,
6. defendant’s race,
7. court identifier
8. name of judge or judge identifier number,
9. type of court that convicted (trial, appeal, etc),
10. in what prison the person was sent
We do not seek any information that identifies defendants.
Sincerely, XXX
The following reports for each state the office responsible for storing the data, as well as relevant
contact emails and numbers at the time we requested the data between late 2016 and mid 2018.
Longer processing times were typically do either to backlogs of data-technicians or to having to go
get our request vetted and signed off on in the institutions that manage the data.
1. Alabama
• Initial contact with the Sentencing Commission at http://sentencingcommission.
31 The only state with digitized sentencing data not included in our analysis is Kansas, which charged five timesmore than other states for our data processing request leading us to echo Frank’s 2007 question.
28
alacourt.gov/
• After emailing [email protected], Bennet Wright processed our
request.
• Time between data application and delivery: 16 months.
2. Arkansas
• Initial contact with the Sentencing Commission at https://www.arsentencing.com/
• Were referred the Administrative Offices of the Courts. Their email was ORJShelp@
arcourts.gov and Joe Beard processed our data request.
• Time between data application and delivery: 4 months.
3. Georgia
• Initial contact with Department of Corrections at http://www.dcor.state.ga.us/
Divisions/ExecutiveOperations/OPS/OpenRecords.
• After emailing [email protected] it was recommended we go through their
‘Media Inquiries’ under +1-478-992-5247, where Jamila Coleman coordinated our request
with their data technicians.
• Time between data application and delivery: 3 months.
4. Kentucky
• We spoke on the phone to Cathy Schiflett at the Kentucky Courts Research and Statistics
Department.
• She guided us to https://courts.ky.gov/Pages/default.aspx, where we had to select
‘Statistical Reports’ and then submit our data request.
• Daniel Sturtevant handled our request.
• Time between data application and delivery: 9 months.
5. Maryland
29
• After initial contact though http://www.courts.state.md.us/reference/piarequests.
html, we submitted our request to the Maryland State Commission on Criminal Sen-
tencing Policy, at http://www.msccsp.org/Default.aspx
• Our request was processed by Lou Gieszl, Assistant Administrator for Programs at the
Administrative Office of the Courts
• Time between data application and delivery: 1 month Unlike most states, Maryland’s
data was ‘off-the-shelf’ available as the MSCCSP (Maryland State Commission on Crim-
inal Sentencing Policy) dataset
6. Minnesota
• Initial contact with the Minnesota Sentencing Guidelines Commission at http://mn.
gov/sentencing-guidelines/contact/contact-us.jsp
Email address: [email protected]
• Kathleen Madland was the Research Analyst who processed our request
• Time between data application and delivery: 2 months
7. Mississippi
• Initial contact with the Mississippi Department of Corrections at https://www.ms.gov/
mdoc/inmate
• Audrey MacAfee and Lynn Mullen processed our request
• Time between data application and delivery: 2 months We use essentially the same data
as Mukherjee (2019)
8. Nevada
• After initial contact with the Nevada Department of Corrections at http://doc.nv.
gov/Inmates/Records_and_Information/Public_Record_Fees/, with email pio@doc.
nv.gov, our request was handled by Brooke Keast, Public Information Officer
• We were provided with the codebook and scraped the raw data from the Nevada’s DOC
site on 7th of July 2016: http://167.154.2.76/inmatesearch/form.php
30
9. North Carolina
• Initial contact though http://www.ncdoj.gov/Top-Issues/Public-Integrity/Open-
Government/Understanding-Public-Records.aspx
• Then we were put in touch with the North Carolina Administrative Office of the Courts,
where our data request was processed by the ‘Remote Public Access’ data technicians
• Time between data application and delivery: 3 months
10. Oregon
• In Oregon, sentencing data is handled by the Criminal Justice Commission’s Statistical
Analysis Center at https://www.oregon.gov/cjc/SAC/Pages/CurrentProjects.aspx
• Kelly Officer processed our request
• Time between data application and delivery: 1 month
11. Tennessee
• Initial contact with Tennessee’s Department of Corrections at https://www.tn.gov/
correction/article/tdoc-prison-directory
• Tanya Washington, the DOC’s Director of Decision Support: Research & Planning,
processed our request
• Time between data application and delivery: 6 months
12. Texas
• Downloaded data online on 4th of November 2016 : https://www.tdcj.state.tx.us/
kss_inside.html
13. Virginia
• Initial contact was through a web-form of the Virginia Criminal Sentencing Commission
at http://www.vcsc.virginia.gov/
• After being initially denied on the grounds that FOIA requests could only be processed
for Virginia residents, we called +1-804-225-4398, and were eventually approved after
speaking to the director Meredith Farrar-Owens.
31
• Time between data application and delivery: 3 months
14. Washington
• Initial contact with the Department of Corrections at http://www.doc.wa.gov/aboutdoc/
publicdisclosure.asp, where Duc Luu processed our request
• Time between data application and delivery: 2 weeks
We observe sentences that are placed on probation in every single state in our data. Texas is
the only state where the data we obtained only contains convictions so that we miss defendents
who were judged to have been innocent altogether. Because probations are always more than 95%
of zero-sentences in the data (i.e. non-convictions are less than five percent), we should not miss
much by this omission in Texas. Texas is also the only state where the data consists of appended
annual snapshots of the correctional populations, as opposed to a single unified dataset with the
case as the unit of observation. Fortunately, the data is complete and there are no gaps in coverage.
In short, the concerns above all pertain to Texas only. Importantly, our leave-one-state-out
robustness checks show that Texas is never important for our core results. This is also unsurprising
because Figure 2 shows that Texas only has 2 counties (on the border with Arkansas) in the CBCP
data to begin with. Table A1 shows the full caseload we observe over time in each state.
32
Tab
leA
1:C
ases
by
Sta
teov
erT
ime
Ala
bam
aA
rkan
sas
Geo
rgia
Ken
tuck
eyM
aryl
and
Min
nes.
Mis
siss
.N
orth
Car
olin
aN
evad
aO
rego
nT
enne
ssee
Tex
asV
irgi
nia
Was
hing
t.
Yea
rsA
LA
RG
AK
YM
DM
NM
SN
CN
VO
RT
NT
XV
AW
A
1986
1,70
42,
960
1987
9,02
13,
547
1988
8,74
24,
739
1989
9,35
46,
951
1990
8,82
33,
554
8,91
919
9111
,348
9,16
13,
822
12,8
2419
9212
,021
9,32
54,
587
15,2
9119
9312
,074
9,63
75,
093
14,0
6719
9412
,903
9,78
64,
835
13,9
0219
9515
,598
9,42
15,
281
16,1
8419
9615
,390
9,48
05,
080
15,9
2919
9716
,473
9,84
75,
679
16,5
0019
9819
,803
10,8
875,
963
16,8
1119
9919
,128
10,6
345,
818
17,9
7620
0020
,016
10,3
956,
255
18,4
0220
0121
,955
10,7
966,
613
18,6
4420
023,
970
22,2
7914
,805
12,9
776,
837
18,7
1320
0316
,760
22,8
9217
,213
14,4
926,
951
18,7
8120
0416
,126
24,8
9318
,970
14,7
517,
296
5,70
337
,793
20,0
4913
,703
2005
17,8
7625
,330
20,2
7715
,460
7,10
98,
351
40,0
5320
,670
29,4
7120
0618
,022
26,0
8119
,924
16,4
437,
619
3462
78,
764
40,9
3820
,556
13,1
1029
,253
2007
18,1
3125
,745
20,2
3012
,192
16,1
677,
538
3625
28,
243
37,2
9422
,933
27,3
8929
,022
2008
18,7
1725
,575
20,5
7111
,203
15,3
948,
162
3801
97,
619
34,5
2921
,736
26,7
9227
,200
2009
20,5
5526
,800
19,8
1710
,962
14,8
408,
084
3823
47,
864
32,9
8721
,938
25,7
1524
,051
2010
19,9
6226
,328
58,4
6220
,039
10,5
8614
,311
7,81
640
475
7,78
233
,864
23,3
157,
461
24,8
5422
,699
2011
19,0
1724
,988
58,0
6020
,513
10,7
8814
,571
8,07
721
195
7,14
133
,208
23,7
349,
732
24,8
0323
,115
2012
18,3
1524
,703
56,2
5520
,393
10,1
6615
,207
7,98
214
675
7,07
334
,728
23,5
4412
,859
24,7
0923
,320
2013
17,5
9025
,566
52,3
4220
,989
10,4
2115
,318
7,65
714
187
7,03
235
,279
21,9
1317
,896
25,4
8524
,805
2014
17,6
1225
,996
52,9
2221
,272
10,5
0016
,145
6,39
615
252
7,13
435
,749
20,0
6425
,311
25,3
2424
,476
2015
17,3
8225
,476
52,0
1821
,542
10,1
336,
030
1605
96,
432
34,6
3918
,600
23,1
5524
,315
12,1
8020
1612
,706
2814
850
,280
21,7
295,
237
3,20
910
544
1873
412
,276
2017
15,9
3250
,718
24,4
552,
250
No
tes:
This
table
show
sth
efu
llca
selo
ad
we
obse
rve
over
tim
ein
each
state
33
Appendix A.3 Prison Costs Data
We collect information on savings from using convict labor from the multiple sources.
• The costs of state public prisons we use data from Vera Institute for Justice (2015).
• In Alabama, the DOC’s annual report reports savings of 22%32
• In Arkansas, the Arkansas Times reports a state contracts pay 30$ per-inmate-per-day to
private prisons,33 while Vera Institute for Justice (2015) reports a 57$ cost per-inmate-per-day
in the public system, which suggests a cost-savings of 48%.
• In Georgia, Vera Institute for Justice (2015) reports a per-inmate-per-day cost of 54.73$ in
public prisons. Consistent with this the Department of Corrections reports the same number
(20,000$ per year) for public prisons in 2014, and a per-inmate-per-day cost of 49.3$ in private
prisons.34
• In Kentucky, state legislation mandates private prisons savings (per bed) to be 10%35
• In Mississippi, state legislation mandates private prisons savings (per bed) to be 10%36
• Maryland has no private prisons, and thus no legislated cost savings.
• Nevada had two private prisons during our sample period, which goes to 2015 (see Table 1).
Vera Institute for Justice (2015) reports a per-inmate-per-day cost of 49$ in public prisons.
The state’s 2008 Environmental Impact Statement reports 47.79$.37
• North Carolina has essentially 0% cost-saving. “North Carolina ended its use of private pris-
ons [] after little cost-savings,” said Daniel Bowes, an attorney at the Second Chance Initiative
at the N.C. Justice Center. Gotsch and Basti (2018) writes that “by 2000, the corrections
32 http://www.doc.state.al.us/docs/AnnualRpts/2016AnnualReport.pdf33 www.arktimes.com/arkansas/the-private-prison-swamp/Content?oid=2389039834 http://www.dcor.state.ga.us/sites/all/files/pdf/CorrectionsCosts.pdf35 See KY. REV. STAT. ANN. 197.510(13), reported in Hakim and Blackstone (2013).36 MISS. CODE ANN. 47-5-1211(3)(a), reported in Hakim and Blackstone (2013).37 See Document 36, Page 9 of 10 in https://books.google.com/books?id=leI0AQAAMAAJ&pg=PA215-IA20&lpg=
PA215-IA20&dq=Southern+Nevada+Women Nevada’s cost estimate comes from a female prison. We use this as thebest available estimate of the private prison cost, although we do not consider female private prisons in our exercisebecause there is no inmate-transfer between male and female private prisons. (See the placebo exercise in Table 3.Nevada’s is the only female private prison in the states we have data on and it plays no role in our empirics.)
34
department found that Core Civics facilities had produced little cost-savings compared to
state-run facilities.”38 Thus we set savings at 0.
• Oregon has no private prisons, and thus no legislated cost savings.
• In Tennessee, state legislation mandates private prisons savings (per bed) to be 5%39
• In Texas, state legislation mandates private prisons savings (per bed) to be 10%40
• In Virginia, the Department of Justice reports the cost savings are 1%41
• Washington has one private prison in our data, run by Correctional Services Corp (CNC) the
Vera Institute for Justice (2015) reports a per-inmate-per-day cost of 105$ in public prisons,
while the Tribune reports negative savings in the Washington’s INS’ contract with CNC.42
We censor these negative savings at 0.
We compute Savings = 1− Cost in private prisonsCost in public prisons
. If private prison costs are the same as public prison
costs, then Savings = 0. We assign the value of zero for the states where there is no private prisons.
Figure A1 shows the data.
38 https://grassrootsleadership.org/in-the-news/2016/nc-private-prison-among-14-impacted-
department-justice-announcement39 TENN. CODE ANN. 41-24-104(c)(2)(B), 41-24-105(c), reported in Hakim and Blackstone (2013)40 TEX. GOVT CODE 495.003(c)(4), reported in Hakim and Blackstone (2013)41 www.tkevinwilsonlawyer.com/library/virginia-private-prisons.cfm42 www.thenewstribune.com/news/special-reports/article25860412.html
35
Figure A1: A histogram of Savings
0
0.1
0.2
0.3
0.4
0.5
0.6
AL AR GA KY MD MS NC NV OR TN TX VA WANotes: This figure displays a histogram of Savings.
36
Appendix B Additional Results
Table A2 shows that the socio-economic characteristics of border-court counties are not statistically
different from all other counties in the same states. Column-set I reports on border-court counties
Column-set II reports the same for all other counties in the 13 states. Reassuringly, column-set
III confirms that border counties are representative of counties in their states more broadly, the
difference between the two samples is never near conventional significant levels. In the bottom panel,
we verify the same holds true for sentencing and defendant characteristics, including defendants’
race and our main dependent variable, the length of a sentence.43
One may be surprised by the balance in county characteristics if one had for example assumed
border-counties were smaller than ‘interior counties.’ However, it turns out that a pretty even split
of the most populous counties in each state are on state borders. For example,
• In Tennessee, the 1st, 4th, 7th, 8th, and 9th most populous counties (Shelby, Hamilton,
Montgomery, Sumner, and Sullivan) all sit on border segments with Arkansas and Mississippi,
Georgia, Kentucky, Kentucky, and Virginia, respectively.44
• In Oregon, the 1st and 2nd most populous counties (Multnomah and Washington) sit on
border segments with Washington.45
• In Mississippi, the 3rd, 5th, and 8th most populous counties (DeSoto, Jackson, and Laud-
erdale) all sit on border segments with Arkansas and Tennessee, Alabama, and Alabama,
respectively.46
• In Kentucky, the 3rd, 5th, and 7th most populous counties (Hickman, Fulton, Cumberland)
all sit on border segments with Tennessee.47
• In Virginia, the 1st, 2nd, 3rd, and 7th most populous counties (Fairfax, Prince William,
43 Sentences of length zero represent cases that the defendant was found not guilty, or sentenced to non-prisonconditions (e.g., fines, probation, or community services). In the case of consecutive sentences, we summed allsentencing within each case. In the case of concurrent sentencing, we took the maximum. The two most importantcharacteristics of a court case are the crime’ severity and the defendant’s recidivism. Because each state classifiesthese two variables into unique discrete scales, we cannot report descriptive statistics on these.
44 https://en.wikipedia.org/wiki/List_of_counties_in_Tennessee45 https://en.wikipedia.org/wiki/List_of_counties_in_Oregon46 https://en.wikipedia.org/wiki/List_of_counties_in_Mississippi47 https://en.wikipedia.org/wiki/List_of_counties_in_Kentucky
37
Loudoun, and Stafford) all sit on border segments with Maryland.48
• In Alabama, the 2rd, 3rd, and 8th most populous counties (Mobile, Madison, and Lee) all sit
on border segments with Mississippi, Tennessee, and Georgia, respectively.49
48 https://en.wikipedia.org/wiki/List_of_cities_and_counties_in_Virginia49 https://en.wikipedia.org/wiki/List_of_counties_in_Alabama
38
Tab
leA
2:B
ord
er-C
ounty
Bal
ance
Tab
le
Mea
ns.d
.M
ean
s.d.
Mea
nP-
valu
eM
ean
P-va
lue
Cou
nty
Con
trols
:Po
pula
tion,
200
067
,056
.2(1
7854
9)65
,218
.3(1
3198
7)-1
,837
.9[0
.870
]-2
6,32
2.1
[0.3
15]
Popu
latio
n de
nsity
, 200
019
8.91
(604
)20
8.62
(756
)9.
71[0
.792
]-4
2.86
[0.3
35]
Land
are
a (s
quar
e m
iles)
774.
83(1
,186
)74
9.68
(1,2
92)
-25.
156
[0.8
32]
192.
246
[0.3
74]
Man
ufac
turin
g em
ploy
men
t4,
968.
6(1
1,85
2)4,
327.
3(6
,354
)-6
41.2
[0.3
62]
-629
.2[0
.628
]M
aufa
ctur
ing
aver
age
wee
kly
earn
ings
($)
592.
04(2
35)
577.
13(1
66)
-14.
91[0
.410
]-1
7.74
[0.5
08]
Res
taur
ant e
mpl
oym
ent
3,36
3.3
(7,9
63)
2,79
5.6
(5,0
05)
-567
.7[0
.347
]-1
,636
.7[0
.247
]R
esta
uran
t ave
rage
wee
kly
earn
ings
($)
187.
56(3
3)18
6.94
(40)
-0.6
24[0
.874
]-8
.59
[0.3
58]
Urb
an (d
umm
y)0.
463
(0.4
99)
0.43
9(0
.497
)-0
.024
[0.5
89]
-0.0
80[0
.279
]U
rban
-rur
al c
ontin
uum
(1-8
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39
Figure A2: Illustrating the Border-Sample Identifying Variation
4950
050
000
5050
051
000
# Be
ds (p
ublic
pris
ons)
(Das
hed
Line
)
6000
7000
8000
90001
00001
1000
# Be
ds (p
rivat
e pr
ison
s)
01jan2010 01jan2012 01jan2014 01jan2016Year
GA
1400
014
500
1500
015
500
1600
0#
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(pub
lic p
rison
s) (D
ashe
d Li
ne)
5000
6000
7000
8000
# Be
ds (p
rivat
e pr
ison
s)
01jan2010 01jan2012 01jan2014 01jan2016Year
TN
Notes: This figure shows the time variation in PrivateCct and PublicCct for two neighboring states (Georgia andTennessee, which together form segment #7 in Table A2) over the same time horizon. The dashed (red) line isthe state-specific time-series of public prison capacity (number of beds). The solid (blue) line is the state-specifictime-series of private prison capacity (number of beds).
Figure A2 illustrates the identifying variation across the border-segment that connects Georgia to
Tennessee. This is segment #7 in 1. Tennessee has considerable variation in PrivateCct, as can be
seen in Figure 1. However, sentencing data from Georgia only goes back to 2010, and within the
2010 to 2016 time frame, Tennessee displays no variation in PrivateCct. The effect of PrivateCct
on courts/counties along border segment #7 is therefore estimated by comparing the expansion
in Georgia’s private prison capacity in 2011 and again in 2012 relative to a constant capacity in
Tennessee.
40
Figure A3: Distribution of Sentences, with and without Probation)
0.0
1.0
2.0
3.0
4D
ensi
ty
0 720Sentence lenght in months
0.0
05.0
1.0
15.0
2.0
25D
ensi
ty
0 720Sentence lenght in months
Notes: The left panel shows the distribution of sentence length with probation, the right panel without. We truncatethe sentence length at 720 months.
41
Figure A4: Robustness of the Results in Panel C of Table 2
-.005 0 .005 .01
AL_D AR_DGA_D KY_DMD_D MS_DNC_D NV_DOR_D TN_DTX_D VA_DWA_D
D(Incarceration / No Probation)
0 .005 .01 .015 .02 .025
AL ARGA KYMD MSNC NVOR TNTX VAWA
Coefficients for beds in private prisons
Notes: This figure reports on the point-estimate and 90th-percent confidence band that results when re-estimatingthe specification in Column VI of Table 2, dropping one state at a time. The (red) vertical line is the baseline pointestimate. The results are sorted top-to-bottom in alphabetical order, i.e., omit AL, then AR, then GA, etc.
Figure A4 is the equivalent of Figure 3. but for only the extensive margin effect on the probability
of going to prison. Figure A4 explains the pattern observed in the left panel of Figure 3.
42
Figure A5: Robustness of the Results in Table 2: Coefficient on ‘Public Prisons’
-1.5 -1 -.5 0 .5
AL ARGA KYMD MSNC NVOR TNTX VAWA
Coefficients for beds in public prisons
0 .005 .01 .015 .02 .025
AL ARGA KYMD MSNC NVOR TNTX VAWA
Coefficients for beds in private prisons
Notes: This figure reports on the point-estimate for public prison capacities and 95th-percent confidence band thatresults when re-estimating the specification in Column VI of Table 2, dropping one state at a time. The (red) verticalline is the baseline point estimate. The results are sorted top-to-bottom in alphabetical order, i.e., omit AL, thenAR, then GA, etc.
Figure A5 is the equivalent of Figure 3 for public prisons Note that even when dropping Mississippi,
the estimate includes 0 at the 90th percentile confidence band.
43
Table A3: The Effect of Private Prisons on Sentence Length
I II III IV V VI
NCRS data for border-sample ~ Table 1 Panel B (because no probation in NCRS data)
Log private prison capacity 0.030** 0.030** 0.025* 0.021* 0.025** -[0.0288] [0.0268] [0.0619] [0.0977] [0.0424] -
Log public prison capacity -0.510 -0.516 -0.456 -0.383 -0.151 -[0.3119] [0.3127] [0.2739] [0.2566] [0.6361] -
R-squared 0.368 0.372 0.502 0.503 0.521Observations 224,318 224,318 224,318 224,318 224,318Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: state x year FEs: court-borderpair FEs: court-borderpair x year
Linear trend: state x calendar-month FEs: judge
Notes: Table ?? reports on the same specifications as Table 2 but using the NCRS data, which includes no probationand no judge information. *** p<0.01, ** p<0.05, * p<0.1
The National Correctional Reporting System (NCRS) data come from the National Corrections
Reporting Program (ICPSR 36373). This is a standard dataset for the literature and it contains
data for all prison admissions in the United States from 1980 to 2014.
This dataset has several drawbacks. The main downside of these data in our view is that (i)
they do not include probation, people who got only fines or community service, or those found not
guilty, (i) the selection-process of which cases are reported in the NCR program is quite unclear to
us (e.g., Arkansas reported a grand total of 28 cases from 19802014), and (c) they have no judge
information.
Our main outcome variable here is the same as in the baseline regression — log of the length
of sentence imposed. We also use the same defendant and case characteristics. The only difference
with our baseline dataset is that here, the classification of offenses is standardized. Therefore,
instead of using state-specific case-severity identifiers we include in our regressions a matrix of 180
standardized fixed effects.
44
Table A4: Prison Capacities Weighted by distance to Private Prison
I II III IV V VIPanel A: baseline Dependent variable: Sentence (log months)Log Σp(private prison capacityp / distancecp) 0.008 0.009* 0.010** 0.006* 0.006* 0.005
[0.1295] [0.0827] [0.0453] [0.0857] [0.0887] [0.1355]
R-squared 0.366 0.380 0.435 0.446 0.446 0.450Observations 3,544,144 3,544,144 3,544,144 3,544,144 3,544,144 3,544,144
Panel B: exclude probation
Log Σp(private prison capacityp / distancecp) 0.002 0.002 0.003** 0.002* 0.002* 0.002[0.4499] [0.3917] [0.0261] [0.0855] [0.0768] [0.1347]
R-squared 0.382 0.389 0.502 0.515 0.515 0.522Observations 2,699,237 2,699,237 2,688,027 2,688,033 2,687,664 2,684,438Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: state x year FEs: court-borderpair FEs: court-borderpair x year
Linear trend: state x calendar-month FEs: judge
Notes: This table replicates Panels D and E of Table 2, but uses prison capacities weighted by the distance from adefendant’s court to each prison. In square brackets we report p-values for standard errors are clustered on state andcounty level.*** p<0.01, ** p<0.05, * p<0.1
In Section 2.3 we argue that the location of prisons is clearly endogenous to local factors that could
also impact local crime and therefore sentencing. This implies that using a court’s distance to a
private prison as a source of variation is endogenous, despite the intuitive appeal of this margin of
variation. For completeness, Table A4 reports on regressions using this endogenous distance-based
measure. Endogeneity concerns aside, conversations with officials in several states revealed that
proximity seems to be anyway largely irrelevant in determining which prison a defendant is sent to.
Prisons are different from jails in this respect: jails are run by the county, and defendants awaiting
trial do so in the jail of the trial court’s county.
45
Table A5: Aggregating Data by County-Month
I II III IV V VI
Dependent variable: Sentence (log months)
Panel A: baseline aggregated to county-month
Log private prison capacity 0.016*** 0.014** - 0.014** 0.014** -[0.0062] [0.0141] - [0.0265] [0.0265] -
Log public prison capacity -0.141 -0.162 - -0.392 -0.392 -[0.6656] [0.6073] - [0.2974] [0.2974] -
R-squared 0.797 0.802 0.839 0.839Observations 72,691 72,691 72,691 72,691
Panel B: baseline w caseload-weights
Log private prison capacity 0.016*** 0.014** - 0.015*** 0.014** -[0.0062] [0.0141] - [0.0050] [0.0265] -
Log public prison capacity -0.141 -0.162 - -0.291 -0.392 -[0.6656] [0.6073] - [0.4283] [0.2974] -
R-squared 0.797 0.802 0.839 0.839Observations 72,691 72,691 72,691 72,691
Panel C: baseline w population weights
Log private prison capacity 0.016*** 0.014** - 0.015*** 0.014** -[0.0062] [0.0110] - [0.0048] [0.0186] -
Log public prison capacity -0.141 -0.168 - -0.284 -0.378 -[0.6656] [0.5888] - [0.4445] [0.3173] -
R-squared 0.797 0.802 0.839 0.839Observations 72,691 72,691 72,691 72,691FEs: state x fiscal-year Demographic controls Case controls FEs: court FEs: court-borderpair x year (Panel A-C) FEs: court x year (Panel D-E)
Linear trend: state x calendar-month FEs: judge
Notes: This table replicates Panel A of Table 2, but uses data aggregated at the county-month level instead ofcase-level (individual) data. Panels B and C use caseload and population weights. *** p<0.01, ** p<0.05, * p<0.1
In Panel A of Table A5 we aggregate our case-level data on county-month level. I.e., our
dependent variable is now log of the average sentence length in county-pair p(c) in month-year
t. Our main explanatory variables (log of private and public prison capacities) do not change
here, because it was already at the state-month level. However, our defendants’ controls become
aggregated; because our individual case controls are state-specific matrices of dummies we can’t
aggregate them, thus we omit Column III in Table A5. Similarly, we can’t aggregate judge fixed
46
effects, and Column VI also remains empty. All results are significant and consistent with our
baseline results. Panels B and C aggregate the data using caseload-weights and county population
weights. All panels reassuringly report significant and consistent results.
47
Table A6: Omitting the Most Severe Cases
I II III IV V VI
Truncated, without severe crimes
Log private prison capacity 0.011*** 0.010** 0.012*** 0.011** 0.014** 0.015**[0.0049] [0.0141] [0.0085] [0.0185] [0.0286] [0.0436]
Log public prison capacity -0.085 -0.071 -0.040 -0.021 -0.091 -0.057[0.7758] [0.7847] [0.8787] [0.9449] [0.7714] [0.8661]
R-squared 0.361 0.370 0.426 0.440 0.440 0.444Observations 706,835 706,835 706,835 706,835 706,835 706,835Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: state x year FEs: court-borderpair FEs: court-borderpair x year
Linear trend: state x calendar-month FEs: judge
Notes: This table replicates Panel A of Table 2, but here we omit most severe cases with sentence length above 10years. *** p<0.01, ** p<0.05, * p<0.1
In Table A6 we omit most severe cases and re-estimate the baseline specification. The results are
smaller in magnitude (consistent with dropping the most severe crimes), but they get stronger in
terms of statistical significance: this is in line with the fact that private prisons are not high security
prisons. We view this as an important check in relation to the findings in Owens (2011) that judges
do not to alter their sentences in responses to discretion over TIS-guidelines, when they consider
violent offences.
48
Table A7: Using Shares of Beds in Private Prisons as the Explanatory Variable
I II III IV V VI
Baseline with share of private prison capacities
Share of private prison capacities 0.647 0.573 0.493 0.509 0.641 0.623[0.2524] [0.2683] [0.3900] [0.3169] [0.2974] [0.3243]
Log public prison capacity -0.126 -0.097 -0.063 -0.083 -0.119 -0.104[0.6773] [0.7201] [0.8290] [0.8075] [0.7170] [0.7661]
R-squared 0.379 0.390 0.455 0.468 0.468 0.472Observations 765,338 765,338 765,338 765,338 765,338 765,338Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: state x year FEs: court-borderpair FEs: court-borderpair x year
Linear trend: state x calendar-month FEs: judge
Notes: This table replicates Panel A of Table 2, but uses share of male private prison capacities (out of total malecapacities) as the explanatory variable. *** p<0.01, ** p<0.05, * p<0.1
In Table A7 we re-estimate baseline results using share of private prison capacities (male) as the
main explanatory variable. While the estimand is positive throughout all columns, it is insignificant.
We hypothesize that this measure is less precise that the actual private prison capacities as it
changes not only because of the changes in private prison capacities but also due to changes in
denominator.
49
Table A8: Checking if Case Load and Case Characteristics Change with Private Prisons
I II III IV V VI
Panel A: Dependent variable: Log (# of cases)
Log private prison capacity 0.006 0.006 - 0.008 0.008 -[0.3895] [0.3895] - [0.3492] [0.3492] -
R-squared 0.287 0.287 0.360 0.360Observations 72,691 72,691 72,691 72,691
Panel B: Dependent variable: Predicted Sentence (log months)
Log private prison capacity 0.002 0.002 - 0.002 0.002 0.002[0.2180] [0.2405] - [0.3245] [0.2471] [0.3238]
Log public prison capacity 0.056 0.054 - 0.064 -0.022 -0.016[0.4957] [0.5176] - [0.3986] [0.7700] [0.8283]
R-squared 0.830 0.831 0.831 0.834 0.836Observations 767,410 767,410 767,410 767,410 767,410Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: court FEs: court-borderpair x year (Panel A-C) FEs: court x year (Panel D-E)
Linear trend: state x calendar-month FEs: judge
Notes: This table replicates Panel A of Table 2. Panel A uses data aggregated at the county-month level instead ofcase-level (individual) data. The dependent variable there is the log of the number of cases. Panel B uses case-leveldata. The dependent variable there is the predicted sentence length base on the set of state-specific case severitycontrols. *** p<0.01, ** p<0.05, * p<0.1
In Panel A of Table A8 we aggregate our case-level data on county-month level, because the
variable caseload is on the county-month level. We compute it by counting the number of cases in
each court-month. Because in this panel we use aggregated data Columns III and VI (with case
and judge fixed effects) are omitted. We find no effect of private prison on caseload, suggesting,
that te effect is not driven by the police officers arresting more people and prosecutors preparing
more cases for the court.
In Panel B, we measure predicted sentence as fitted value of the regression of actual sentence
length on the set of state-specific case controls. Hence, this variable only uses information of
the case; i.e., the average sentence length for that type of crime in a state. We would expect
private prisons to have no effect on predicted sentence, as it should only be affected by the changes
in criminal legislation. Here, we set Column III to be empty because adding case controls would
50
explain away all variation in the dependent variable here. We find no effect of private prisons on the
predicted sentence length, suggesting that opening private prison does not affect the composition
of cases (in terms of their severity). It also suggests that prosecutors do not appear to be bringing
more serious charges due to opening of private prisons.
51
Table A9: Full Sample 2-months Dummy
I II III IV V VIDependent variable: Sentence (log months)
Panel A: full sample with a dummyD(Private prison opens within 2 months) 0.026* 0.028** 0.019** 0.021** 0.019** 0.018**
[0.0520] [0.0384] [0.0265] [0.0250] [0.0182] [0.0354]
Log private prison capacity -0.000 -0.000 -0.002 0.000 0.001 0.002[0.9490] [0.9864] [0.6759] [0.9380] [0.9202] [0.7936]
R-squared 0.366 0.380 0.435 0.416 0.446 0.450Observations 3,544,144 3,544,144 3,544,144 3,544,144 3,544,144 3,544,144Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: court FEs: state x year FEs: court x year
Linear trend: state x calendar-month FEs: judge
Notes: This Table replicates Panel D of Table 2 but instead of the log of private prison capacities as the mainexplanatory variable uses dummy equal to one if private prison was open within a 2-months time interval. In squarebrackets we report p-values for standard errors are clustered on state and county; *** p<0.01, ** p<0.05, * p<0.1
See Table A9 serves as a bridge from the core results We do get enough precision testing for an
effect around capacity changes if we use the full data;
The abundance of different space-time-varying fixed effects in the core CBCP identification
strategy makes it difficult to get at the time-path of the adjustment with any statistical precision.
Table A9 shows that we do get enough precision to test for an effect around capacity changes if we
use the full data.
52
Table A10: Event-Study Coefficients for Figure 4
I II III IVDependent variable: Sentence (months)
Opening of private prison
Closing of private prison
Opening of public prison
Closing of public prison
4 months before event 1.330 5.676** 0.330 0.511[0.5709] [0.0249] [0.5228] [0.3242]
3 months before event 1.428 4.142*** 0.184 -0.102[0.4135] [0.0041] [0.7855] [0.8509]
2 months before event 1.614 3.711** 0.525 0.138[0.2692] [0.0104] [0.2452] [0.8908]
1 month before event 0.212 2.700** -0.403 -1.273[0.9007] [0.0354] [0.5756] [0.2398]
1 month after event 3.666* 1.844 -0.788 -0.180[0.0837] [0.2471] [0.1956] [0.7494]
2 months after event 2.985** 2.009 0.110 -0.307[0.0394] [0.3446] [0.8537] [0.6375]
3 months after event 0.712 -2.422 -0.363 -0.138[0.7299] [0.2097] [0.4757] [0.8798]
4 months after event 1.101 -1.889 0.612 -1.000[0.5206] [0.3032] [0.6400] [0.5287]
R-squared 0.107 0.107 0.029 0.164Observations 163,372 155,354 434,725 353,513Notes: This Table estimates event-study specification 2. Column I reports results for the opening-of-private-prisonevents. In Column II, the events are closing of private prisons. Columns III and IV look at opening and closing ofpublic prisons, respectively. In square brackets we report p-values for standard errors are clustered on state and eventlevel; *** p<0.01, ** p<0.05, * p<0.1
53
Figure A6: Re-Estimating Figure 4 with Probations Excluded
Equation (2) for Private Prison Openings (left) and Public Prison Openings (right)
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Equation (2) for Private Prison Closings (left) and Public Prison Closings (right)
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Notes: Panels A and B graph the results of estimating equation (2) for private and public prison openings and closingswithout cases that received probation. The results are reported in Table A11.
54
Table A11: Event-Study Coefficients for Figure A6 with Probations Excluded
I II III IVDependent variable: Sentence (months)
Opening of private prison
Closing of private prison
Opening of public prison
Closing of public prison
4 months before event 2.244 6.688** 0.596 0.321[0.4354] [0.0221] [0.3536] [0.6024]
3 months before event 1.640 4.929*** 0.331 -0.174[0.3648] [0.0003] [0.7075] [0.7761]
2 months before event 2.245 4.326*** 0.934 -0.385[0.2340] [0.0063] [0.1193] [0.7497]
1 month before event 0.532 2.887** -0.360 -1.660[0.7807] [0.0439] [0.7113] [0.2031]
1 month after event 5.310* 2.182 -1.289 0.057[0.0623] [0.1552] [0.1620] [0.9092]
2 months after event 3.278** 2.067 -0.519 -0.035[0.0470] [0.4013] [0.5157] [0.9616]
3 months after event 0.689 -2.256 -0.649 0.050[0.8235] [0.2944] [0.3399] [0.9626]
4 months after event 0.697 -1.800 1.014 -0.940[0.7777] [0.3662] [0.5906] [0.6438]
R-squared 0.113 0.094 0.028 0.181Observations 103,572 130,337 299,338 274,357
Notes: This Table estimates event-study specification 2 without cases that received probation. Column I reportsresults for the opening-of-private-prison events. In Column II, the events are closing of private prisons. Columns IIIand IV look at opening and closing of public prisons, respectively. In square brackets we report p-values for standarderrors are clustered on state and event level; *** p<0.01, ** p<0.05, * p<0.1
55
Figure A7: Re-Estimating Figure 4 with Probability of Incarceration
Equation (2) for Private Prison Openings (left) and Public Prison Openings (right)
-.02
-.01
0.0
1.0
2
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-.01
-.005
0.0
05.0
1.0
15
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Equation (2) for Private Prison Closings (left) and Public Prison Closings (right)
-.03
-.02
-.01
0.0
1.0
2
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-.015
-.01
-.005
0.0
05.0
1
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Notes: Panels A and B graph the results of estimating equation (2) for private and public prison openings andclosings. The results are reported in Table A12.
56
Table A12: Event-Study Coefficients for Figure A7, Probability of Incarceration
I II III IVDependent variable: D(Incarceration / No Probation)
Opening of private prison
Closing of private prison
Opening of public prison
Closing of public prison
4 months before event -0.003 -0.015 0.001 -0.005[0.6841] [0.1032] [0.8431] [0.2857]
3 months before event -0.001 -0.015 0.003 -0.006[0.8400] [0.1231] [0.5415] [0.3276]
2 months before event -0.003 -0.012 -0.002 0.001[0.4846] [0.1163] [0.6142] [0.9066]
1 month before event -0.001 -0.009* 0.002 -0.006[0.8246] [0.0772] [0.7066] [0.3442]
1 month after event 0.006 -0.007* 0.007 -0.002[0.3225] [0.0914] [0.1404] [0.7391]
2 months after event 0.003 0.006 0.002 -0.006[0.2956] [0.3504] [0.6505] [0.2251]
3 months after event 0.005 -0.007 -0.000 -0.005[0.4283] [0.4103] [0.9291] [0.4743]
4 months after event 0.004 -0.006 0.001 -0.003[0.6370] [0.3077] [0.8802] [0.5909]
R-squared 0.285 0.482 0.282 0.338Observations 163,372 155,354 434,725 353,513
Notes: This Table estimates event-study specification 2. Column I reports results for the opening-of-private-prisonevents. In Column II, the events are closing of private prisons. Columns III and IV look at opening and closing ofpublic prisons, respectively. In square brackets we report p-values for standard errors are clustered on state and eventlevel; *** p<0.01, ** p<0.05, * p<0.1
Table A12 reports the coefficients displayed in Figure A7, where the event study analysis is
applied to the probability of incarceration. There is a marginally significant reduction in the
likelihood of being sentenced only the month before and the month after a private prison is closed.
57
Figure A8: Event-Study of Openings in High (left) vs Low (Right) Cost-Savings Settings
Panel A: Sentence Length
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-10
10
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Panel B: Probability of Being Incarcerated
-.05
0.0
5
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
-.02
-.01
0.0
1.0
2
-4 -3 -2 -1 0 1 2 3 4Relative time in months
Size of the Coefficients
Notes: Panels A and B graph the results of estimating equation (2) for private and public prison openings andclosings. The results are reported in Table A12.
58
Table A13: Interactions with Prisons’ Overcrowding
I II III IV V VIDependent variable:
Sentence (log months) Sentence (log months), no probations
D(Incarceration / No Probation)
Log private prison capacity 0.036** 0.022** 0.007* 0.014*** 0.006** 0.002[0.0125] [0.0448] [0.091] [0.0001] [0.0409] [0.4059]
Log private prison capacity -0.016* 0.006* -0.005**x D(total overcrowding) [0.0812] [0.072] [0.0106]
D(total overcrowding) -0.467 -0.171 0.061 -0.059 -0.172** -0.084[0.1443] [0.8006] [0.579] [0.6266] [0.0149] [0.5829]
Log private prison capacity -0.012 0.004 -0.004x D(overcrowding in private prisons) [0.2197] [0.3898] [0.1410]
D(overcrowding in private prisons) 0.098 0.020 0.021[0.2428] [0.5751] [0.2997]
Log public prison capacity -0.088 -0.207 -0.389 -0.331 0.036 0.000[0.8709] [0.6720] [0.120] [0.1662] [0.6988] [0.9987]
Log public prison capacity 0.054* 0.015 0.010 0.006 0.019*** 0.008x D(total overcrowding) [0.0725] [0.7959] [0.323] [0.5449] [0.0053] [0.5772]
R-squared 0.468 0.468 0.530 0.530 0.309 0.309Observations 765,168 765,338 570,674 570,674 765,338 765,338
Notes: This replicates Panel A of Table 2 This Table replicates Panel A of Table 2 but adds the interaction of logprivate prison capacities with a dummy for overcrowding in a state’s prisons. Crowding is defined as a state’s annualprison occupancy relative to its capacity. The distribution of this ratio is depicted in Figure A9. We use an indicatorfor over-crowing defined as D(total overcrowding) ≥ 1. Similarly, we compute overcrowding of the private prisons(D(overcrowding in private prisons)). The capacity is the same used everywhere in the data. The occupancy data isannual data from the Bureau of Justice Statistics (Carson and Mulako-Wangota 2020). In square brackets we reportp-values for standard errors are clustered on state and border segment; *** p<0.01, ** p<0.05, * p<0.1
We argue in our paper that our results are not likely to be driven by capacity or over-crowding
considerations. A capacity- or crowding-based explanation for the effects we find is inconsistent
with the effect being concentrated in only private prisons, because there are as many new public
prison openings in our data as private ones, and they are of similar magnitude. Table A13 makes
this point clearer, by showing that prison (over-)crowding interacts weakly and (across columns)
inconsistently with our baseline effect, and does not nullify the baseline effect of prison capacity.
59
Figure A9: Overcrowding hist
0.5
11.
52
2.5
Den
sity
.5 1 1.5 2Total prison population / total prison capacities
Notes: Figure A9 depicts the ratio of a state’s annual prison occupancy over its capacity. This ratio is used (as anindicator) in Table A13.
60
Tables A14–A16 report robustness checks on Table 4. In Table A16, we check the robustness of
the results to capping the reported cost savings. In the case of Nevada and Arkansas, these cost
savings surprisingly large (55%, and 48%), and these are reported from local news reports (see
Appendix A.3). In Table A16, we cap these cost savings at 15% (the maximum number obtained
from actual data/estimates) and re-estimate the model. Reassuringly, the key patterns in the table
are not affected by capping the cost-savings data in this way.
61
Tab
leA
14:
Cost
-Savi
ngs
vs
Dir
ect-
Infl
uen
ceC
han
nel
s:N
oP
rob
atio
n
III
III
IVV
VI
VII
VII
IIX
XN
O P
roba
tion
Sam
ple:
Log
pri
vate
pri
son
capa
city
0.59
10.
240
0.03
31.
377*
**1.
490*
**4.
908*
*0.
508*
*[0
.119
8][0
.342
0][0
.715
0][0
.002
2][0
.001
3][0
.015
6][0
.045
5]
Log
pri
vate
pri
son
capa
city
3.92
8**
0.53
70.
509
x sh
are
save
d[0
.020
8][0
.306
8][0
.394
0]
Log
pri
vate
pri
son
capa
city
0.07
10.
012
0.50
8**
in lo
w s
avin
g st
ates
[0.5
192]
[0.9
083]
[0.0
452]
Log
pri
vate
pri
son
capa
city
1.11
5***
0.15
4***
0.61
8***
in h
igh
savi
ng s
tate
s[0
.007
8][0
.005
8][0
.000
1]
Pro
xim
ity
to e
lect
ion
0.21
9***
0.56
3***
4.77
8**
4.77
9**
[0.0
018]
[0.0
037]
[0.0
282]
[0.0
281]
Pro
xim
ity
to e
lect
ion
x-0
.444
*-0
.429
*-0
.429
*
Log
pri
vate
pri
son
capa
city
[0.0
596]
[0.0
875]
[0.0
875]
Δ H
igh
and
Low
sav
ings
, p-v
alue
[0.0
170]
**[0
.217
3][0
.396
3]
R-s
quar
ed0.
294
0.29
40.
294
0.32
50.
325
0.52
40.
524
0.52
40.
524
0.52
4O
bser
vati
ons
570,
674
570,
674
570,
674
2,69
9,23
72,
699,
237
671,
426
671,
426
671,
426
671,
426
671,
426
Log
pub
lic
pris
on c
apac
ity
FE
s: s
tate
x f
isca
l-ye
ar
FE
s: q
uart
er F
E
F
Es:
cou
rt-b
orde
rpai
r
F
Es:
sta
te x
yea
r
FE
s: c
ourt
-bor
derp
air
x ye
ar
D
emog
raph
ic c
ontr
ols
Cas
e co
ntro
ls
F
Es:
judg
e
Dep
ende
nt v
aria
ble:
Sen
tenc
e (m
onth
s)
CB
CP
Ful
lJu
dge
sam
ple
w/o
VA
, CO
, MN
, KY
No
tes:
This
table
re-e
stim
ate
sT
able
4w
ithout
pro
bati
ons.
Insq
uare
bra
cket
sw
ere
port
p-v
alu
es.
Sta
ndard
erro
rsare
two-w
aycl
ust
ered
on
state
and
bord
erse
gm
ent
inco
lum
ns
I–II
I,tw
o-w
aycl
ust
ered
on
state
and
county
inco
lum
ns
IV–V
,and
thre
e-w
aycl
ust
ered
on
state
,ca
lendar-
yea
r,and
quart
er-o
f-yea
rin
colu
mns
VI-
X.
***
p<
0.0
1,
**
p<
0.0
5,
*p<
0.1
62
Tab
leA
15:
Cost
-Savi
ngs
vs
Dir
ect-
Infl
uen
ceC
han
nel
s:F
ixed
Eff
ect
Var
iati
ons
III
III
IVV
VI
VII
VII
IIX
X
Sam
ple:
with
Pro
batio
nno
Pro
batio
n
Log
pri
vate
pri
son
capa
city
0.79
8**
0.87
8**
2.13
00.
154
0.17
80.
265*
**0.
511*
*0.
356
[0.0
433]
[0.0
287]
[0.2
773]
[0.5
079]
[0.1
147]
[0.0
023]
[0.0
309]
[0.2
723]
Log
pri
vate
pri
son
capa
city
1.39
81.
291
x sh
are
save
d[0
.154
4][0
.177
7]
Log
pri
vate
pri
son
capa
city
0.15
40.
356
in lo
w s
avin
g st
ates
[0.5
066]
[0.2
712]
Log
pri
vate
pri
son
capa
city
0.45
8**
0.63
6***
in h
igh
savi
ng s
tate
s[0
.020
9][0
.002
1]
Pro
xim
ity to
ele
ctio
n0.
209*
**0.
329*
1.44
11.
441
1.37
5***
3.85
23.
389
3.39
0[0
.008
8][0
.057
1][0
.470
5][0
.470
3][0
.000
9][0
.119
0][0
.220
4][0
.220
1]
Pro
xim
ity to
ele
ctio
n x
-0.1
58-0
.070
-0.0
70-0
.314
-0.2
62-0
.262
Log
pri
vate
pri
son
capa
city
[0.4
765]
[0.7
509]
[0.7
510]
[0.2
738]
[0.4
107]
[0.4
104]
Δ H
igh
and
Low
sav
ings
, p-v
alue
[0.1
551]
[0.1
787]
R-s
quar
ed0.
464
0.46
40.
464
0.46
90.
469
0.53
00.
530
0.53
00.
530
0.53
0O
bser
vatio
ns80
4,75
280
4,75
280
4,75
280
4,75
280
4,75
267
1,42
667
1,42
667
1,42
667
1,42
667
1,42
6L
og p
ublic
pri
son
capa
city
FEs:
sta
te x
fis
cal-
year
FE
s: q
uart
er F
E
FE
s: c
ourt
-bor
derp
air
FEs:
sta
te x
yea
r
FEs:
cou
rt-b
orde
rpai
r x
year
Dem
ogra
phic
con
trol
s
C
ase
cont
rols
FEs:
judg
e
Dep
ende
nt v
aria
ble:
Sen
tenc
e (m
onth
s)
No
tes:
Colu
mns
I–V
re-e
stim
ate
colu
mns
VI–
Xof
Table
4w
ith
alt
ernate
fixed
effec
ts.
Colu
mns
VI–
Xre
-est
imate
colu
mns
VI–
Xof
Table
A14
wit
halt
ernate
fixed
effec
ts.
Insq
uare
bra
cket
sw
ere
port
p-v
alu
es.
Sta
ndard
erro
rsare
two-w
aycl
ust
ered
on
state
and
bord
erse
gm
ent
inco
lum
ns
I–II
I,tw
o-w
aycl
ust
ered
on
state
and
county
inco
lum
ns
IV–V
,and
thre
e-w
aycl
ust
ered
on
state
,ca
lendar-
yea
r,and
quart
er-o
f-yea
rin
colu
mns
VI-
X.
***
p<
0.0
1,
**
p<
0.0
5,
*p<
0.1
63
Tab
leA
16:
Cost
-Savi
ngs
vs
Dir
ect-
Infl
uen
ceC
han
nel
s:C
app
edS
avin
gs
III
III
IVV
VI
VII
VII
IIX
XC
appe
d S
avin
gs (
15%
)S
ampl
e
Log
pri
vate
pri
son
capa
city
n/a
0.16
70.
001
n/a
n/a
n/a
0.19
5[0
.235
5][0
.990
9][0
.424
8]
Log
pri
vate
pri
son
capa
city
6.30
0***
1.98
8**
1.55
8*x
shar
e sa
ved
[0.0
033]
[0.0
186]
[0.0
976]
Log
pri
vate
pri
son
capa
city
n/a
n/a
n/a
in lo
w s
avin
g st
ates
Log
pri
vate
pri
son
capa
city
n/a
n/a
n/a
in h
igh
savi
ng s
tate
s
Pro
xim
ity
to e
lect
ion
n/a
n/a
1.89
9[0
.365
1]
Pro
xim
ity
to e
lect
ion
xn/
a-0
.134
Log
pri
vate
pri
son
capa
city
[0.5
713]
Δ H
igh
and
Low
sav
ings
, p-v
alue
R-s
quar
ed0.
310
0.34
10.
464
Obs
erva
tion
s76
5,33
83,
544,
144
804,
752
Log
pub
lic
pris
on c
apac
ity
FE
s: s
tate
x f
isca
l-ye
ar
FE
s: q
uart
er F
E
F
Es:
cou
rt-b
orde
rpai
r
F
Es:
sta
te x
yea
r
FE
s: c
ourt
-bor
derp
air
x ye
ar
D
emog
raph
ic c
ontr
ols
Cas
e co
ntro
ls
F
Es:
judg
e
Dep
ende
nt v
aria
ble:
Sen
tenc
e (m
onth
s)C
BC
PF
ull
Judg
e sa
mpl
e w
/o V
A, C
O, M
N, K
Y
No
tes:
This
table
re-e
stim
ate
sco
lum
ns
II–V
,and
IX–X
of
Table
4w
ith
Sa
vin
g sin
expre
ssio
n(3
)ca
pp
edat
15
per
cent.
Insq
uare
bra
cket
sw
ere
port
p-v
alu
es.
Sta
ndard
erro
rsare
two-w
aycl
ust
ered
on
state
and
bord
erse
gm
ent
inco
lum
ns
I–II
I,tw
o-w
aycl
ust
ered
on
state
and
county
inco
lum
ns
IV–V
,and
thre
e-w
aycl
ust
ered
on
state
,ca
lendar-
yea
r,and
quart
er-o
f-yea
rin
colu
mns
VI-
X.
***
p<
0.0
1,
**
p<
0.0
5,
*p<
0.1
64
Table A17: Introducing Small Measurement Error into Private Prisons
I II III IV V VI
Baceline with small measurement error into private prison capacity
Log private prison capacity 0.022** 0.021** 0.020** 0.018** 0.020** 0.021*[0.0209] [0.0336] [0.0310] [0.0322] [0.0433] [0.0552]
Log public prison capacity -0.166 -0.133 -0.094 -0.113 -0.159 -0.143[0.5987] [0.6354] [0.7508] [0.7409] [0.6321] [0.6865]
R-squared 0.379 0.390 0.455 0.468 0.468 0.472Observations 706,835 706,835 706,835 706,835 706,835 706,835Log public prison capacity FEs: state x fiscal-year Demographic controls Case controls FEs: state x year FEs: court-borderpair FEs: court-borderpair x year
Linear trend: state x calendar-month FEs: judge
Notes: This table redoes Table 2, with measurement error introduced into the private prisons capacity data. ***p<0.01, ** p<0.05, * p<0.1
In Section Appendix A.1 we discuss why the public prison capacity changes may be measured with
slightly more measurement error than private prison capacity changes. To address this concern, we
round the capacity of private prisons to the nearest 100, which rounds away small capacity changes.
In other words, we introduce measurement error into private prison capacity changes that matches
roughly the potential measurement error in public prison capacity changes. Table A17 reports the
results, and shows that the core results are basically unchanged. This is an important robustness
check, as it confirms that the core results are identifiers of the more major changes in capacity that
are also more likely to be salient to a judge in the same state.
65