Incarceration length and recidivism :
qualitative results from a collective pardon in France
Benjamin Monnery†
GATE Lyon St-Etienne
February 2015
Abstract
This paper exploits the French collective pardon of July 1996 to investigate how incarceration length alters criminal behavior after release. Eligibility to the pardon (and the amount of
sentence reductions granted) dramatically depended on whether prisoners were still in prison
on the date of the pardon, and for how long. This setting provides large, plausibly exogenous
variation in the overall amount of sentence reductions obtained by French prisoners. My IV
estimates show no significant causal effect of sentence reductions on overall probability of recidivism in the five years following prison. However, this overall null relationship hides a large
detrimental effect on property crime (+1.3 pp per day of sentence reduction), probably driven
by a surprise effect (prisoners released unexpected early are less pepared for successful reentry) ;
one the other hand, other types of offenses are not responsive to changes in incarceration length.
Using new sentences as a proxy for severity, it seems that property crime are less serious. The
paper also explores the practical implementation of the 1996 pardon in France, and discusses
the implications for both public policy and judicial practice.
JEL : K42
Keywords : economics of crime, prison, recidivism
†
Université de Lyon, Lyon, F-69007, France ; CNRS, GATE Lyon Saint-Etienne, Ecully, F-69130, France
Contact : [email protected] and 93 chemin des Mouilles - B.P.167 - 69131 - ECULLY cedex
I thank Annie Kensey for providing the data, and Paolo Buonanno, Frédéric Jouneau, Arnaud Philippe,
François-Charles Wolff, and seminar participants at GATE and 2nd Lyon-Torino PhD Workshop for comments
on earlier drafts. The financial support of Region Rhone Alpes (Explora’Doc) is gratefully acknowledged.
Introduction
There is now compelling evidence that prison sentences prevent crime through incapacitation
of criminals behind bars and general deterrence of potential offenders (Abrams, 2013). However,
it is less clear whether the experience of imprisonment reduces prisoners’ propensity to commit
crimes, as most inmates reoffend rapidly after release : in the five years following release, 77% of
prisoners are re-arrested in the U.S. (Cooper et al., 2014) while 59% are re-convicted in France
(Kensey and Benaouda, 2011).
These large rates of recidivism may suggest that prisons are ineffective in reducing inmates’ criminal propensity. Alternatively, they could simply reveal that most prisoners are deeply
immersed in criminal ways of life, and are therefore hard to deter and rehabilitate. The question of whether incarceration works as a rehabilitative and/or deterrent treatment has long
remained unanswered, because of the difficulty to estimate convincing causal effects : indeed,
court decisions (about incarceration, sentence length, etc.) are not drawn randomly but are
rather intended to fit each criminal’s profile. Therefore, the most hardened criminals receive the
harshest punishments, leading to severely biased estimates of the effect of punishement on reoffending. However, since the end of the 1990’s, a growing number of high-quality studies attempt
to investigate the effectiveness of prison exploiting quasi-experimental designs, where similar
individuals face dissimilar treatments 1 . One limitation of this strand of research is its large
focus on the United States, an outlier among developed countries in terms of sentencing (the
U.S. scores no 1 worldwide in incarceration rate and displays particularly long prison sentences).
The main contribution of this paper is to provide a new estimate of the net effect of incarceration on recidivism, using data from a European country, France. Relying on a representative
cohort sample of prisoners released in France in 1996-1997, this study focuses on the intensive
margin of prison and estimates how shorter (versus longer) incarceration affects the odds of
reconviction after release. A second contribution is to document the effects of incarceration
length in a more qualitative way than existing research, tracking how prison time affects the
type and seriousness of new offenses, and how these effects vary from one individual to another.
These qualitative aspects may prove crucial for public policy and practice, not only because
incarceration may have very heterogenous effects on criminal propensity, but also because even
small changes in the types of offenses committed after release could have huge consequences on
social welfare.
To deal with omitted variable bias in the relationship between time served and recidivism,
1. Such quasi-experimental designs have been used to estimate the effect of custodial versus non-custodial sentences, shorter versus longer incarceration, harsh versus lenient prison conditions, participation to rehabilitation
programs or not, etc.
1
I follow Maurin and Ouss (2009) and exploit a yearly political tradition in France where the
President granted collective pardons to almost all prisoners for the National Holiday, around the
14th of July of each year (from 1990 to 2006). This policy was explicitely aimed at combating
overcrowding in French prisons (a longstanding problem) by hastening prisoners’ release before
summer. Pardon eligibility and amount (how much sentence reductions were granted thanks
to the collective pardon) were based on a short list of administrative criteria designed by the
Government, which left no room for discretion by prison staff at each facility, where computation
was done in practice 2 .
Due to the cohort nature of the dataset, I focus on the pardon of July 1996 which granted
collective sentence reductions to all offenders who were incarcerated on the 9th of July, except
for those convicted for a short list of unfrequent offenses (terrorism, felony against children under
15, felony against police or correctional officers on duty, or international drug trafficking). All
eligible prisoners were granted one week of sentence reduction for each month that remained
to be served on the 9th of July, 1996, with the number of remaining months rounded upward,
and with sentence reduction capped at 4 months tops. Note that the 1996 collective pardon also
provided sentence reductions (of 2 months) to soon-to-be prisoners who were already convicted
to a prison sentence by July 9 and whose prison sentence would become definitive and enforceabe
by July 21. However, the dataset does not provide date of conviction or date of enforceability,
so it is difficult to predict which of the soon-to-be prisoners were actually eligible to the pardon.
Thus I restrict the analysis to offenders who were already in prison on the date of the pardon,
and whose pardon eligiblity and amount can be well predicted with available data.
The identification strategy exploits the arbitrariness of the pardon design, in the sense that
similar prisoners (in terms of initial sentence length notably) obtained very different amounts
of sentence reductions from the 1996 pardon, depending on their date of incarceration : keeping
initial sentence constant, individuals who had already served most of their sentence when the
pardon occured benefited little from it (because the remaining sentence was marginal) and
individuals who still had to serve several months in prison on July 9 benefited a lot from it.
This design provides a natural instrument for actual length of incarceration : the number of
months which remained to be served on the 9th of July 1996, controlling for initial sentence
length and other potential confounding factors. A second available instrument is simply whether
this number of remaining months is positive or not, i.e. whether prisoners still had some time
2. In case of manipulation in the computation of the pardon by prison staff, prisoners could press charges.
However, the fact that prison staff had no room for discretion and potential manipulation does not mean that
prison staff or other players (such as sentencing judges) had no way of by-passing the effect of the pardon on
time served by shrinking other types of sentence reductions left at their discretion. I adress this issue in detail
further.
2
left to serve on July 9 or whether they had already been released from prison (leaving them
unaffected by the collective pardon).
One difficulty with this methodology is to infer retrospectively the number of months that
remained to be served on the 9th of July, had there been no collective pardon in 1996. The dataset
only provides dates of incarceration and actual release, and amount of sentence reductions by
type (pardons, amnisties, good behavior, parole, etc.) aggregated over the whole prison spell.
Therefore, I need to infer prospective date of release from the data. In contrast to Maurin and
Ouss (2009) 3 , I first drop all individuals who were already in prison for the previous collective
pardon of July 1995 (only keeping individuals incarcerated after the 1st of August, 1995) to
have clean measures of the amount of sentence reductions which are due to the sole pardon of
1996 4 ; as explained earlier, I also drop all prisoners who entered prison after the pardon, since
pardon eligibilty and amount is hard to predict for them with date of conviction missing. Of
course, these sample restrictions reduce the scope of the study as I estimate the effect of sentence
reductions on a subsample of prisoners with quite short prison stays (< 2 years). However, these
prisoners still represent more than 80% of France’s inmates (DAP, 2013). Second, I compute
prospective date of release as the sum of the date of actual release and the amount of pardoned
time. This measure hypothesizes that the pardon was implemented fairly by prison staff, in
the sense that they followed the government’s rules for computation (which is credible since
prisoners could press charges in case of error). I later show that (1) this hypothesis provides the
best fit for the instrumental regression and the best F-statistic for the instrument(s) ; (2) the
results are hardly sensistive to this hypothesis (in robustness checks, I use a ”blind” method for
computing prospective date of release).
My IV estimates show that sentence reductions have no significant effect on the probability
of recidivism. However, this overall null relationship hides a large positive effect on new property
crime, and no effect on other types of offenses (violent, drug, traffic, etc.). The detrimental effect
on property reoffending seems to be driven by a very short-term surprise effect, in the sense
that prisoners who were released unexpectedly early after the pardon were less prepared for
successful reentry (in terms of employment, housing, etc.). My results also suggest that the
effects of prison time vary markedly between prisons and prisoners. Finally, using new sentences
(custodial or not) as a proxy, I confirm the idea that property crime tends be less serious.
3. Maurin and Ouss (2009) used the same dataset to estimate the effect of sentence reductions on recidivism.
However, they did not drop long-sentence prisoners but dropped prisoners who benefited from the pardon though
they were incarcerated after its date (possibly introducing bias in their study sample).
4. A small concern here is that the pardon variable may also include ”case-by-case” pardons, which are also
granted by the President but on a purely individual basis (usually in high-profile, controversial cases). These
individual pardons may add measurement error in prospective date of release, but their effect is likely to be
limited because ”case-by-case” pardons are very rare in the French system.
3
1 Related literature
A large body of evidence shows that prison sentences have a crime-preventing effect, first
by incapacitating offenders behind bars and second by detering potential offenders outside
prison (see Durlauf and Nagin (2011) and Abrams (2013) for good reviews). However, the
effect of longer sentences on recidivism among ex-prisoners is less clear, both empirically and
theoretically.
According to economists’ model of rational choice (Becker, 1968), harsher punishement increases the expected cost of crime and therefore deters crime. This basic idea can be extended to
offenders who have already experienced punishment : the specific deterrence hypothesis posits
that offenders who experienced harsher punishment (for example in the form of longer prison
sentences) update their beliefs about the true cost of crime (upward), which reduces their propensity to reoffend. However, serving longer spells behind bars may have collateral consequences.
First, it may decrease the opportunity cost of crime by reducing post-release labor market prospects (either through increased stigma or decreased human capital) or by reducing the utility
derived from law-abiding, free life (through reduced family bonds, labelling and prisonization).
Second, longer incarceration may increase the expected payoff from future crime by enhancing
prisoners’ criminal capital (in the form of new criminal skills, networks and opportunities).
For decades, empirical research has attempted to distinguish the net effect of time served
between these competing theories. However, most research until recently was flawed by the
fact that prison sentences are typically not exogenous but related to intrinsec risks of recidivism
(yielding inconsistent estimates due to omitted variable bias). One of the very few exceptions was
a controlled experiment run by Berecochea and Jaman (1981) in California, in which a random
group of prisoners received a 6-month sentence reduction whereas the control group served their
normal sentence. The results revealed a significant increase in return to prison among the earlyrelease group, suggesting a negative relationship between length of incarceration and probability
of recidivism.
However attractive, RCTs are ethically difficult to implement in the current judicial context.
Thus, to solve the omitted variable problem and identify causal effects of incarceration length,
researchers increasingly rely on natural experiments, i.e. quasi-random events which lead similar
offenders to face dissimilar prison sentences. One such source of exogeneity is when criminal
cases are allocated randomly between judges who differ in their levels of severity (some judges
being more prone than others to sanction to long prison sentences). These between-judges
sentencing disparities may serve as instruments for sentence length : applying this method to
the study of drug offenders in the District of Columbia in the U.S., Green and Winik (2010) do
4
not find evidence of any deterrent effect of longer prison sentences on future offending. Kling
(2006) and Loeffler (2013) use similar methods in other regions of the U.S. (Florida, California,
and around Chicago) to study how incarceration length affects not only crime participation but
also labor market outcomes : they also find that longer incarceration is not associated with
large, significant changes in post-release behavior 5 . However, these IV strategies tend to rely
on weak instruments (a potential source of inconsistency) and assume that judges can only
affect recidivism through the effect of longer versus shorter prison sentences (assuming away
other plausible mechanisms 6 ). A closely-related brand of research exploits differences in ability
between randomly assigned attorneys : using data from the region of Las Vegas, Abrams (2011)
finds a similarly insignificant effect of sentence length on probability of recidivism. However, his
results provide some evidence of specific deterrence among short prison sentences.
Alternative identification strategies rely on sentencing grids in the U.S., where judicial discretion is ”guided” (restricted) by mimimum and maximum sentences, depending on each offender’s
risk score and offense type. These grids generate large discontinuities in sentence length between similar offenders (at the cutoff scores, from one cell to the next). Kuziemko (2013) exploits
these discontinuites and a mass release in the state of Georgia to estimate the causal effect of
sentence length on recidivism among a sample of low-seriousness offenders : her estimates show
a 1.3 pp reduction in probability of reconviction for each extra month in prison, suggesting a
large specific deterrent effect of incarceration length. Using the same data, two papers study
whether alternative explanations may drive Kuziemko’s results : Ganong (2012) investigates the
confounding effect of prisoners’ aging and incapacitation, and concludes that specific deterrence
is still at work after controlling for these other channels. Similarly, Zapryanova (2014) distinguishes the true effect of early release from the effect of the symetric increase in time under
parole supervision (after release) : she confirms the existence of a (slighty smaller) deterrent
effect of longer incarceration, while the duration of parole supervision has no effect on its own.
Overall, the existing empirical evidence on the effect of incarceration length on recidivism
is mixed, with some studies pointing to a null relationship and others suggesting a specific deterrent effect. This inconsistensy in prior findings may have several explanations : an obvious
explanation is that the effects of time served in prison may vary widely between local contexts,
due to unmeasured differences in prison conditions, access to rehabilitation programs, socioeconomic environment, etc. : for instance, Mastrobuoni and Terlizzese (2014) show that spending
5. Landerso (2012) provides competing evidence from Denmark, showing that longer prison sentences due to
a policy reform in 2002 actually benefited to violent offenders in terms of post-release employment and earnings,
probably thanks to an increased access to rehabilitation programs.
6. For example, we may imagine that progressive judges indeed sanction to shorter prison sentences than
conservative judges, but at the same time pronounce longer suspended sentences or more mandatory therapeutic
sentences, which may also affect recidivism.
5
more time in an open prison instead of a traditional prison significantly reduces recidivism in
Italy. A second explanation is that the relationship between incarceration length and recidivism
may be non-linear (for example U-shaped as argued by Orsagh and Chen (1988)), leading estimates to vary depending on the share of short versus long prison sentences in the samples
under study : Drago et al. (2009) tend to confirm this intuition on quasi-experimental data from
Italy, as prisoners serving long sentences (about 6 years) tend to be less deterred than others
by longer expected sentences in case of recidivism. Finally, a third explanation may be that the
effects of incarceration length are heterogenous and vary markedly between criminal profiles, as
argued by Mears et al. (2014). Surprisingly few high-quality quantitative papers investigate this
possibility 7 , though qualitative evidence exists : Souza and Dhami (2010) and van der Laan
and Eichelsheim (2013) show that individuals differ greatly in their reaction to the experience
of imprisonment, notably depending on their age and prior experience of prison 8 . We may also
imagine that imprisonment triggers very different mechanisms depending on the types of offenders and their motivations : rational economically-motivated offenders may reconsider the costs
and benefits of criminal activity while incarcerated ; drug dealers may use prison time as an
opportunity to meet new customers and suppliers ; and impulsive violent offenders may remain
unaffected, for example.
In addition, current quantitative research pays almost no attention to whether incarceration
length alters the type and seriousness of new offenses. We may hypothesize that more time in
prison hardens inmates, turning them away from petty crime in favor of more serious offenses.
The underlying mechanisms may have to do with material prison conditions (seen as inherently
violent), social exclusion, or peer effects. Indeed, a nascent literature on interactions inside
prison provides strong evidence of large crime-specific peer effects : among juvenile prisoners in
Florida, Bayer et al. (2009) find that the probability to reoffend in a particular offense type is
strongly related to own and peers’ prior experience in that offense. Ouss (2011) and Damm and
Gorinas (2013) also find evidence of peer effects for drug crime in French and Danish prisons,
especially when cellmates belong to the same age group. These results suggest that imprisonment
can alter recidivism qualitatively, notably through the development of criminal networks and
the exchange of criminal skills inside prison. With exposure to criminal peers highly depending
on time served in prison, changes in incarceration length may also have qualitative effects on
7. On the related topic of general deterrence, Drago et al. (2009) investigate heterogeneity but find little evidence of differential effects between males and females, young and old prisoners, violent and property offenders...
8. Interviewing a sample of first-time and recurrent inmates in England, Souza and Dhami (2010) show that
first-time prisoners are more likely than experienced inmates to see prison as an ”opportunity for rehabilitation”,
though they feel worse about being imprisoned and are more concerned about being attacked. Experienced
prisoners tend to view emprisonment more pessimistically as a waste of time, the only often-cited benefit being
a chance to improve health.
6
recidivism. From a social welfare perspective, these effects are likely to be crucial since the
total burden of crime predominantly depends on how serious crimes are, instead of their total
number. Unfortunately, these qualitative effects don’t receive proper attention in most existing
high-quality empirical work on the effects of time served : for instance, Kuziemko (2013) only
runs one ”seriousness-weighted” regression (to confirm specific deterrence), and Abrams (2011)
only uses a poor measure of seriousness (expected sentence lenght for the new crime type),
finding weak evidence of escalation (positive, insignificant IV estimates of current sentence
length on future sentence length).
2 Data
The dataset is drawn from a nationaly representative survey of 2408 inmates run by Kensey
and Tournier (2005) for the French prison administration. All sampled individuals are convicted
prisoners who were released from French prisons between May 1st, 1996 and April 30th, 1997.
Data include sociodemographic and judicial characteristics recorded at entry (gender, age, educational level, employment status, marital status, homelessness, French citizenship), detailed
information regarding the initial conviction (type of offense committed, prison sentence length)
and the number of prior convictions. Importantly, the dataset precisely records the dates of
incarceration and release, the amount of pre-trial detention, as well as the amount of sentence
reductions over the whole prison spell by type of reductions : good behavior, pardons, parole,
etc.
As explained in the introduction, the dataset doesn’t decompose ”pardoned time” between
the successive collective pardons (though remember that pardons were a yearly tradition in
France and prisoners incarcerated for long sentences may have benefited from several successive
pardons), therefore I restrict the analysis to prisoners who were incarcerated after August 1,
1995, to make sure that all the prisoners under study only benefited from the 1996 pardon, if
any. I also drop individuals incarcerated after the pardon, since eligibility can not be retrieved
from available data. Finally, I drop all prisoners who benefited from early-release programs 9 :
these programs often grant very large sentence reductions for a very selected group of prisoners
with the best chances of successful reentry, adding endogeneity in the data and weakening the
instrument(s) 10 .
To measure recidivism, nation-wide criminal records were consulted in June 2002. They
cover all offenses that led to any new conviction by this date, and include date and type of new
9. Libération conditionnelle, semi-liberté, and placement à l’extérieur.
10. As a matter of fact, the instruments lose about all of their power when parolees are included, suggesting
no effect of the pardon on the length of incarceration of these prisoners.
7
offense(s) in a quite detailed format, as well type and length of new sentence(s). This measure
of recidivism is particularly reliable for three reasons : (a) it requires final conviction for a new
crime (and not simply rearrest or parole violation) committed after release ; (b) it covers a 5-to-6
years follow-up period, much longer than most empirical studies in the field ; (c) it captures new
offenses no matter whether the new sentence is custodial or not. However, it was impossible to
obtain criminal records for 200 releasees (death or other unknown reason).
Finally, I retrieve rudimentary prison-level characteristics (region, type of prison, capacity,
overcrowding rate as of Jan 1, 1996) which are matched to each prisoner 11 . Among the 183
different prisons represented in the original dataset, it was impossible to clearly identify three
facilities except for their type and region (probably because they shut down since 1996) so I
replace the missing values for capacity and overcrowding by the region-type averages.
The final study sample consists of 746 observations. Table 1 shows descriptive statistics for
the main sociodemographic and judicial characteristics over the study sample. 96% of the study
sample are men, as in the current prison population. Educational attainment is greater than
middle school for 67%. 43% had a job before incarceration and 13% were married. The share
of foreign prisoners is 34%, while 19% were homeless. Prisoners had already been convicted 3.5
times before on average, and were 30 years old at release. The most serious offense leading to
prison was property crime for 31%, assault or sex offense for 22%, drug crime for 16%, traffic
offense for 8%, and it did not fall in any of these categories for 22% of the sample.
Table 2 provides descriptive statistics regarding initial prison sentence and actual time served
behind bars. On average, sampled prisoners were convicted to prison sentences of 276 days (9
months), and actually spent about 73% behind bars (198 days). Overall, sentence reductions
hastened release by 78 days, with two thirds of sentence reductions coming from good behavior
(52 days) and one third from the pardon (26 days). Overall, 8% of initial sentence were not
actually served behind bars thanks to the 1996 pardon on average (this percentage reaches 15%
when focusing on the 399 prisoners who effectively benefited from the pardon).
Table 3 shows statistics about reoffending in the study sample. All recidivism measures are
consistent across dates of release, as they only capture reoffenses that are committed exactly
within a 5-year window after release. I focus on reoffending data for the first new conviction
only and not all reconvictions over the 5-year follow-up period, since the impact of incarceration
length (if any) is expected to fade out as times goes by and new sanctions accumulate. 38%
of the study sample are not reconvicted for any new offense in the 5 years following release,
yielding a recidivism rate of 62%. Most recidivists are reconvicted for only one new offense, but
11. For the minority of inmates who served time in several different prisons for the current sentence, I can only
retrieve information for the last prison facility before release, since previous facilities are not recorded.
8
Table 1: Sociodemographic and judicial variables
Variables
Male
Education > middle school
Employment
Married
Foreigner
Homeless
Nb of prior convictions
Age at release
Initial offense
Assault/Sex
Property
Drug
Traffic
Other
Mean
Range
96.25%
67.29%
43.30%
13.40%
33.64%
19.03%
3.51
30.44
[0 ;1]
[0 ;1]
[0 ;1]
[0 ;1]
[0 ;1]
[0 ;1]
[0 ;21]
[15.95 ;69.97]
21.98%
31.37%
16.49%
8.04%
22.12%
[0 ;1]
[0 ;1]
[0 ;1]
[0 ;1]
[0 ;1]
Sample Size
746
22% are reconvicted for several offenses during the same trial. The lower part of Table 3 shows
the distribution of reoffenses across the five crime categories. Percentages don’t add up to 100%
as each ex-prisoner may either not reoffend, commit one new offense of type j, or commit several
new offenses of one or more types. About one fourth of ex-prisoners commit a new property
crime, and recidivism rates are over 10% for all types of new offenses except for drug (5.3%).
Finally, new sentences are displayed in Table 4. About 40% of ex-prisoners are sentenced
back to prison for their first reconviction (if any) : they represent 2/3 of reoffenders. The other
third is sentenced to non-custodial sanctions such as probation or suspended prison time. For
Table 2: Sentence length and time served
Variables
Mean
SD
Min
Max
Initial sentence length
Actual time served
Pre-trial detention
Sentence reductions
Good behavior
Pardon
Amnisties
% Sentence Reductions
From Pardon only
275.92
195.08
44.04
78.30
51.52
26.16
0.62
26.67
7.92
181.88
125.96
81.13
65.26
37.24
35.71
13.72
9.91
9.43
8
8
0
0
0
0
0
0
0
1140
856
414
617
241
202
360
77.78
73.89
Sample Size
746
9
Table 3: New offenses in the 5 years following release
Number of offenses
None
1
2
3+
All
% in whole sample
% among recidivists
38.11
-
48.26
77.98
10.85
17.53
2.79
4.50
100
100
Assault/Sex
Property
Drug
Traffic
Others
11.61
23.57
5.29
12.38
19.47
Types of offenses
% in whole sample
those who receive new prison sentences, average length is 6.95 months (the median is much
smaller, 4 months). This is shorter than initial prison sentences (7.5 months), suggesting that
crime seriousness decreased pre- versus post-prison. This decrease is even more striking when
one considers the potential effect of sentence enhancement laws, which are likely to lengthen
prison sentences from one trial to the next, holding crime seriousness constant. Therefore, it
seems that crime seriousness significantly decreased before versus after incarceration. A simple
explanation of this pattern may be aging (as criminals get older, they commit less serious crimes)
but it could also be that time served in prison had a small deterrent and/or rehabilitative effect.
I properly investigate this hypothesis later.
Table 4: New sentences among reoffenders
Type of sentence
Custodial
Non-custodial
Total
38.60
23.30
61.89
Prison sentence length
Mean (SD)
Median
Range
in months
6.95 (11.58)
4
[0 ; 144]
% in whole sample
3 Identification strategy and Instrumental Regression
The aim of this paper is to estimate the causal effect of shorter incarceration on reoffending
(keeping initial sentence and other variables constant), using the total amount of sentence
reductions as variable of interest. The main empirical challenge is that most sentence reductions
are presumably endogenous, as they are explicitely designed to reward or punish prisoners,
depending on their efforts to behave well in prison and reenter society successfully. In France,
such incentives are at play not only for the allocation of the very selective early-release programs
(which explicitely target prisoners displaying the best reentry prospects) but also for the more
casual ”good behavior” sentence reductions, whose eligibility are universal in theory (as long
as prisoners do not misbehave in prison) but which leave much room for discretion in practice
10
(both in terms of eligibility and amount granted) 12 . If the best behaving prisoners are also those
with the lowest intrinsec criminal propensity, then any correlation between sentence reductions
and probability of recidivism would be negatively biased and yield overly optimistic estimates
of the true effect of shorter incarceration on future crime.
The French collective pardon of July 1996 allows me to control for this source of bias as it
introduced large, plausibly exogenous changes in sentence reductions between similar prisoners
(convicted to the same initial sentences notably) depending on their date of incarceration (and
independently of in-prison misconduct or any other unobservable factor). The pardon provided
one-week sentence reductions for each month that remained to be served on the 9th of July 1996.
The number of remaining months was rounded upwards, leading to a theoretical step-function
of 7-days increments for each marginal month (in the limit of 4 months of pardoned time).
My IV strategy attempts to replicate the design of the pardon : I compute for each prisoner
the number of months that remained to be served on July 9 (rounded upward), called M R.
Prospective date of release, had there been no pardon, is calculated as the sum of actual date
of release and the amount of sentence reductions from the pardon (Explain why + evidence
that this is what prison staff actually did) 13 . Depending on date of release, the number
of remaining months M R can be either positive or negative 14 : I create an indicator variable
(M R > 0) to capture the discontinuous change in sentence reductions between those who had
some time left versus no time left to serve on the 9th of July 1996. Then, I compute M R∗(M R >
0) to capture the (somewhat linear) effect of having one additional month remaining on the date
of the pardon, among those who were still in prison at that time.
12. These ”good behavior” sentence reductions are separated in two in practice : Réduction de Peine (RP) and
Réduction de Peine Supplémentaire (RPS) in French. RP are often seen as universal sentence reductions but they
can be withdrawn in case of misconduct. The definition of misconduct and the extent of withdrawals remain to a
large extent at the discretion of sentencing judges and prison staff. Regarding RPS, these sentence reductions are
more exceptional and reward particularly good behavior and reentry prospects, allowing even larger discretion
in their allocation.
13. As explained in the introduction, the empirical strategy highly depends on how one computes prospective date of release, had there been no pardon. In baseline regressions, I compute it as follows :
P rospectiveReleaseDate = ActualReleaseDate + P ardonedT ime. This computation implicitely assumes that
pardoned time was fully converted into more sentence reductions, i.e. that sentencing judges did not use these
mandatory sentence reductions as substitutes for other, more discretionary types of sentence reductions (good
behavior, parole, etc.). This assumption may well hold for several reasons : (1) good behavior sentence reductions are almost automatic in French law (on paper, sentencing judges can only withdraw them after prisoner
misconduct), (2) sentencing judges fix the level of good behavior sentence reductions only once a year for each
prisoner, thus for many cases they examine, it would be very difficult to anticipate how the next pardon (if any)
will affect the length of incarceration. Thus, good behavior sentence reductions (which represent most of total
sentence reductions) are unlikely to be widely used as substitutes for pardoned time. However, one may argue that
sentencing judges may still be tempted to attenuate the effect of the collective pardon, by shrinking good behavior
sentence reductions or by delaying early-release under parole. To allow for such a possibility, I run robustness
checks where P rospectiveReleaseDate is computed as ActualReleaseDate + a fraction of P ardonedT ime. No
sensitivity is detected, i.e. none of the estimates differ substantilly from the baseline scenario when allowing
f raction < 1 (down to 0.2).
14. Remember that the sample includes prisoners released between May 1996 and April 1997, so most individuals have positive values
11
The two available instruments are therefore M R∗(M R > 0) and (M R > 0), whose expected
effect on sentence reductions should be positive and significant, while M R should have no effect
on its own as it captures the effect of months remaining on individuals who were already out of
prison by July 9.
Figure 1: Probability of pardon and sencence reductions, depending on M R
The actual data is plotted in Figure 1. The first graph shows the frequency of pardon
beneficiaries (whatever the amount) depending on the number of remaining months, which
ranges from -2 to +16 in the study sample. The second graph similarly shows how the average
amount of total (blue) and pardon (red) sentence reductions evolve with M R. These graphs
display a reassuring pattern that is consistent with the pardon design : the share of prisoners who
obtained some pardoned time goes from virtually zero 15 to more than 70% 16 between prisoners
who were released just before versus just after July 9. The amount of sentence reductions (both
total or from the pardon) also increases with M R, as expected by the reform. Note that the
actual amount of pardoned time perfectly fits the theoretical prediction represented by the red
line (P ardonedT ime = 7 ∗ M R) for M R ≤ 7 and then deviates a bit : such deviation may come
from (1) increased variance, as the number of observations in each bin diminishes, or (2) from
the fact that the computation of sentence reductions does not follow official rules for high levels
of sentence reductions. I later run robustness checks to make sure that my results do not rely
on this messier part of the data, where the instruments are likely to be weaker.
15. The non-zero frequency at M R = 0 may be due to a few prisoners who benefited from ”case-by-case”
presidential pardons, which may add (a bit of) measurement error in my data. My IV estimates should not be
affected however.
16. Remember that the pardon design excluded some prisoners, though incarcerated on the date of the pardon,
from the eligibility pool because of their initial offense : this is presumably why the frequency is not 100%.
However, a more puzzling fact is the variation in P r(P ardon) along M R : one explanation is that the share
of excluded offenders may somewhat differ between bars ; a second explanation is simply that the number of
observations diminishes as M R increases, yielding greater variance.
12
From an econometric point of view, this graphical pattern brings support to the identification
strategy : prisoners experienced large differences in total sentence reductions depending on how
much time remained to be served on July 9. The identification strategy yields the following
instrumental regression :
SentRedip = α0 + α1 M R ∗ (M R > 0)ip + α2 (M R > 0)ip + α3 M Rip + ...
+ Γ0 Initial.Sent.ip + Θ0 P retrial.Detip + Λ0 Xip + Φ0 Zp + up + eip (1)
while the outcome (recidivism) equation writes :
Recidip = β0 + β1 SentRedip + β2 M Rip + ...
+ Π0 Initial.Sent.ip + ∆0 P retrial.Detip + Ψ0 Xip + Ω0 Zp + µp + ip (2)
The econometric specification allows a linear trend between sentence reductions and M R
(using both positive and negative values), and only exploits the discontinuity at M R = 0 (α2 )
and the somewhat linear relationship afterwards (α1 ), as the (now strictly positive) number of
months remaining increases. For identification, it is crucial to control for length of initial prison
sentence, in order to compare prisoners who were convicted to similar prison sentences but who
actually served different amounts (initial sentence is highly correlated with M R) : I include a
5th degree polynomial for initial sentence length. This degree provides the best fit in terms of
adjusted R2 , but higher- and lower-ordered polynomials yield very similar results. Another set of
control variables deals with pre-trial detention since the level of sentence reductions mechanically
depends on how much of the initial sentence was served before trial (as sentence reductions are
only available to prisoners who already received a sentence) : therefore, I include a linear term
for the total amount of pre-trial detention. Similarly, the amount of pardoned time mechanically
depends on whether prisoner i was on pre-trial detention on July 9, and how much time he still
served on pre-trial detention after that date (if prisoner i receives his final conviction long after
the pardon, it will reduce his potential for pardoned time as he will have served more of his final
sentence -potentially all of it- before trial) : I include a dummy for pre-trial detention status
on July 9 and a linear variable for the length of pre-trial detention post-July 9. I also control
for a large set of individual socio-demographic and judidical characteristics : these include age
at release (to capture the obvious aging effect of sentence reductions on recidivism, see Ganong
(2012)), dummies for type of most serious initial offense (property, assault-sex, drug, traffic and
others), and dummies for gender, education, employment, marital status, homelessness, French
13
citizenship, prior convictions (and the number of). Finally, I control for some rudimentary
prison-level characteristics : region where the prison is located 17 , type of prison (Centre de
Détention, Centre Pénitentiaire, or Maison d’Arrêt) 18 , and prison overcrowding ratio (actual
population/capacity) as of January 1st, 1996.
The structure of the error term allows heteroskedastic errors that are correlated within prison
facilities, to account for the fact that (1) some of the regressors only vary at the prison level, (2)
prisoners from the same facility face roughly the same environment, (3) inmates may influence
one another (peer effects). To compute such clustered-robust standard errors, the study sample
consists of a large enough number of clusters (121 facilities) but cluster sizes vary markedly
(mean size is 6.17, SD = 11.97). In robustness checks, I compute simple standard errors, or
I exclude the largest prison facilities to compute less size-sensitive clustered-robust standard
errors. The main results remain unaffected.
In order to illustrate the strenght of my instruments, I estimate Equation 1 by OLS (Table
5, col. 1). As expected, the estimates are positive and significant for both instruments : on
average, prisoners whose prospective date of release lies just after the 9th of July obtained 4
more days of sentence reductions than similar prisoners released just before the pardon date.
Plus, each additional month remaining to be served on July 9 increased sentence reductions by
4.5 days on average. Reassuringly, M R has no detectable effect on sentence reductions among
those released before the pardon (insignificant point estimate of -0.002). All the individual-level
controls also have expected signs : the total amount of sentence reductions tends to increase
(non-linearly) with initial sentence length, and sharply decreases with pre-trial detention : a
10-day increase in pre-trial detention diminishes sentence reductions by 0.9 day overall, and
by 1.6 days when only post-pardon pre-trial detention is considered. Plus, being on remand on
the day of the pardon reduces sentence reductions by 19 days on average. Regarding prisonlevel characteristics, sentence reductions do not significantly differ by type of prison, but prison
overcrowding matters : a 1-unit increase in the population/capacity ratio increases the average
amount of sentence reductions by 7.3 days. This significant relationship suggests that prison
staff and sentencing judges adapt their decisions to capacity constraints, and hasten inmates’
release in overcrowded prisons. Overall, this model fits the data very well (R2 = 90%) and yields
strong instruments with F-statistics well above 10.
The second column shows the results from the same regression when all the additional
17. French territory is divided into 10 regions by the correctional administration.
18. There are different types of prisons in France, which host particular criminal profiles : for example, prisoners
serving relatively long sentences are usually sent to Centres de Détention with enhanced focus on rehabilitation,
whereas short-sentence prisoners and pre-trial detainees are usually incarcerated in the more common Maisons
d’Arrêt with stricter rules and less services available.
14
socio-demographic and judicial characteristics are excluded from the model. The fact that the
coefficients of interest remain similar in magnitude and significance is reassuring and consistent
with the design of the 1996 pardon, as it didn’t mention any individual characteristic as a
criterion (other than certain types of offenses for exclusion). However, I later use the full set
of covariates (column 1) as my preferred specification, as additional covariates can increase the
precision of my estimates (but my substantive results never depend on them).
Finally, the third column regresses the full model on the subsample of eligible prisoners
(i.e. those who had time left to serve on July 9 and who effectively benefited from the pardon,
no matter the amount) : following the design of the pardon, one would expect each additional
month remaining to increase total sentence reductions by 7 days. However, the estimate (5.240)
is statistically different from 7. This gap suggests that the pardon didn’t reduce incarceration
length as much as it should have in theory : for a theoretical 7-day reduction in incarceration
length, eligible prisoners actually received only 5.2 days of sentence reductions. This 25% difference is evidence that prison staff and sentencing judges did somehow attenuate the effect of the
collective pardon, probably by shrinking ”good behavior” sentence reductions so as to maintain
prisoners behind bars longer. However, this strategy was of limited success, as prisoners still
benefited from significant reductions in incarceration length thanks to the pardon.
Overall, these results provide strong evidence that the collective pardon of July 1996 truly
resembles a quasi-natural experiment which introduced large, very significant changes in sentence reductions between similar prisoners, depending on their (plausibly exogenous) date of
incarceration. I now exploit this source of exogeneity in sentence reductions to identify the
causal relationship between length of incarceration and reoffending behavior.
4 Results
4.1 Sentence reductions and overall probability of recidivism
First, I investigate the effect of sentence reductions on the probability of reoffending in the 5
years following release (Table 6). As a benchmark, I estimate a simple probit model for Equation
2 without correction for endogeneity (col. 1). The average marginal effect is slighlty negative
(-0.0004) but insignificant.
Since sentence reductions are usually targeted to the ”best” prisoners (in terms of in-prison
behavior and reentry prospects), one would expect this coefficient to be biased downward. This is
confirmed when I correct for such omitted variable bias, by estimating the full model (Eq. 1 and
Eq. 2) simultaneously (col. 2) : the estimated average marginal effect after IV probit becomes
15
Table 5: Instrumental regressions by OLS
Y = Sentence Reductions (in days)
(1)
(2)
(3)
4.505***
(0.855)
3.999*
(1.805)
4.269***
(0.902)
3.471*
(1.695)
5.240***
(0.455)
-
-0.002
(0.811)
0.285***
(0.023)
4.266
(2.406)
-16.339
(8.750)
17.351
(14.512)
-5.680
(6.792)
-0.088***
(0.015)
-18.814***
(4.061)
-0.158***
(0.039)
0.159
(0.102)
0.266
(0.805)
0.287***
(0.023)
4.496
(2.531)
-16.276
(8.619)
16.902
(14.460)
-5.641
(6.954)
-0.087***
(0.014)
-18.824***
(4.235)
-0.160***
(0.041)
0.114
(0.066)
0.250***
(0.021)
14.856*
(6.501)
-48.561
(24.712)
47.156
(32.267)
-7.955
(8.781)
-0.030
(0.022)
-12.977
(13.089)
-0.266
(0.136)
0.135
(0.136)
ref.
-2.274
(4.360)
-4.718
(2.667)
7.321**
(2.506)
YES
ref.
-2.585
(4.419)
-4.755
(2.702)
7.514**
(2.634)
YES
ref.
-4.745
(5.065)
-6.323
(4.159)
10.172**
(3.435)
YES
Additional X
R-squared
N
YES
0.906
746
NO
0.906
746
YES
0.896
398
F-stat : α1 = α2 = 0
F-stat : α1 = 0
15.23
27.77
12.66
22.41
132.79
Instruments
M R ∗ (M R > 0)
(M R > 0)
Individual-level controls
MR
Initial sentence
Initial sentence2
Initial sentence3
Initial sentence4
Initial sentence5
Total pre-trial detention
Detention status on July 9
Pre-trial detention after July 9
Age at release
Prison-level controls
Type : Centre de détention
Type : Centre Pénitentiaire
Type : Maison d’Arrêt
Overcrowding rate
Region FE
∗
p < 0.05,
∗∗
p < 0.01,
∗∗∗
p < 0.001
Robust standard errors in parentheses, clustered at16
prison level. ∗ p < 0.05 ; ∗∗ p < 0.01 ; ∗∗∗ p < 0.001
If included, the set of additional controls includes dummy variables for gender, education level, employment
status, marital status, French citizenship, homelessness, prior convictions>0 and a continous variable for
number of prior convictions.
largely positive (+0.008), suggesting that each additional day of sentence reduction actually
increases probability of recidivism by 0.8 pp. Though this estimate is still not statistically
different from zero, it is consistent with the existence of (positive) selection in the allocation of
sentence reductions to prisoners. The point estimates are very similar when the additional set
of controls is dropped (col. 3), or when using Two-Stage-Least-Squares instead of simulatenous
probit estimation by Maximum Likelihood (col. 4). The results also remain very similar when
using only one instrument, when using simple standard errors instead of prison-level CRSE,
when dropping large values of M R (not shown).
While sentence reductions do not seem to impact overall probability of recidivsm within 5
years, they may have large significant effects in the short run. To test this, I create dummy
variables capturing recidivism in the first, second, third, fourth and fifth years separately. None
of the estimates are large and significant (not shown) : for example, the point estimate for
first-year recidivism is 0.0020 and very imprecise, suggesting that sentence reductions do not
matter either in the short nor in the long run in terms of risk of reoffending. This null result
also holds when splitting the analysis by quarters after release.
Table 6: Sentence reductions and overall P(Recid)
(1)
Probit
(2)
IV Probit
(3)
IV Probit
(4)
2SLS
-0.0004
(0.0008)
0.0080
(0.0065)
0.0086
(0.0075)
0.0091
(0.0096)
Y2 = Sentence Reductions
M R ∗ (M R > 0)
-
(M R > 0)
-
4.3139***
(0.9878)
4.4391**
(1.6135)
4.1379***
(1.0538)
3.8681**
(1.5048)
4.5050***
(0.8549)
3.9991*
(1.8053)
YES
YES
746
YES
YES
746
YES
NO
746
YES
YES
746
-
28.99
25.29
15.23
Y1 = Recidivism
Sentence Reductions
Baseline X
Additional X
N
F-stat : α1 = α2 = 0
Robust standard errors in parentheses, clustered at prison level. ∗ p < 0.05 ; ∗∗ p < 0.01 ; ∗∗∗ p < 0.001
IV Probits are estimated by ML as system of two equations. Average Marginal Effects are reported.
All regressions include the same set of baseline controls as in Table 5 col 2. When included, the set of
additional controls includes dummy variables for gender, education level, employment status, marital status,
French citizenship, homelessness, prior convictions>0 and a continous variable for number of prior convictions.
17
4.2 Sentence reductions and Type(s) of new offense(s)
Shorter versus longer incarceration does not seem to have a clear-cut effect on overall probability of recidivism on average. However, time served may alter which offenses are committed
after release. To investigate such crime-specific effects, I decompose recidivism in five nonmutually-exclusive dummies capturing the type(s) of offense(s) committed in the 5-year followup period 19 : property crime, assault-sex, drug, traffic, and others. I successively estimate by
IV probit the probability to reoffend in each crime category after release. The results appear in
Table 7.
The effects of sentence reductions strikingly differ between the type of new offense considered.
On one hand, sentence reductions have a very significant detrimental effect on future property
offenses : the estimated average marginal effect suggests that each additional day of sentence
reduction increases probability of committing property crime after release by 1.3 pp. Since the
1996 collective pardon shortened actual incarceration length by 4.5 days on average for each
remaining month, my estimates imply a very large impact of the pardon on property offending :
a prisoner with 2 months remaining to be served on July 9 had a 6 percentage points greater
probability of committing property crime after release than an otherwise-similar prisoner with
only 1 month left to serve (4.5 ∗ 1.3pp = 5.8pp).
On the other hand, sentence reductions have no significant effect on any of the other crime
categories, although most point estimates are negative. Noteworthy is the fact that sentence
reductions do not have any detrimental impact on future assaults and sex offenses (AME of
-0.0006) which are often considered as the most harmful in terms of public safety and social
welfare.
Taken as a whole, these results suggest that sentence reductions have crime-specific effects :
they significantly increase the probability of new property crime, but have no effect on other
offenses, yielding an insignificant (slighlty positive) overall effect (as obtained in Table 6). I now
investigate which mechanisms may drive these divergent effects of sentence reductions on future
crime.
4.3 Exploring the mechanisms linking sentence reductions to future offending
The fact that only property crime is responsive to changes in sentence reductions suggests
a variety of mechanisms linking incarceration length to recidivism, instead of a single, straightforward mechanism. For example, if specific deterrence and rehabilitation were major factors
19. I only use offense data from the first criminal conviction after release. However, this first case may refer to
several offenses of different types (though it is quite rare in the sample).
18
Table 7: Sentence reductions and Type(s) of new offense(s)
(1)
Property
(2)
Assault-sex
(3)
Drug
(4)
Traffic
(5)
Others
0.0131***
(0.0024)
-0.0006
(0.0067)
-0.0054
(0.0067)
0.0019
(0.0066)
-0.0028
(0.0097)
4.5059***
(0.8528)
3.9961**
(1.3994)
4.4965***
(0.8494)
4.0292*
(1.8251)
4.9200***
(1.0854)
3.4286+
(1.8146)
4.5156***
(0.8337)
3.9588*
(1.7747)
4.5074***
(0.8396)
3.9905*
(1.7995)
Baseline X
Additional X
N
YES
YES
746
YES
YES
746
YES
YES
686
YES
YES
746
YES
YES
746
F-stat : α1 = α2 = 0
30.91
31.81
20.71
31.93
31.90
Y1 = Recidivism
Sentence Reductions
Y2 = Sentence Red
M R ∗ (M R > 0)
(M R > 0)
Robust standard errors in parentheses, clustered at prison level. ∗ p < 0.05 ; ∗∗ p < 0.01 ; ∗∗∗ p < 0.001
IV Probits are estimated by ML as system of two equations. Average Marginal Effects are reported.
All regressions include the same set of baseline controls as in Table 5 col 2. When included, the set of
additional controls includes dummy variables for gender, education level, employment status, marital status,
French citizenship, homelessness, prior convictions>0 and a continous variable for number of prior convictions.
preventing recidivism, one would probably expect positive estimates for all types of offenses. As
a matter of fact, leaving aside property crime, most point estimates are very small and insignificant (somewhat negative) : this null effect is in line with many empirical studies finding no
relationship between time served and recidivism (e.g. Green and Winik (2010), Abrams (2011)).
This result does not imply that prison time has no consequences on future social, economic,
psychological outcomes, but simply that the net effect of serving more versus less time in prison
has minimal effect on future offending, on average.
However, these averages may hide large beneficial and detrimental effects in the sample,
depending on prisoners’ characteristics or on prison conditions. Plus, property crime seems very
particular in its elasticity to sentence reductions. I now explore these two issues successively.
4.3.1
Are the effects of sentence reductions heterogenous between prisons and prisoners ?
I investigate whether the effect of sentence reductions varies between prisoners. To do so, I
successively split the sample in two groups (above/below median) by prior social resources, prior
criminal experience, and age. I find evidence that sentence reductions have significantly beneficial effects (AME of -0.013**) among experienced prisoners (with more than 2 prior convictions)
and no significant effect on less experienced criminals. I also find that sentence reductions significantly decrease recidivism among prisoners who had more social resources at entry (measured
19
as a [0-3] score = housing + work + marriage), but has no significant effect on those with lower
resources.
I also investigate how the effects of sentence reductions vary between prisons. I do not have
data on access to work or rehabilitation programs in each prison, so I only on overcrowding. Prior
research tends to show that prison overcrowding increases risk of recidivism, suggesting that
sentence reductions in overcrowded prisons may be more beneficial than in non-overcrowded
prisons 20 .
4.3.2
Why are sentence reductions so detrimental for property crime ?
The detrimental effect of sentence reductions on property crime (AME = 1.3 pp per day)
may have several explanations : the first is that property crime, which is usually considered as
more rational than other offenses, may respond to changes in incentives. Specifically, shorter
incarceration may simply foster the commission of ”rational” new offenses, because sentence
reductions are perceived as an unanticipatedly lenient punishment, which in turn reduces specific
deterrence. However, if this is true, it is surprising not to observe a similarly rational effect on
traffic offenses, which are also quite responsive to legal incentives 21 . Plus, if this mechanism
applied, one would expect this rational adaptation to be particular salient among prisoners
initally convicted for a property crime (i.e. the ”rational” offenders) : to test this hypothesis,
I successively estimate the effect of sentence reductions on new property crime among those
initially convicted for a property vs a non-property offense (Table 8, col. 1 and 2). I find that
the effect of sentence reductions is very similar among property and non-property offenders
(AME = 0.013), casting doubt on the deterrence story.
A second explanation for the large positive response of property crime to sentence reductions
has to do with in-prison training and education : prisoners may use prison time to invest in their
own human capital (and therefore their own reentry prospects) through vocational training and
education. Such human capital investment could well increase the opportunity cost of future
crime (by increasing employability and earnings). Sentence reductions could have the unintended
consequence of stopping this positive process, leading to the release of inmates with poorer job
prospects and fueling economically-motivated crime. The dataset doesn’t allow me to properly
test this hypothesis (I don’t have information on in-prison education and training, or on job
market outcomes after release) but it seems overly-optimistic in practice, as most prisoners do
not get to work or attend classes while incarcerated.
Finally, a third and more plausible explanation has to do with preparedness for release :
20. Discuss the results
21. On the deterrability of traffic offending, see Hansen...
20
for most inmates, reentry after release is a difficult process which needs careful preparation
(with family, probation agents, public administrations, etc.) to secure housing, find a job, etc.
Sentence reductions, especially those from collective pardons, may well be unanticipated by
many prisoners and hasten their release unexpectedly 22 : if this is the case, sentence reductions
would leave prisoners less prepared for reentry and worsen their economic/social situation at
release, leading to increased property crime. This surprise effect would presumably be especially
large for prisoners who are released soon after the pardon, as they have little time to adapt and
prepare before release compared to those released long after the pardon. To test this mechanism,
I split the sample between prisoners who were actually released less than 80 days after July 9
(the median), and those released later (in October 1996 or later). I suspect the surprise effect
to be particularly salient among the first group, and less so in the second group. The results,
reported in Table 8 col. 3 and 4, support the surprise effect hypothesis : the estimate for sentence
reductions is positive and significant among those who were released shortly after the pardon
date (AME = 0.0050*), and equals virtually zero among those who were released long after the
implementation of the pardon (AME = -0.0008).
Table 8: Sentence reductions and future property crime
Y1 = Property reoffending
Sentence Reductions
Y2 = Sentence Reductions
M R ∗ (M R > 0)
(M R > 0)
Baseline X
Additional X
Sample : prisoners incarcerated for...
Sample : prisoners released...
N
F-stat : α1 = 0
(1)
(2)
(3)
(4)
0.0133+
(0.0084)
0.0131***
(0.0023)
0.0050*
(0.0021)
-0.0008
(0.0024)
6.9554**
(2.6066)
8.3016**
(2.5447)
3.6572***
(1.0196)
2.5499
(1.5997)
9.4445***
(1.4399)
-
5.5138***
(1.1746)
-
YES
YES
Property
234
YES
YES
Non-property
512
YES
YES
Before D+80
238
YES
YES
After D+80
265
24.79
13.31
43.02
22.04
Robust standard errors in parentheses, clustered at prison level. ∗ p < 0.05 ; ∗∗ p < 0.01 ; ∗∗∗ p < 0.001
IV Probits are estimated by ML as system of two equations. Average Marginal Effects are reported.
All regressions include the full set of baseline and additional controls.
22. One may argue that collective pardons were a yearly tradition in France, suppressing the effect of surprise.
However, the criterion for pardon eligibility and the amount granted changed (more or less) from one year to the
other, so it was impossible for a given prisoner to precisely predict before the date of the pardon when he would
eventually be released. Plus, it seems fair to say that not all prisoners knew about it this tradition.
21
4.3.3
Short-term effects
I now test whether the effects of sentence reductions on property and non-property crime
vanish over time, as might be expected (especially if one has a surprize/unpreparedness mechanism in mind). To do so, I compare the estimated effects 23 of sentence reductions on property
reoffending within different time windows : first quarter after release, second quarter, third
quarter, fourth quarter, and additionally second year, third year, fourth year and fifth year.
These estimates are plotted in Figure 2 as well as their 95% confidence intervals. The graph
suggests the existence of very large effects in the first quarter of release (estimated effects close
to +2 pp for property crime), and virtually no effect in the following quarters and years.
Figure 2: Effects of SentRed on property crime at various time windows
4.3.4
Property crime = Less serious crime ?
The preceding results tend to show that sentence reductions increase prisoners’ propensity
to commit property crime after release, but do not affect their propensity to commit other
types of offenses on average. However, the crime categories I use may be too wide to document
the level of seriousness of new offenses, and therefore their implications for public safety and
social welfare. To better estimate how sentence reductions affect the severity of recidivism, I
now exploit a plausibly more qualitative variable : the severity of new sentences.
In France as in most countries, the principle of proportionality requires judges to adapt
sentences to the seriousness of each offense. Therefore, the severity of new sentences can be
used as potentially good proxies for the social harm caused by each offender. Judicial sentences
can be splitted in two broad categories with clear hierarchy : custodial sentences (imprisonment)
versus non-custodial sentences (suspended prison, probation, fines, etc.).
The independent variable of my structural equation then becomes a dummy variable taking
one in case of new custodial sentence in the five years following release, and zero otherwise. The
23. Estimates obtained after GMM estimation of a two-equation linear model, instead of IV Probit by ML
(convergence issues for some time windows).
22
results after estimating IV probit models are reported in Table 9.
As a benchmark, I first estimate a probit model on the full sample. The correlation between
sentence reductions and probability of a new prison conviction is significantly negative, but of
limited size (-0.0015*). When I estimate the full model by IV probit, the effect becomes slighly
positive but insignificant, suggesting no overall impact of sentence reductions on the probability
to go back to prison in the five years following release.
However, this estimate is obtained on the full sample, which consists of reoffenders and nonreoffenders. In order to capture the effect of sentence reductions on the severity of future crime,
it seems appropriate to focus on those who actually reoffend. Therefore, in the next columns of
Table 9, I exclude all prisoners who are not reconvicted in the follow-up period. The correlation
after probit remains similarly negative (-0.0015*), suggesting that prisoners who obtained more
sentence reductions were less likely to go back to prison, conditional on recidivism. Again,
one would expect this estimate to be biased downward due to positive selection (i.e. prisoners
displaying the lowest risk of return to prison obtaining more sentence reductions). In fact, my
estimates after running IV probit models suggest the opposite : the estimated causal effect of
sentence reductions on return to prison now becomes even more negative (a tenfold increase)
and remains significant 24 : the estimated average marginal effect suggests that each additional
day of sentence reduction decreases the probability of reconviction to prison among those who
actually reoffend by 1 percentage point.
This negative effect should come as no surprise, as it confirms that sentence reductions
had qualitative effects : they increased property offending while not affecting non-property
recidivism, yielding an overall decrease in the average severity of the newly committed offenses
(as measured by the severity of new court sentences).
However, it is interesting to note that sentence reductions are not allocated effectively so as
to reduce the conditional risk of return to prison (the selection process actually seems negative),
but more simply so as to reduce probability of recidivism. It seems that prison staff and sentencing judges fail to properly predict how serious new offenses will be, but only predict whether
some reoffending will occur. This failure may have large consequences in terms of future prison
population, public safety, and eventually social welfare.
24. When focusing on reoffenders only, the instrumental variable (M R > 0) loses power, but instruments still
pass the rule-of-thumb F > 10. When I only exploit the first, strongest instrument M R ∗ (M R > 0) and use the
second as a control variable, I obtain a similar but more precise point estimate, which is reassuring.
23
Table 9: Sentence reductions and New Prison Sentence
(1)
Probit
(2)
IV Probit
(3)
Probit
(4)
IV Probit
(5)
IV Probit
-0.0015*
(0.0008)
0.0034
(0.0116)
-0.0015*
(0.0006)
-0.0107+
(0.0062)
-0.0099*
(0.0048)
Y2 = Sentence Reductions
M R ∗ (M R > 0)
-
-
(M R > 0)
-
4.3100**
(1.2896)
4.4451*
(2.0797)
4.3069**
(1.5460)
1.9252
(3.3384)
4.4784***
(1.2039)
-
Y1 = Prison Reconviction
Sentence Reductions
Baseline X
Additional X
Sample
N
F-stat : α1 = α2 = 0
YES
YES
YES
YES
All prisoners
746
746
-
28.22
YES
YES
YES
YES
YES
YES
Reoffenders only
488
488
488
-
12.68
13.84
Robust standard errors in parentheses, clustered at prison level. ∗ p < 0.05 ; ∗∗ p < 0.01 ; ∗∗∗ p < 0.001
IV Probits are estimated by ML as system of two equations. Average Marginal Effects are reported.
All regressions include the full set of baseline and additional controls.
Conclusion
This paper provides new estimates from a European country of the net effect of incarceration
length on recidivism. I exploit plausibly exogenous sentence reductions induced by the French
collective pardon of July 1996, and attempt to estimate how sentence reductions impact not
only the quantity of new offenses (probability of recidivism) but also their quality (type of crime,
severity).
My results confirm that incarceration length have crime-specific effects. More precisely, I
find consistent evidence that sentence reductions have large, short-term detrimental effects
on probability to commit property crime, while they leave unaffected other types of offenses.
The mechanisms underlying this dual relationship seems to be driven by the surprise effect
of collective pardons among French prisoners, which hastened their release unexpectedly and
left them less prepared for successful reentry. I also find that the increase in property crime
actually converts into less serious crimes committed on average, as measured by the lower
risk of reconviction to prison conditional on recidivism. From a public policy perspective, the
social savings from shorter incarceration of all prisoners may possibly outweight the costs of
increased property, less serious crime after release. However, it is beyond the scope of this study
to quantify the net social welfare consequences of sentence reductions, especially without any
available estimate of the general deterrent effect of prison sentences in France.
24
Another interesting set of results has to do with judicial practices : first, my results tend
to show that, even though the computation of sentence reductions from the pardon followed
the government’s rules, the effect of the pardon on actual incarceration length was eventually
attenuated. It seems that prison staff and sentencing judges used some level of discretion to
cut other types of sentence reductions (good behavior sentence reductions) so as to partly delay
prisoners’ release. My results also suggest that sentencing judges allocate good behavior sentence
reductions in an efficient way so as to limit risk of recidivism (by targeting prisoners with low
propensity to reoffend), but failed to allocate them efficiently to obtain a far-reach reduction in
the seriousness of new offenses. As a matter of fact, it seems that the selection process granted
sentence reductions to prisoners with lower propensity to reoffend but posing actually greater
threat to society in terms of crime severity.
25
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Appendix
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