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2015-11
Rasmus Landersø
PhD Thesis
Essays in the Economics of Crime
DEPARTMENT OF ECONOMICS AND BUSINESS
AARHUS UNIVERSITY DENMARK
Essays in the Economics of Crime
By Rasmus Landersø
A PhD thesis submitted to
School of Business and Social Sciences, Aarhus University,
in partial fulfilment of the requirements of
the PhD degree in
Economics and Business
May 2015
Contents
I
Does Incarceration Length Affect Labor Market Outcomes?
1 Introduction
1
3
2 Background
2.1 The Reform of the Penal Code . . . . . . . . . . . . . . . . . . . . . . . . . .
2.2 Imprisonment in Denmark . . . . . . . . . . . . . . . . . . . . . . . . . . . .
7
10
14
3 Data
16
4 Econometric Framework
21
5 Results
5.1 Macroeconomic Trends . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
5.2 Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
24
29
33
6 Conclusion
36
References
38
A Supplementary Results
43
B Data Appendix
48
II
53
School Starting Age and the Crime-Age Profile
1 Introduction
55
2 Institutional settings and mechanisms
2.1 Educational Institutions and School Starting Age . . . . . . . . . . . . . . .
2.2 Institutions Guarding Juvenile Crime . . . . . . . . . . . . . . . . . . . . . .
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3 Methodology
62
4 Data
64
5 Results
5.1 Timing of Birth Within the Calendar Year and School Starting Age
5.2 Crime Results: 2SLS . . . . . . . . . . . . . . . . . . . . . . . . . .
5.3 Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . .
5.4 Potential Mechanisms and Effects on Alternative Outcomes . . . . .
6 Conclusion
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References
84
A Supplementary Results
88
III
The Effects of Admissions to Psychiatric Hospitals
105
1 Introduction
107
2 Background
109
2.1 Institutional framework - mental health care in Denmark . . . . . . . . . . . 111
3 Data
112
4 Econometric Framework
121
5 Results
5.1 2SLS Results . . . . . . . . . . . . . . .
5.2 Gender and age differences . . . . . . . .
5.3 Marginal Treatment Effects . . . . . . .
5.4 Effect of Admittance on Spouses’ Labour
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Market Outcomes
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6 Conclusion
145
References
147
A Supplementary Results
152
B Data Appendix
163
Preface
Foremost, I wish to thank both of my two supervisors, Marianne Simonsen and Helena Skyt
Nielsen, who have guided me safely towards the point where I now can hand in my thesis.
I appreciate that you have always been forthcoming while treating me as your peer, and
I have gained significantly from being allowed to work and learn independently througout
our joint project. I also appreciate that you have been very considerate towards our ‘long
distance relationship’.
I also need to thank a further number of individuals who have helped me in different
ways throughout my PhD. First, I would like to thank James Heckman for hosting my visit
to the the University of Chicago. I have learned tremendously from this visit and from our
project. Second, I owe thanks to Greg Veramendi, for being an expert tutor in latent factor
models and for mediating my contact with the University of Chicago. Third, I wish to thank
Christian Dustmann for his guidance and tutoring throughout our joint work.
Almost eight years ago, I attended a TA session in Introductory Macroeconomics at 8 in
the morning - we were only three students present. After the class, the TA showed a jobposting for a research assistant at the Rockwool Foundation Research Unit (RFRU) with
deadline that very day. I went home, wrote an application, and have been working there
ever since. I have not always known that I would write a PhD in Economics, and the truth
is that I am not certain I would be where I am now, had it not been for that particular
TA session. Working for RFRU and research director Torben Tranæs has showed me the
crossroad between empirical research, microeconomics, and policy relevance, which quickly
turned out to be exactly where my research interests lie. After completing my master’s
degree, Torben Tranæs offered to fund my PhD. I am very grateful for the years of support
RFRU has given me, while provinding me with the freedom and funding to follow my research
interests (whether these took me to Aarhus or Chicago).
I
During all of the years at RFRU, I have been so fortunate to work alongside Peter,
Peer, and Lars who soon became my good friends. Peter and I have shared office and have
supported each other through the ups and downs that academic (and non-academic) life
brings through those years. Peer and Lars have both taught me very valuable lessons; Peer
has been my everyday tutor into protestant work-ethics and economics, while Lars has shown
that criminology, fatherhood, and pub-crawling does intersect somewhere.
Selma, your love and ever-steady support has helped me through these past years’ endevours. You have listened patiently to my ongoing (and seemingly endless) monolugues on
the topics of this thesis, and you joined me on my academic travels around the world. I
treasure the life we live together. Finally, however much I may be thrilled by the prospect
of completing my PhD, this will not be the most significant event in my life during the past
three years. Josephine - my daughter - does not know what PhD and Economics mean. Yet,
as her presense makes all of the long and hard working days seem infitesimal, I cannot list
all the important people in the making of this thesis without mentioning her.
May 20th, 2015
Copenhagen
Rasmus Landersø
II
Summary
This PhD dissertation consists of three self-contained papers. The papers are not meant to
constitute an entity even though they share a lot of common ground in topics, data souces,
methodology, and outcomes of interest. Furthermore, the three essays all focus on aspects
of at-risk behavior and on providing a better understanding of the outcomes experienced by
marginalized individuals in soceity.
In the first paper, titled Does Incarceration Length Affect Labor Market Outcomes?, I
investigate the effects of time spent in jail on subsequent unemployment rates, dependency on
other public transfers, and earnings. The previous literature on the effects of imprisonment
focuses on the effect of imprisonment at the extensive margin and not at the intensive
margin: the lengths of incarceration. At the intensive margin, the effect of incarceration
length will depend on the marginal costs and benefits of time spent in jail and not the
costs and benefits of the jail sentence in total. I use a DD and DDD approach to study
the effects of Danish reform in 2002 for offenders who are convicted of simple violence,
which constitute around 20% of all imprisonment-sentences in Denmark. The reform mainly
affected offenders who serve incarceration spells of one or two months, which are modal
incarceration spells in Denmark. I find that the increase in incarceration length resulted in
lower rates of unemployment, unchanged dependency on other public transfers, and higher
earnings. Using survey data, I show that participation in rehabilitation increase by time
spent in jail, especially during the first months. Thus a likely mechanism is through increased
participation rates for which an offender’s pre-reform sentence would otherwise have been too
short, leaving the offender solely with the possible stigma, job-loss, and general alienation
from the labor market which incarceration might involve. Finally, I show that the reform
mainly affected young men with relatively short criminal histories. As younger individuals
may be more malleable than older offenders, young offenders may benefit significantly more
III
from rehabilitating programs or change their perception of the payoff to crime to a larger
degree compared to their older peers with more extensive criminal histories.
The second paper, titled School Starting Age and the Crime-Age Profile (joint with H. S.
Nielsen and M. Simonsen) investigates long-term effects of school starting age (SSA) while
providing novel insights into the determinants of life-cycle criminal behavior. Parents may
manipulate their childs school starting age; in our sample of children born in Denmark in
the period from 1981-1993 around 20-25% of boys and 10-13% of girls start school one year
later than the law dictated. In order to obviate this non-random selection in SSA, we exploit
that Danish children typically start first grade in the calendar year they turn seven, which
gives rise to a fuzzy regression discontinuity design that shifts SSA by one year around New
Year. First, we present causal evidence of the underlying nature of onset and persistence
of criminal behavior across an individuals life-course. We find that the onset of crime can
be modified by life-course and is not only determined by age per se while the continuation
of criminal behavior is affected by both age, life circumstances, and criminal opportunity.
Finally, we find that incapacitation seems to play an important role and that the effects of
SSA vary across different parental characteristics as education and labor market attachment.
In the third paper The Effects of Admissions to Psychiatric Hospitals (joint with P.
Fallesen) we examine the effects of admitting a patient as an inpatient upon first contact
with a psychiatric hospital on the patient’s subsequent contacts and admissions to psychiatric hospitals, self-harm/suicide attempts, labor market outcomes, criminal behavior, and on
his spouse’s labor market attachment. We address the fundamental differences between the
counterfactual outcomes of individuals who are admitted and those who are not by using
the intensity of patient contacts to a hospital the weeks before an individual’s first contact
(a proxy for a given hospital’s occupancy rate) as an IV. We find that inpatient care has
ambiguous effects. In the short run, inpatient care addresses the patients’ immediate needs,
to the benefit of both the patients and potential victims of crime. Being admitted lowers
IV
self-inflicted lesions/cuts and leads to large reductions in crime shortly after the admission.
We show that the crime reduction is driven by incapacitation during the period of utmost
mental distress. In the longer run people admitted into inpatient care experience a higher
degree of institutionalization which also leaves them with poorer long-term labor market
outcomes. We also identify large heterogeneity across observable and unobservable characteristics. Males experience the largest reductions to crime whereas females experience the
largest increase in re-admissions and reductions to labor market attachment. By estimating
Marginal Treatment Effects we show that patients with the most severe disorders experience significant reductions to overdoses of drugs/alcohol and the largest reductions to crime,
whereas patients with the least severe disorders are institutionalized to a larger extend. Finally, we identify additional sources of positive externalities of hospital admissions, as we
find that it increases the employment rates of patients’ spouses.
V
Resumé
(Danish summary) Denne ph.d. afhandling består af tre separate kapitler. Kapitlerne er ikke
tænkt eller skrevet som en enkelt enhed eller sammenhængende tekst, men de har en lang
række fællestræk i form af emner, datakilder, metoder og relevante resultater. Hvad mere
er, så fokuserer de tre artikler alle på aspekter af risikoadfærd og forsøger at give en bedre
forståelse af de livsforløb, som personer, der befinder sig i sammenfundets margin, oplever.
I det første kapitel, Does Incarceration Length Affect Labor Market Outcomes? undersøger
jeg, hvordan indespærringslængde påvirker kriminelles efterfølgende indtægt, afhængighed
af overførselsindkomster og arbejdsløshedsrater. Den eksisterende litteratur om effekterne af
fængsling fokuserer primært på den ekstensive margin og ikke på den intensive margin: længden af fængslingen. På den intensive margin vil effekten af indespærringslængde afhænge af
de marginale omkostninger og fordele ved den specifikke tid i fængsel, ikke omkostningerne
og fordelene ved fængselsdommen som en helhed. Jeg anvender en difference-in-differences
(DD) og triple-differences (DDD) tilgang til at undersøge effekterne af en dansk reform
fra 2002 for kriminelle, som bliver dømt for simpel vold (Straffelovens §244), hvilket udgør
omkring 20% af alle fængselsdomme i Danmark. Reformen påvirkede primært kriminelle,
som aftjente domme på 1 eller 2 måneder, hvilket er de hyppigst anvendte domslængder i
Danmark. Jeg finder, at den længere tid i fængsel resulterer i lavere arbejdsløshedsrater,
samme afhængighed af overførselsindkomster og højere gennemsnitsindtægt. Ved hjælp af
data fra en spørgeskemaundersøgelse blandt indsatte i danske fængsler viser jeg, at deltagelse i rehabilitering stiger med tiden brugt i fængsel, specielt i de første måneder. Derfor
er øget deltagelse i rehabilitering en sandsynlig mekanisme bag resultaterne. Indespærringslængderne før reformen har sandsynligvis været så korte, at rehabilitering har været
umulig, hvorfor de indsatte udelukkende er blevet efterladt med de mulige stigma, tab af job
og generel fremmedgørelse fra arbejdsmarkedet, som fængsling kan medføre. Endelig viser
jeg, at reformen primært påvirkede unge mænd med en forholdsvis kort kriminel baggrund.
VI
Yngre individer er muligvis mere fleksible end ældre kriminelle og derfor mere modtagelige
overfor rehabiliteringsprogrammer. De har muligvis også større chancer for at skifte opfattelse af værdien af kriminalitet i sammenligning med deres ældre, mere kriminelt erfarne,
medindsatte.
Det andet kapitel, School Starting Age and the Crime-Age Profile (skrevet sammen med
H. S. Nielsen og M. Simonsen) undersøger langsigtede effekter af skolestartsalder (SSA) og
bidrager med ny indsigt i sammenhængen mellem kriminalitet og alder. Forældre kan manipulere deres børns skolestartsalder; i vores sample af børn født i Danmark i perioden fra
1981-1993 startede omkring 20-25% af drenge og 10-13% af piger et år senere end loven
dikterer. For at omgå denne højst selektive udvælgelse af, hvilke børn der starter senere og
tidligere, udnytter vi, at danske børn ofte starter i første klasse i det kalenderår, hvor de
fylder syv. Dette resulterer i et fuzzy regression discontinuity-design, der skubber SSA med
et år for børn født lige omkring nytår. Herved undersøger vi sammenhænge mellem start
og fortsættelse af kriminel opførsel i forhold til et individs livsforløb og alder. Vi finder, at
starten på kriminel løbebane er knyttet til et individs livsforløb og ikke til alder som sådan.
Til sammenligning er fortsat kriminel adfærd både påvirket af alder såvel som kriminelle
muligheder og livsforløb. Vi finder endvidere, at indespærring/fasholdelse i uddannelse lader
til at være en vigtig mekanisme heri. Gennem vores undersøgelse leverer vi også ny viden
omkring konsekvenserne af skolestartsalder på længere sigt. Endelig finder vi, at effekterne
af skolestartsalder varierer mellem forældre med forskellige uddannelser og arbejdsmarkedstilknytning.
I det tredje kapitel, The Effects of Admissions to Psychiatric Hospitals (skrevet sammen
med P. Fallesen) undersøger vi effekterne af at indlægge en patient på et psykiatrisk hospital
ved første kontakt med psykiatrien, på patientens videre kontakt og indlæggelse på psykiatriske hospitaler, skade på sig selv/selvmordforsøg, arbejdsmarkedstilknytning, kriminalitet
og på patientens ægtefælles arbejdsmarkedsforhold. Vi tager højde for de fundamentale
VII
forskelle mellem individer, som bliver indlagt, og dem, der ikke bliver, ved at bruge intensiteten af patientkontakter med hospitalet i ugerne op til et individs første kontakt (en
indikator af et specifikt hospitals belægningsgrad) som en instrument variabel. Vi finder, at
indlæggelse har et tvetydigt resultat. På kort sigt hjælper indlæggelse på patientens direkte
behov, til fordel for både patienten og eventuelle ofre af kriminelle handlinger. Indlæggelse
sænker selvpåførte skader såvel som reducerer kriminalitet lige efter indlæggelse. Vi viser,
at reduktionen i kriminalitet er resultatet af fastholdelse/indespærring som følge af hospitalsindlægelsen. På længere sigt viser indlagte individer en højere grad af institutionalisering,
som giver dem lavere arbejdsmarkedstilknytning. Vi identificerer også en stor heterogenitet på tværs af observerbare såvel som uobserverbare karakteristika. Mænd oplever den
største reduktion i kriminalitet, mens kvinder oplever den største stigning i sandsynlighed
for genindlæggelse og den største reduktion i arbejdsmarkedstilknytning. Ved at estimere
Marginal Treatment Effects viser vi, at patienter med de mest alvorlige mentale lidelser oplever markante reduktioner i sandsynligheden for overdoser af alkohol/stoffer såvel som den
største reduktion i kriminalitet. Til sammenligning bliver patienter med de mildeste lidelser
institutionaliseret til en større grad. Afsluttende finder vi yderligere positive eksternaliteter
af hospitalsindlæggelse, idet vi viser, at indlæggelse hæver ægtefællers beskæftigelsesrater.
VIII
Part I
Does Incarceration Length Affect
Labor Market Outcomes?
1
Does Incarceration Length Affect Labor Market Outcomes?
Rasmus Landersø
Abstract
This paper studies how longer incarceration spells affect offenders’ labor market
outcomes, by using a reform that increases incarceration lengths by approximately one
month. I use detailed register data for offenders who predominantly serve incarceration
spells of one to two months. I analyze the sample for several years prior to and after
incarceration and show that the reform led to an exogenous increase in incarceration
length. I find that the longer incarceration spells result in lower unemployment and
higher earnings, possibly because marginal increases in short incarceration spells improve conditions and incentives for rehabilitation, but not the costs of jail related to
these outcomes. I show that the estimates are robust to different econometric specifications and further provide evidence that my results are not driven by changes in
macroeconomic conditions.
Keywords: crime, incarceration length, labor market outcomes.
JEL: K4
Acknowledgements: I thank Marianne Simonsen Helena Skyt Nielsen, Joseph Doyle, Anna Piil Damm,
Christopher Taber, Bas van der Klaauw, Peter Sandholt Jensen, the participants of the 2011 EALE conference, the 2011 American Association of Criminology conference, Dennis Carlton, and an anonymous referee
for useful comments and suggestions. I also thank colleagues Signe Hald Andersen, Peer Skov, and Lars
Højsgaard Andersen for helpful discussions and Linda Kjær Minke for providing data from her study of
Danish jails.
The paper is forthcoming in the Journal of Law and Economics.
2
1
Introduction
As prison populations have risen during the past decades both in the U.S. and elsewhere
(OECD (2010)), so have the benefits from successful rehabilitation of former inmates. Also,
reintegration in the labor market after release from jail is profitable for the offender as well
as society in general, e.g., because it lowers the risk of recidivism (e.g., Fougère et al. (2009);
Witte & Tauchen (1994)). This paper studies the effect of the length of an incarceration
spell on three subsequent labor market outcomes: unemployment rates, dependency on other
public transfers, and earnings.
The previous literature on the effect of imprisonment on subsequent labor market outcomes mainly focuses on the effect of serving a jail sentence relative to not serving a jail
sentence. Yet, policy-makers and judges do not only face choices at the extensive margin on
whether to convict offenders to imprisonment or not. They also face choices at the intensive
margin, as determining the lengths of incarceration. At the intensive margin, the effect of
incarceration length, which is the focus of this paper, will depend on the marginal costs and
benefits of time spent in jail and not the costs and benefits of the jail sentence in total.
The majority of the earlier studies struggle with the endogenous relationship between
crime and labor market outcomes, as offenders with different incarceration lengths differ on
a number of observable and unobservable characteristics. One exception is Kling (2006) who
estimates the average effects of incarceration length on employment and earnings for a wide
range of offenders by using an instrumental variable of randomly assigned judges. I obtain
causal inference by examining the effects of a reform that increased violent offenders’ incarceration lengths by roughly one month, independent of individual offender characteristics.
The effects of incarceration lengths may depend on whether one investigates the effects
of changes in shorter or longer incarceration spells. I.e., the conclusions could rely heavily
on the range of incarceration spells one examined, and estimations including offenders who
3
serve short and long incarceration spells may offset opposing effects. This study extends
Kling (2006) by focussing on offenders who mainly serve incarceration spells of one or two
months, which are modal incarceration spells,1 instead of compiling different offender groups.
I use highly detailed Danish register data to construct a panel of the 1,748 individuals
who were sentenced to jail for crimes subject to the reform, and analyze the sample from
several years before incarceration until three years after release. The sample includes around
20 percent of all men who served time in Danish jails during the period of time in question.
I define the control and treatment group by the date of crime relative to the timing of the
reform. Those who committed crimes prior to the reform are the control group and those
who committed crimes after the reform are the treatment group.
Figure I.1 visualizes the main empirical findings. It shows the averages of the three
outcomes for the treatment and control group, from 48 months prior to incarceration until
36 months following release. I denote the start of the incarceration as time 0, the month
prior to this time −1, and similarly, I denote the first month following release time 1, the
subsequent month time 2, and so forth. All points in time from incarceration initiation to the
date of release have been deleted for all individuals in order to create a coherent time-line.
Figure I.1 shows that unemployment, dependency on other public transfers, and earnings
did not differ systematically between the treatment and control group prior to incarceration,
neither in trends nor in levels.2 Moreover, the figure shows that the two groups’ unemployment rates and earnings diverge after release from jail. The treatment group has lower
average unemployment rates and a higher level of earnings, whereas there are no differences
in dependency on other public transfers. When estimating the effects of the reform, using a
1
The sentences that this paper investigates are comparable to most county jail sentences. The U.S.
Bureau of Justice Statistics estimates that around 1/3 of all U.S. inmates serve time in county jails.
2
The time paths of the unemployment rates and earnings display a spike/dip prior to incarceration. The
spikes/dips could indicate the initiation of a criminal trajectory, while they also display great resemblance
to Ashenfelter’s dip (Ashenfelter (1978)). As noted with regard to effect evaluation in labor economics, the
spikes/dips here could imply self-selection into incarceration. However, as there is no difference between the
treatment and control group’s spikes/dips they do not affect my results.
4
differences-in-differences model and a triple-difference model with property offenders as an
additional control group, I confirm these results. The results are robust to differential trends
by pre-incarceration characteristics and I show that the estimated effects are not caused by
business cycle changes across the timing of the reform. By estimating the average characteristics of those who experienced the largest increase in incarceration length as a result of the
reform, I also find that offenders who are younger and have shorter criminal records than
the full sample are most likely to drive the results.
The findings are in line with the results from Kling (2006) and highlight that offenders
who serve short incarceration spells may incur the costs of going to jail without being able
to benefit from the time spent behind bars. Especially for young offenders, increases in
incarceration length as induced by the reform, improve labor market outcomes with the
improvement in the conditions and incentives for rehabilitation, which may take various
forms. Some may benefit from being constrained to a highly structured life while others
may benefit from couselling, anger-management, transition focussed aid around the before
release, or increase labor force participation as the payoff to crime decreases.
The remainder of the paper is organized as follows: Section 2 provides the background
by introducing the link between incarceration length and subsequent labor market outcomes
and reviewing the previous literature and findings. Section 3 introduces the data and the
sample. Section 4 introduces the econometric framework and Section 5 presents the results
and specification tests. Section 6 concludes.
5
Figure I.1: Average Earnings, Rates of Unemployment, and Dependency on Other Public
Transfers for the Control and Treatment Groups
1800
1
1600
0,9
0,8
1400
0,7
1200
0,6
0,5
Rate
US $, 2005
1000
800
0,4
600
0,3
400
0,2
200
0,1
0
0
-60
-48
-36
-24
-12
0
12
24
36
48
Months
Earnings, control
Unemployment, control
Other public transfers, control
Earnings, treatment
Unemployment, treatment
Other public transfers, treatment
Note: Figure shows monthly earnings, rates of unemployment, and dependency of other public transfers
before and after incarceration (time 0) for the control and treatment (pre- and post reform) groups. For
earnings there were no significant differences the last 48 months leading up to the incarceration spell, except
in one single month (at time -8), for rates of unemployment there were no significant differences between
the two groups the last 48 months prior to incarceration, and for dependency of other public transfers there
were no significant differences the last 30 months prior to incarceration.
6
2
Background
An individual’s labor market outcomes are determined by a wide range of individual skills
and characteristics such as level of human capital, work-experience, level of education (e.g.,
Ben-Porath (1967); Mincer (1974)), social capital (e.g., Granovetter (1995)),3 search behavior
(e.g., Holzer (1988)), and non-cognitive skills (Almlund et al. (2011); Cunha & Heckman
(2008)). On the one hand, these skills may affect the propensity to commit crime and the
type of crime, (cf. Cunha et al. (2010); Lochner (2004); Machin et al. (2011); Moretti &
Lochner (2004)) consequently affecting how much time any given offender serves in jail. On
the other hand, the skills can also change as a result of a jail sentence and the subsequent
time spent behind bars; some skills may erode while other skills may increase and provide
society with benefits in relation to an offender’s labor market outcomes after release from
jail. Moreover, experiencing incarceration may also deter offenders from recidivism (Abrams
(2012); Owens (2009)) and increase their motivation to find employment.
The individual costs of jail can manifest themselves as stigma, job-loss, general informal
sanctions from society, or depreciation of human capital as offenders lose skills and productivity in general or miss out on potential work-experience (e.g., Waldfogel (1994); Western
et al. (2001)). Incarceration spells may also depreciate social capital by eroding personal
connections which match workers to employers or provide information about possible job
opportunities (Sampson & Laub (1995)).
Individual costs of incarceration, in terms of labor market outcomes, may be evaluated
at the extensive margin and at the intensive margin. At the extensive margin, costs include
the penalty from receiving a jail sentence and consequently setting foot in jail, even for just
one second, while at the intensive margin the costs include the effects of marginal increases
in time spent in jail.
3
The economic literature on social capital is more sparse than that on human capital. For an introduction
e.g., Glaeser et al. (2002).
7
The benefits may be increased possibilities for participation in rehabilitating programs
or assistance in job search (a proposition put forward as early as the 19th century by criminologist Arnould Bonneville De Marsangy), academic or vocational training, treatment for
substance abuse (e.g., Kling (2006)), and deterrence in the form of more realistic evaluations
of the pay-off from crime (Freeman (1996); Sah (1991); Wilson & Abrahamse (1992)).
Once an offender has been sentenced to jail, the costs at the extensive margin are sunk.
It then follows that the relationship between marginal costs and marginal benefits composes the maximization problem in relation to labor market outcomes after release from jail.
Where marginal benefits exceed marginal costs the offender would increase his subsequent
labor market affiliation by being imprisoned for a longer period of time. In other words,
disregarding deterrence and incapacitation effects of jail sentences, increasing incarceration
lengths could increase society’s net benefits from an offender’s jail sentence even though the
total costs of incarceration exceed the total benefits.
A vast body of literature investigates the effects of incarceration at the extensive margin
(for notable examples see Aizer & Doyle (2011); Freeman (1992); Grogger (1995); Nagin
& Waldfogel (1995, 1998); Waldfogel (1994); Western et al. (2001)). Most of the studies
find that total individual costs of going to jail or prison are substantially larger than total
individual benefits, and the literature generally ascribes this finding to stigma from the incarceration, as employers who face imperfect information may use criminal records as signals,
revealing otherwise unobserved characteristics. However, these findings do not necessarily
imply that marginal costs exceed marginal benefits, but only that the costs at the extensive
margin are large.
Literature on the effects of incarceration length at the intensive margin is much sparser
than the literature on the effects of incarceration at the extensive margin. Lott (1992a)
estimates a first-difference model on a sample of convicted drug-offenders and finds no significant association between sentencing length and the difference in earnings before and after
8
jail. In contrast, Lott (1992b) finds a significant monetary penalty to offenders convicted of
larceny or theft by as much as a 32 percent reduction in earnings for an additional month
in jail while his corresponding estimates for offenders convicted of embezzlement or fraud
are insignificant. Needles (1996) uses a quasi-experiment of randomly assigned “Transitional
Aids”4 to newly-released prisoners convicted of various types of crime. When examining the
marginal changes in incarceration length while controlling for selection into employment,
she finds no significant effect on earnings. Kling (2006) uses an instrumental variable of
randomly assigned judges as exogenous variation in time incarcerated on a sample of various
types of offenders convicted by the federal judicial system in California.5 He finds no significant effects from incarceration length on neither future employment nor on earnings nine
years after the beginning of the incarceration spell. The study further finds relatively small
positive but significant short-term effects from incarceration length on future employment
and earnings (12 and 30 months after release respectively), using data from the Florida state
prison system together with the Californian sample (Kling does, however, stress that the
lack of exogenous variation in the latter model may bias the estimates). In addition, Kling
(2006) suggests that the results arise because longer incarceration spells might enhance the
possibility of the individual inmates receiving assistance that increases employability once
released, such as treatment for substance abuse.
No matter whether one studies the effects at the extensive or intensive margin, the endogenous nature of crime and labor market outcomes must be addressed. Different incarceration lengths may correlate with unobserved individual characteristics that also affect labor
market outcomes, which could obscure the results and the causal reading of the estimates.
Frameworks such as first difference or fixed effects estimations may obviate time-invariant
unobserved individual characteristics that affect both employability and proneness to crime,
but these frameworks do not eliminate any probable relationships between unobserved time4
A programme designed to help newly-released prisoners rehabilitate, see Needles (1996).
Inmates of federal prisons must have committed a crime defined as ”being within federal jurisdiction”.
Kling mentions ”interstate postal fraud and some drug cases” as examples of such crimes.
5
9
varying components and labor market conditions; for example if layoffs, pay-cuts, etc. prior
to the incarceration spark crime. In such cases, previous levels of labor market outcomes or
shocks will correlate with the length of the subsequent incarceration spell, which means that
simply eliminating the individual fixed effects is insufficient. One solution to this problem of
endogeneity is to implement an instrumental variable, as Kling (2006) does to estimate the
average effects of incarceration length on subsequent earnings and employment for a wide
range of offenders. However, estimates of the effects of incarceration length on subsequent
labor market outcomes may differ across various incarceration lengths and consequently heterogeneous and non-linear effects may offset when averaging treatment effects in samples
of pooled offender types who serve jail sentences of very different lengths. I obtain causal
inference by using a reform that increases incarceration lengths exogenously while I avoid
issues concerning non-linearities by estimating the effect of incarceration length at a more
narrow range of incarceration lengths.
2.1
The Reform of the Penal Code
On the 31st of May 2002 the Danish government and parliament made a change to the penal
code concerning violent crime. It was done by formally issuing an decree to judges saying that
they should increase incarceration lengths by approximately 1/3.6 Further, the maximum
sentences was changed accordingly so the reform would not be ineffective to offenders with
sentences close to the pre-reform maximum sentences. The bill was immediately put into
effect and the aim was explained as follows:
The government finds that the previous level of sanctions in cases of crime harming others
does not adequately reflect the victims’ suffering. Hence, the government wishes to increase
the sanctions for such crimes. [Secretary of Justice Lene Espersen (2002), own translation]
6
Though an internal review (Ministry of Justice, Research Unit (2007)) concluded that the reform did
not increase incarceration lengths by 1/3 but only around 1/6.
10
Thus, the reform targeted violent offenders in general and increased the sanctions for a
given violent crime.
Figure I.2 shows the distributions of incarceration lengths (actual time spent in jail) in
this paper’s sample7 divided by whether the crime was committed prior to or after the
reform.8 Those who committed crime prior to the reform are the control group and those
who committed crime after the reform are the treatment group.
Figure I.2: Pre- and Post-Reform Distributions of Incarceration Length
Note: Figure shows densities of incarceration length measured in days for the control and treatment (preand post reform) groups. P-value for Kolmogorov-Smirnov test for equality of distributions < 0.001. P-value
for a test of differences in means < 0.01.
Both distributions are heavily concentrated in the interval 20 to 70 days, with peaks at 30
and 60 days corresponding to sentences of one and two months of incarceration, respectively.
7
I will introduce the sample formally in section 3.
The figure has been censored at 150 days. The censored data corresponds to 5.26 percent of the sample
prior to the reform and 6.30 after.
8
11
Moreover, the post-reform distribution in general shows fewer sentences in the lower part of
the sentence range and a larger number of sentences at the high end of the range. There seems
to be no noteworthy difference between the tails of the two distributions which might call in
question whether the reform increased the incarceration length for all offenders. However,
as a consequence of the few observations on offenders receiving sentences above 70 days any
non-extreme changes would be undetectable in practice. Also, figure I.2 shows that much of
the increase in average length arose because of increases in incarceration length from one to
two months, for a proportion of the sample, i.e., a substantial proportion of offenders served
two months instead of one month as a result of the reform.
The sample consists of individuals sentenced to jail for ordinary violence (general fights,
bar brawl, minor assaults, etc.).9 The upper panel of figure I.3 shows the fraction that violent crimes in general, ordinary violence, and the sample constituted relative to all crimes10
committed by men aged 18 to 45 between December 2000 and November 2003 which resulted
in convictions to imprisonment. The vertical solid line marks the timing of the reform. In
analogy, the lower panel of figure I.3 shows the fraction of all convictions for violent crimes
and ordinary violence committed by men aged 18 to 45 between December 2000 and November 2003 which resulted in either a suspended sentence or a conviction to imprisonment.
Figure I.1 in the Appendix shows trends in crime convictions by crime type from 1995 until
2009.
The upper panel of figure I.3 shows no change in the proportions of violent crimes or
ordinary violence relative to the aggregated crimes across the timing of the reform. Violent
crimes accounted for approximately half of aggregated crime and ordinary violence was the
most common type of violence as it constituted 50-60 percent of all convictions due to violent
9
For a legal definition of the term see https://www.retsinformation.dk/Forms/R0710.aspx?id=126465. In
everyday terms ordinary violence comprises assaults and fights from which the victim does not suffer major
permanent injuries.
10
In the following paragraph I only consider individuals sentenced as results of violations of the Penal Code.
This includes property crimes, violent crimes, and drug related crimes, but not traffic offences, environmental
offences, or military crimes.
12
Figure I.3: Composition of Crimes from Dec. 2000 to Nov. 2003 for Men Aged 18-45
&ƌĂĐƚŝŽŶŽĨĂůůĐŽŶǀŝĐƚŝŽŶƐƚŽŝŵƉƌŝƐŽŶŵĞŶƚ
ϭ
Ϭ͕ϵ
Ϭ͕ϴ
Ϭ͕ϳ
Ϭ͕ϲ
Ϭ͕ϱ
Ϭ͕ϰ
Ϭ͕ϯ
Ϭ͕Ϯ
Ϭ͕ϭ
Ϭ
ĚĞĐͲϬϬ
ũƵŶͲϬϭ
ĚĞĐͲϬϭ
ũƵŶͲϬϮ
ĚĞĐͲϬϮ
ũƵŶͲϬϯ
DŽŶƚŚŽĨĐƌŝŵĞ
sŝŽůĞŶĐĞ
KƌĚŝŶĂƌǇǀŝŽůĞŶĐĞ
^ĂŵƉůĞ
&ƌĂĐƚŝŽŶŽĨĂůůĐŽŶǀŝĐƚŝŽŶƚŝŽŶƐŽĨǀŝŽůĞŶƚĐƌŝŵĞͬ
ŽƌĚŝŶĂƌǇǀŝŽůĞŶĐĞ
Note: Figure shows the fractions that violent crime, ordinary violence, and the sample constituted of all
suspended sentences or convictions to imprisonment across the timing of the reform (marked by the vertical
solid line) for males aged 18-45 at the time of crime.
ϭ
Ϭ͕ϵ
Ϭ͕ϴ
Ϭ͕ϳ
Ϭ͕ϲ
Ϭ͕ϱ
Ϭ͕ϰ
Ϭ͕ϯ
Ϭ͕Ϯ
Ϭ͕ϭ
Ϭ
ĚĞĐͲϬϬ
ũƵŶͲϬϭ
ĚĞĐͲϬϭ
ũƵŶͲϬϮ
DŽŶƚŚŽĨĐƌŝŵĞ
ĚĞĐͲϬϮ
ũƵŶͲϬϯ
sŝŽůĞŶĐĞ͕ĐŽŶǀŝĐƚŝŽŶƐƵƐƉĞŶĚĞĚƐĞŶƚ͘ŽƌŝŵƉƌŝƐŽŶŵĞŶƚ
sŝŽůĞŶĐĞ͕ĐŽŶǀŝĐƚĞĚƚŽŝŵƉƌŝƐŽŶŵĞŶƚ
KƌĚŝŶĂƌǇǀŝŽůĞŶĐĞ͕ĐŽŶǀŝĐƚŝŽŶƐƵƐƉ͘ƐĞŶƚ͘ŽƌŝŵƉƌŝƐŽŶŵĞŶƚ
KƌĚŝŶĂƌǇǀŝŽůĞŶĐĞ͕ĐŽŶǀŝĐƚĞĚƚŽŝŵƉƌŝƐŽŶŵĞŶƚ
Note: Figure shows the fractions of all convictions that resulted in a suspended sentence or a sentence to
imprisonment for violent crime, ordinary violence, and the sample across the timing of the reform (marked
by the vertical solid line).
13
crimes during the period. In addition, the figure shows that this paper’s sample includes
approximately 20 percent of men aged 18 to 45, who served time in jail during that particular
period of time. Likewise, the lower panel of figure I.3 shows no change in the proportions
of suspended sentences or convictions to imprisonment across the timing of the reform.
Approximately 75-80 percent of all violent crime and ordinary violence resulted in either a
conviction to imprisonment or a suspended sentence. Around 45-50 percent of all violent
crime and ordinary violence resulted in a conviction to imprisonment. In conclusion, figure
I.2 shows that the reform resulted in an increase in incarceration lengths at the intensive
margin, while figure I.3 shows that the reform did not result in changes at the extensive
margin, as it affected neither the types of crime nor to the composition of convictions.
2.2
Imprisonment in Denmark
In Denmark, a sentence to imprisonment is either served in local, open, or closed prisons. The
penal system in Denmark is generally considered quite lenient both in terms of incarceration
lengths and serving conditions (Danish Prison and Probation Service (2012)), in particular
when compared to the United States (Guerino & Sabol (2012); Motivans (2012)). Around
85% of sentencing lengths in Denmark are below one year and only 7% are longer than two
years (Danish Prison and Probation Service (2012)) which, in terms of time in jail, makes
U.S. county jails the best suited comparison.
Only offenders with the longest prison sentences or gang affiliation serve in closed prisons,
which have more staff and control than open prisons and stricter rules about e.g. money,
telephone calls, visits, and other matters. The stark differences between the modal sentencing
lengths in Denmark and the U.S. partly stem from differences in the frequency of ’severe
crime’. However, they also reflect that the general view towards criminal sactions differs. The
most common form of imprisonment in Denmark is in open state prisons which, according
to the Danish Prison and Probation Service, reflect the particular view that closed prisons
14
often institutionalize and brutalize offenders compared to open prisons.11 The open prisons
seek to mimic a highly structured everyday life, where the inmates have mandatory chores
such as manual or vocational labor and also cook their own meals. The prisons also provide
possibilities of various lower secondary and vocational educations, in addition to programs
such as anger-management and treatment for substance abuse.
Traditionally, rehabilitation and counseling has been focussed on offenders who served
long incarceration spells. In addition, there were no official guidelines for Danish jails on e.g.
rehabilitating and work release programs for short sentences until 2006. Beyond anecdotal
evidence, little is known of in-jail rehabilitation for offenders who only served one or two
months in jail prior to 2006.12 Minke (2010) presents the most thorough documentation of
the inmates’ conditions in Denmark through her survey from 2007-2009 (see Minke (2010)
for information on the survey). Table I.1 in the shows the reported rates of participation in
rehabilitation programs across time spent in jail using data from this survey.
Table I.1: Participation Rates, In-Jail Rehabilitation
Time spent in jail
Participation rates
Less than 1 month
0.202
Between 1 and 2 months
0.244
Between 2 and 3 months
0.414
Between 3 and 6 months
0.500
More than 6 months
0.534
Observations
109
41
29
72
442
Note: Table shows fraction of inmates who report that they had participated
in rehabilitation programs while incarcerated by time spent in jail.
Rehabilitation programs include: Treatment for drug or alcohol abuse,
anger management therapy, cognitive behavior therapy.
Based on data from Minke (2010). The data stem from surveys of
inmates in 12 of the 16 jails in Denmark. The surveys were conducted
between 2007 and 2009.
The table shows that participation rates in rehabilitating programs increase in incarcer11
http://www.kriminalforsorgen.dk/Default.aspx?ID=1256, (accessed 04/11-2014)
After 2006, all incarcerated offenders are entitled to an interview with a case officer at the time of
admission into jail. The Danish Jail and Probation Service cannot specify the content of the admission
interviews, except that the “incarceration lengths obviously limit the type of in-jail rehabilitation that can
be put into effect.” Nevertheless, Minke (2010), which to my knowledge is the only coherent analysis of
rehabilitation possibilities in Danish jails, finds that rehabilitation posibilities during short incarceration
spells are very limited, even if the inmates themselves request treatment, assistance or training.
12
15
ation length. Around 20 % of the survey participants who have been incarcerated for less
than one month and more than half the survey participants who have been incarcerated for
three or more months have participated in rehabilitating programs.
Finally, the absence of official guidelines prior to 2006 suggests that the offenders who
committed crime prior to the reform experienced similar conditions as those who committed
crime after the reform.
3
Data
This paper13 uses full population register data from Statistics Denmark14 on criminal records, education, earnings, age, gender, ethnicity, marital status, and children, along with
information on recipients of public transfers from the DREAM database.15 The DREAM
database contains weekly information on all recipients of public transfers in Denmark along
with a specification on type of public transfer (unemployment benefits, social assistance,
public pensions, etc.). The various information are linked by an individual-specific social
security number. The criminal registers include a unique case-specific code, verdict (guilty,
acquitted), sentence type (imprisonment, suspended sentence, fine, warning, detainment),
date of crime, type of crime, incarceration date, release date, type of incarceration (e.g.,
remand, serving term of imprisonment, etc.).
As the frequency of violent crime decreases with age and the majority of crimes are
committed by men, I only include men who were aged 45 or younger at the date of the
13
See Appendix B for a detailed description of the construction of data.
Only Danish residents are included in the registers.
15
A supplementary register used in the Danish Rational Economic Agent Model (DREAM), an
general equilibrium model used for forecasting. The database contains information on every Danish citizen who has received public benefits/transfers of any kind.
For further information see:
http://www.dst.dk/upload/microsoft word - beskrivelse af dream koder - version 22.pdf.
14
16
crime,16 in order to ensure homogeneity between the individuals in the sample. As special
conditions apply for individuals below the age of 18, I only include adults of 18 or above.
The data are available for several years prior to and after incarceration. Hence, I create
a panel with one time series per individual per case. Since individuals in the sample served
their specific jail sentence at different points in time, I create a separate time-line that does
not include the time a given individual spent in jail, but measures the time to/from the
start/end of incarceration for all individuals. Hence, -1 denotes the last observation before
the beginning of the incarceration spell and 1 denotes the first observation after release.
The sample consists of individuals incarcerated as a consequence of ordinary violence
committed within a period of 18 months on each side of the reform, i.e., between December
2000 and November 2003. I only use offenders convicted of ordinary violence in order to
obtain a sufficiently large homogenous sample, with respect to both incarceration length and
observable characteristics. The time-span is chosen to reach a sample size that on the one
hand reduces random variation, and on the other hand minimizes the differences between
the earlier and later parts of the sample caused by changing demographics and business
cycles. The group that committed crimes before the reform is the control group and the
opposite group is the treatment group. No individual in the sample experienced more than
one incarceration for ordinary violence during the time span considered in this paper.17
The resulting panel is perfectly balanced with a final sample size of 1,748 individuals,
875 belonging to the control group and 873 belonging to the treatment group. Importantly,
though one and two months are the modal incarceration lengths, the sample is not restricted
16
Women and individuals aged 46 or older at the time of the crime made up 3.7% of the sample at this
point.
17
I exclude the individuals who are not included in data the for at least 12 months prior to the incarceration
in focus. This applies to 9 individuals, 5 and 4 individuals from the treatment and control groups, respectively.
Additionally, some individuals e.g., emigrated or died during the three years after release. I exclude these
from the sample. This censoring applies to 43 and 40 persons from the treatment and control groups
respectively (2.5 and 2.2 percent of the final sample). The estimation results, with various imputations for
the attrites’ missing periods instead of the above mentioned censoring, do not differ qualitatively from the
results presented throughout the paper. The auxiliary estimation results can be obtained from the author
on request.
17
by incarceration length. Limiting the sample by a endogenous variable would likely bias
the results. Hence, the paper uses all individuals who were convicted of ordinary violence
committed on each side of the reform.
This study focuses on three outcomes: unemployment rates, dependency on other public
transfers (e.g. pensions, support for education and skills-upgrades, labor market programs),
and earnings (gross earnings excluding public transfers). The residual of unemployment
and dependency on other public transfers is employment and self-sufficiency. The sum of
unemployment and dependency of other public transfers constitute all public transfers. Thus,
a reduction to one which is not offset by an increase to the other implies an increase to
employment.
I use the weekly observations of public transfers from the DREAM database to compute
monthly rates of unemployment and dependency on other public transfers. I then combine
this information with information on income, to obtain monthly observations of earnings.
Table I.2 shows means and standard deviations of the three outcome variables along with
observable characteristics. The pre-incarceration outcomes and socio-economic characteristics are measured 12 months prior to the incarceration and indicators of previous criminal
history are measured at the time of incarceration. The table also shows means divided by
treatment status, in order to investigate whether the reform was unrelated to the two groups’
observed characteristics prior to incarceration, and a random draw of the full male population
in 2002 with similar age distribution as main sample of ordinary violence offenders.
The table shows that the individuals in the sample suffered from high rates of unemployment, dependency on other public transfers, and low earnings compared to their average
equal aged peers. Average monthly earnings were $ 1,473 (monetary units have been transformed using the 2005 exchange rate of DKK 6,003.37 to USD 1,000).18 Further, sizable
proportions of the sample - 33 and 15 percent, respectively - were unemployed or depend18
As reported by the Central Bank of Denmark: http://nationalbanken.dk/DNDK/statistik.nsf/side/
Faerdige tabeller - Valutakurser!OpenDocument (accessed 11/03-2011).
18
Table I.2: Summary Statistics by Treatment Status
Full sample
Variable
Measured 12 months prior to incarceration
Unemployed
Dependent on other public transfers
Earnings (USD 2005)
Age
Married
Cohabitant
Have children
Non-western immigrants or descendants
No job-qualifying education
Vocational or skilled
Upper secondary or higher
Convicted before
Convicted of a violent crime before
Convicted of a property crime before
Months since 1st date of crime leading to an indictment
Months since 1st date of crime leading to an conviction
Months since 1st incarceration
Number of previous convictions
N
Control
Treatment
Significant Random
difference weighted
sample
0.33
0.33
0.33
0.05
(0.46)
(0.46)
(0.45)
(0.21)
0.15
0.15
0.15
0.15
(0.48)
(0.35)
(0.34)
(0.36)
1,473
1,510
1,417
2,993
(1,922)
(1,980)
(1,862)
(2,567)
28.13
28.40
27.86
28.61
(7.80)
(7.83)
(7.76)
0.23
0.26
0.20
(0.42)
(0.44)
(0.40)
(7.70)
∗∗∗
0.26
(0.44)
0.28
0.28
0.27
0.45
(0.45)
(0.45)
(0.44)
(0.50)
0.36
0.38
0.34
(0.48)
(0.49)
(0.48)
∗
0.34
(0.47)
0.12
0.11
0.13
0.07
(0.48)
(0.32)
(0.34)
(0.25)
0.67
0.68
0.67
0.51
(0.47)
(0.47)
(0.47)
(0.50)
0.23
0.23
0.23
0.31
(0.42)
(0.42)
(0.42)
(0.46)
0.10
0.09
0.10
0.18
(0.30)
(0.30)
(0.30)
(0.39)
0.83
0.83
0.83
0.21
(0.37)
(0.37)
(0.37)
(0.41)
0.48
0.50
0.47
0.04
(0.50)
(0.50)
(0.50)
(0.20)
0.67
0.67
0.66
0.15
(0.47)
(0.47)
(0.48)
(0.36)
109
110
108
(83)
(81)
(84)
98
99
97
(84)
(82)
(85)
46
47
44
(73)
(71)
(75)
4.44
4.45
4.43
(5.89)
(5.62)
(6.15)
1,748
875
873
33,248
Note: Table shows summary statistics for the full sample and divided by treatment status. T-test for mean differences in
mean sample by treatment status: + p < 0.10, ∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001
Random sample has been drawn from the full Danish population in 2002 with similar age distribution as main sample (here
labelled Full sample).
Significant difference indicate significant difference in means between the control and treatment groups.
19
ent on other public transfers 12 months prior to incarceration. There were no significant
differences in any of the outcome variables 12 months prior to incarceration.
The table also shows that the sample had a low level of resources as measured by socioeconomic variables, as the majority had no education beyond secondary school and few
were married or cohabiting. On average the offenders committed the first crime for which
they were charged 109 months prior to the incarceration, they had committed their first
crime for which they were convicted at 98 months prior to the incarceration, and 18 percent
of these crimes were violent. In addition, they experienced their first incarceration at 46
months prior to the incarceration, and more than 80 percent had received a conviction prior
to the one studied in this paper. 43 percent had been convicted of a violent crime, whereas
64 percent had received convictions for a property crime. Finally, the average individual
in the sample had more than four convictions prior to the one in question. The table also
shows a significantly higher proportion of married individuals in the control group and a
lower proportion of individuals with children in the treatment group. Beyond these two
covariates, the table shows no other significant differences between the two groups.
The use of a reform as identification also rests on the assumption that the pre-reform and
post-reform groups were subject to equal trends. Therefore, I also need to consider potential
macro-level differences across the reform. Denmark experienced a small recession that began
in late 2001 and ended at the beginning of 2004. The recession was followed by a boom that
lasted for the remaining part of the data period covered by this paper. However, figure I.1
indicates that the labor market outcomes for the two groups prior to their incarceration were
not affected by the business cycles. Also, the official policies on the transition from life in jail
to life outside did not change during the period of time covered by this paper. Hence, the
two groups most likely faced the same general conditions on the labor market before their
incarceration spells and there is little or no sign of any change in the average characteristics
of the “violent offender” across the reform, nor any sign of a difference between the two
20
groups as a result of macroeconomic trends. Consequently, the reform most likely provided
an exogenous increase in incarceration lengths.
4
Econometric Framework
This paper evaluates the effect of a treatment on subsequent labor market outcomes. I define
treatment as being incarcerated under the post-reform guidelines. I assess this treatment
effect by following the terminology first introduced by Rosenbaum & Rubin (1983); Rubin
(1974), and adopted by the general treatment literature, and define the treatment effect on
the treated conditional on observable characteristics as:
δAT T = E (δ | Di = 1) = E (yi (1) | xi , Di = 1) − E (yi (0) | xi , Di = 1)
(1)
where Di is a binary treatment indicator equal to 1 if individual i receives treatment and
0 otherwise. yi (1) denotes the outcome for individual i if i is sentenced under the postreform guidelines and yi (0) is the outcome if i is sentenced under the pre-reform guidelines,
and xi is a set of observable characteristics. The estimate of δAT T expresses the difference
between the expected outcomes for individual i if he is sentenced to incarceration under
the post-reform guidelines rather than the pre-reform guidelines, under the condition that
he would be incarcerated under the post-reform guidelines. Obviously, in reality I cannot
observe individual i in both states at the same point in time.
In order to reduce the volatility of the labor market outcomes I use the weekly observation of public transfers from the DREAM and income data to compute 6 months rates
of unemployment, dependency on other public transfers, and earnings. I denote every 6
month period since release period s. Moreover, imposing a parametric form on the relationship between the outcome yi , the observable characteristics xi , the reform Di , and the
unobserved components over time (defined as periods of six months), I express this as:
21
yis = βxis + δDi + ai + eis
(2)
where yis is a given labor market outcome for individual i in period s > 0 (that is, period
s after the incarceration), xis is a set of observable characteristics, ai is an unobserved fixed
effect, and eis is an unobserved idiosyncratic error. δ is the parameter of interest, i.e., the
effect on y of the increase in incarceration length induced by the reform. By differencing
equation (2) with pre-incarceration characteristics (one year prior to the beginning of the
incarceration spell) I define ∆yis = yis − yi,−1year , ∆xis = xis − xi,−1year , ∆eis = eis − ei,−1year .
Keeping in mind that Di is a dummy indicator of the treatment that I seek to evaluate
over several periods from time of release s, the panel structure of the data allows me to pool
every period s = 1, ..., 6 (i.e., the first three years after release) and I obtain the differencesin-differences (DD)19 model:
∆yis = β∆xis +
s=6
X
γs ds +
s=2
s=6
X
δsDD Di + ∆eis
(3)
s=1
where β is a vector measuring the effects of the co-variates,20 and ds is an indicator of
the time since release equal to 1 if period = s and 0 otherwise. γs captures the pre-reform
group’s (control group’s) labor market trends after release from jail while δsDD captures the
difference between the control and treatment group in each of the six month periods since
release. Hence, δsDD captures the effect of the reform.
In order to obtain consistent results, none of the terms I include in equation (3) may
correlate with the unobserved components. Figure I.1 and table I.2 showed that neither the
magnitude of the dip nor the trends and levels of the outcome variables prior to incarceration
19
Here, differences-in-differences imply the difference between the pre- and post-incarceration outcomes of
the post-reform offenders relative to the difference between the pre- and post-incarceration outcomes of the
pre-reform offenders.
20
∆x includes a constant term, changes in marital status, changes in children, three indicators of changes
in education status, and changes in area of residence.
22
differed significantly across the two groups, and the reform provided an exogenous shift in
incarceration lengths (so Di is orthogonal to the unobserved factors embedded in the time
invariant ai and the idiosyncratic error eis ). If prior and recent levels of characteristics xi·
are independent of the idiosyncratic error ei· while the reform provides an exogenous shift in
incarceration lengths I can estimate the parameters consistently by OLS . As the observable
differences between the two groups are negligible, it seems reasonable to assume that there
are no fundamental differences between the unobserved characteristics of the two groups.21
However, the estimation of δsDD also relies on the assumption that the reform did not
coincide with changes in labor market conditions. In such a case the pre- and post-reform
groups would be subject to different macroeconomic trends after release from jail, which
would - wrongfully - be interpreted as effects of the reform. In order to eliminate any
macroeconomic trends that may bias the DD estimates I also estimate the effect of the
reform by a triple-differences (DDD) model using offenders of property crimes (who were not
subject to any reforms and did not experience any changes to the length of their incarceration
spells) as additional controls. Hence, the triple-differences model allows me to eliminate any
differences in labor market outcomes between the control and treatment group that were
not a result of the reform. Appendix B (online appendix) describes the construction of the
auxiliary sample. Let Vi be a binary indicator equal to 1 if i belongs to the main sample of
violent offenders and equal to 0 if i belongs to the auxiliary sample of property offenders:
∆yis = β∆xis +
s=6
X
s=2
µs ds +
s=6
X
γs ds · Vi +
s=1
s=6
X
s=1
21
ρs D i +
s=6
X
δsDDD Di · Vi + ∆eis
(4)
s=1
Using the reform as an instrumental variable is an alternative estimation strategy relying on similar
assumptions. If an IV strategy was employed instead, the DD estimates would be normalized by a first
stage regression. The DD estimates should be divided by the mean increase as result of the reform if the
treatment variable was measured in days of incarceration. This would result in smaller estimates than I
obtain with the differences-in-differences strategy. The DD estimates should be rescaled by the increase in
the fraction treated, if the treatment variable was defined as a dummy variable of experiencing incarceration
below or above a threshold (e.g. 35 days see table IA.5). This would result in larger estimates than I obtain
with the differences-in-differences strategy.
23
Here µs captures the property offenders’ pre-reform labor market trends after release
from jail, γs captures the violent offenders’ pre-reform labor market trends, ρs captures the
property offenders’ post reform groups labor market trends, and δsDDD captures the DDD
estimates of the reform. The effect of the reform will be estimated consistently by OLS if
prior and recent levels of characteristics xi· are independent of the idiosyncratic error term
ei· and if the property offenders’ pre-reform to post-reform change in labor market outcomes
equals that of the ordinary violence offenders, had these not been subject to the reform.
Furthermore, as noted by Bertrand et al. (2004), differences-in-differences estimates often
yield underestimated standard errors, as ordinary standard errors fail to take account of serial
correlation often observed in relation to labor market outcomes, e.g. between unemployment
rates from on period to the next. Therefore, I bootstrap the standard errors by blocks,
drawing all observations for each individual instead of single observations, and implement
a wild bootstrap procedure that introduce the variance to the estimates which otherwise
would be too low.22
5
Results
The following section presents the results of the differences-in-differences and triple-differences
estimations of the effect of the reform. In addition, the section will also introduce robustness
checks of the estimated effects.
For unemployment rates and dependency on other public transfers the parameter estimates are effects in percentage points, as the two variables are measured in percentages. A
parameter estimate of e.g., -0.055 at 7-12 months after release from jail, as seen in column
1 of table I.3, implies that those who committed crime after the reform experienced 0.055
percentage points lower unemployment rates during those six months when compared to
22
The wild bootstrap randomly assigns extra noise to the estimates. As proposed
n by Davidson & Flachaire
with probability 0.5
(2008); Flachaire (2005), I multiply each estimated error ∆eis with ρis = −1
, so
1 with probability 0.5
E (ρis ) = 0 and σρ2 = 1.
24
individuals who committed crime prior to the reform. For earnings, the parameter estimates
corresponds to a change in monthly earnings in 2005 USD.23 Hence, a parameter estimate
of 150.99 at 7-12 months after release from jail, as seen in column 5 of table I.3, corresponds
likewise to an increase in earnings of 150.99 USD during the six months in question.
Table I.3 shows the estimated effects of the reform (δs ) for the first three years after
release for each of the three outcomes, together with block-bootstrapped standard errors
of the estimates in parentheses. The columns labelled DD show the estimates from the
differences-in-differences model as specified in equation (3) and the columns labelled DDD
show the estimates from the triple-differences model as specified in equation (4).
Table I.3: Main Estimation Results
Periods
1-6 months after release
7-12 months after release
13-18 months after release
19-24 months after release
25-30 months after release
31-36 months after release
R2
N
Wald statistic (p-val)
Unemployment
(1)
DD
-0.033*
(2)
DDD
-0.105***
Dep. on other
transfers
(3)
(4)
DD
DDD
0.005 0.044
Earnings
(0.019)
(0.039)
(0.014)
(0.029)
-0.055***
-0.129***
0.005
0.009
150.99**
(0.021)
(0.043)
(0.015)
(0.033)
(76.16)
(122.52)
-0.067***
-0.121***
0.04
0.007
126.84
130.85
(0.020)
(0.043)
(0.016)
(0.033)
(77.74)
(133.53)
-0.071***
-0.132***
0.004
-0.014
255.53***
303.50**
(0.021)
(0.039)
(0.017)
(0.032)
(82.18)
(138.38)
205.19
(5)
DD
87.49
(6)
DDD
147.45
(63.00)
(113.93)
171.75
-0.076***
-0.074*
0.007
-0.024
236.04***
(0.021)
(0.043)
(0.018)
(0.034)
(87.39)
(152.65)
-0.096***
-0.068
-0.001
0.010
393.04***
219.33
(0.020)
(0.044)
(0.019)
(0.038)
(86.35)
(166.58)
0.023
0.025
1,748
2,388
<0.001*** <0.001***
0.008
1,748
0.998
0.014
2,388
0.801
0.023
0.021
1,748
2,388
<0.001*** 0.044**
Significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows DD and DDD regression results for unemployment rates, dependency of other
public transfers, and earnings the first 36 months after release from jail.
The block-bootstrapped standard errors are reported in parentheses below the estimates
23
Though it is customary, I do not use log earnings because a large proportion of the sample experience
longer periods with full unemployment. For unemployed individuals, earnings are equal to zero by definition.
Table IA.1 in the online appendix shows the estimates using log earnings by replacing earnings equal to zero
with one. The DD estimates do not differ qualitatively from those shown by table I.3 though the DDD
estimates are very noisy with large standard errors.
25
Column 1 and 2 show the estimated effect of the reform on unemployment for the first
three years after release. All of the DD estimates are negative and, except for the first six
months after release, significant at a one percent significance level. The sizes of the estimates
indicate that the reform induced a drop in the unemployment rate of approximately 4-5
percentage points. As time since release increases, so does the numerical size of the estimates,
to a level of roughly 7 to 10 percentage points two years after release. The DDD estimates
are also negative. However, they are numerically largest in the first two years after release
from jail, with estimates around 10 percentage points. The estimates decrease somewhat
two years after release both in size and significance and are insignificant three years after
release. The table suggests that the reform has resulted in lower unemployment rates, but
is ambiguous as to whether the effect increases or decreases in size with time since release.
Moreover, the estimates appear to be volatile with large standard errors.
Column 3 and 4 show the estimated effects of the reform on dependency on other public transfers the first three years after release. The table shows that most of the estimates
are positive, but all numerically small and insignificant even at a ten percent level. The
estimates are not significant when tested jointly either. Furthermore, the insignificant estimates of dependency on other public transfers show that there was no substitution between
unemployment and other public transfers.24 This finding implies that the change in incar24
In order to investigate the possibility of opposing effects within the composite measure of dependency
on other public transfers, I have estimated the model with a subdivision of this outcome into two general
categories: first, voluntary efforts revealing an interest in (re-)entering the labor market at some point, e.g.,
financial support for education, financial aid for upgrading work-oriented skills, specific voluntary labor market programs; and second, mandatory programs required in order to be eligible for the receipt of benefits or
passive support without any requirements, such as sick leave, early retirement relating to lack of employability, etc. None of the benefits included in the second group are aimed at obtaining future employment on the
labor market. The first outcome category was unaffected by the reform, while there was a weak sign of an
increase in the second category as a consequence of the reform. However, this result was neither sufficiently
robust nor significant on a sufficient level for any conclusions to be drawn.
Additionally, I have estimated the model with total dependency on public transfers (the sum of unemployment and dependency on other public transfers). The results using this outcome did not change any
conclusions, as they were not significantly different from those with rate of unemployment as an outcome.
Hence, I conclude that the results are not caused by a substitution effect.
26
ceration length following the reform increased employment for the sample, as the reduction
to unemployment is not offset by an increase in other types of public dependency.
Column 5 and 6 show the estimated effect of the reform on earnings for the first three
years after release. The DD estimates show no effect of the reform on subsequent earnings
during the first six months after release, but the estimated effect increases with time since
release and, except for the time between 1-6 months and 13-18 months after release, it is
highly significant. The estimates show a positive and significant effect of the reform of more
than $ 300 per month, three years after release from jail. The DDD estimates do not differ
in sign from the DD estimates. All DDD estimates are positive but generally the standard
errors of the DDD estimates are much larger than those of the DD estimates. Only one
of the DDD estimates is significant at a five percent level, while the estimates are jointly
significant at a five percent level. The results suggest that the reform was associated with an
increase in earnings. The data do not allow me to determine whether the earnings increases
appear due to higher levels of productivity or lower levels of unemployment. However, since
table I.3 also shows that unemployment decreased for the treated, resulting in a greater
number of individuals with none-zero earnings, I suspect this to be the dominant factor.
A possible source of bias is different trends according to pre-treatment characteristics,
e.g., if offenders with children experience different labor market trajectories. Table I.4
presents the estimation results, while allowing for different trends according to observable
pre-incarceration characteristics. The columns labelled DD show the estimates from the
differences-in-differences model and the columns labelled DDD show the estimates from the
triple-differences model. Column 1 and 2 of the table show the estimated effect of the reform
on unemployment, column 3 and 4 show the estimated effects of the reform on dependency
on other public transfers, and column 5 and 6 show the estimated effect of the reform on
earnings the first three years after release.
The table shows that the estimates from table I.3 are robust to differences in trends
27
Table I.4: Estimation Results, Different Trends
Periods
Unemployment
(2)
DDD
-0.104***
Dep. on other
transfers
(3)
(4)
DD
DDD
0.005 0.043
Earnings
(5)
DD
87.49
1-6 months after release
(1)
DD
-0.037*
(0.019)
(0.040)
(0.014)
(0.028)
(47.80)
(115.72)
7-12 months after release
-0.060***
-0.128***
0.005
0.009
150.99**
174.95
(0.021)
(0.042)
(0.015)
(0.032)
(90.56)
(124.69)
132.30
13-18 months after release
19-24 months after release
25-30 months after release
31-36 months after release
R2
N
Wald statistic (p-val)
-0.072***
-0.122***
0.04
0.007
126.84
(0.020)
(0.041)
(0.016)
(0.033)
-0.075***
-0.134***
0.004
-0.014
(0.021)
(0.039)
(0.017)
(0.033)
-0.080***
-0.075*
0.007
-0.026
(0.021)
(0.042)
(0.018)
(0.036)
-0.100***
-0.067
-0.001
0.009
(0.020)
(0.043)
(0.019)
(0.038)
(107.99)
255.53***
(109.21)
236.04***
(156.17)
393.04***
(260.28)
0.027
0.033
1,748
2,388
<0.001*** <0.001***
0.009
1,748
0.999
0.015
2,388
0.775
(6)
DDD
149.93
(137.20)
307.99**
(144.60)
210.44
(154.61)
223.60
(164.27)
0.032
0.033
1,748
2,388
<0.001*** 0.043**
Significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows DD and DDD regression results for unemployment rates, dependency of other public
transfers, and earnings the first 36 months after release from jail with different trends for
pre-incarceration characteristics: dummies for completed any education beyond secondary school,
completed any qualifying education, maritial and cohabiting status, and parental status.
The block-bootstrapped standard errors are reported in parentheses below the estimates
according to pre-treatment characteristics, as none of the estimates shown in table I.4 differ
much from the estimates shown in table I.3. The estimates on unemployment are negative
and highly significant, the estimates on dependency on other public transfers are insignificant,
and the estimates on earnings are positive and jointly significant.
A different source of bias could arise as the timeline on the one hand is defined relative to
the date of release while the reform on the other hand changes the incarceration length and
hence the dates of release for the treatment group. If, for example, the reform lead to surge
in summer releases, relative to the pre reform period, then the estimated reform effects could
include both seasonal differences in unemployment rates as well as the prolonged incarceration effect. However, computing the treatment effect based on the start of incarceration will
28
eliminate any seasonal differences between the treatment and control group that are caused
by changes to release dates rather than the actual changes to incarceration lengths.
Table IA.225 shows the DD and DDD estimation results when evaluating unemployment
rates from the date of incarceration and not from the day of release, setting all in-prison
unemployment rates to 0, 1, or the last observed unemployment rate before incarceration,
respectively. Generally, the results do not differ in sign, size or significance level compared
to the main estimation results from table I.3. In similar vein, longer incarceration spells
will also postpone future earnings after release. Table IA.326 shows the DD and DDD
estimation results for earnings discounted relative the incarceration length using an annual
discount rate of 0.04, in order to investigate whether the effects of the reform on the present
value of earnings differ from the overall effect on earnings. The estimation results from table
IA.3 do not differ qualitatively from those of table I.3.
5.1
Macroeconomic Trends
In the following, I restrict the sample such that I only include persons who committed crime
4 months prior to or after the implementation of the reform27 (rather than 18 months).28
I do this to investigate whether macro-level changes affected the main results. The shorter
time-span reduces the sample size to 351 for the differences-in-differences estimation and
484 for the triple-differences. The reduced sample size may affect significance levels but not
signs or sizes of the estimates from table I.3, if these are robust.
Table I.5 shows the estimated effect of the reform for the three outcomes using the reduced
sample(s) (corresponding to table I.3), together with the standard errors of the estimates.
25
In the appendix.
In the appendix.
27
Table IA.4 shows balancing tests for this restricted sample.
28
I have also performed this robustness check with persons sentenced to imprisonment for a crime committed 2, 3, 5, 6, 7, 8, and 9 months prior to or after the implementation of the reform. The results can be
obtained from the author on request.
26
29
Table I.5: Estimation Results, Reduced Sample
Periods
1-6 months after release
(1)
DD
-0.046
(2)
DDD
-0.146*
Dep. on other
transfers
(3)
(4)
DD
DDD
0.031 0.062
(0.043)
(0.086)
(0.033)
(0.064)
(138.82)
(253.71)
7-12 months after release
-0.092**
-0.144
0.044
0.112
238.51
231.10
(0.045)
(0.092)
(0.034)
(0.070)
(159.44)
(278.80)
13-18 months after release
19-24 months after release
25-30 months after release
31-36 months after release
R2
N
Wald statistic (p-val)
Unemployment
Earnings
(5)
DD
51.54
(6)
DDD
145.87
-0.128*** -0.190*
0.023
0.007
287.15
229.77
(0.044)
(0.105)
(0.038)
(0.077)
(150.25)
(287.04)
-0.059
-0.181*
0.004
0.005
205.50
170.64
(0.047)
(0.102)
(0.041)
(0.081)
(166.92)
(312.15)
-0.040
-0.015
0.013
-0.076
-17.75
66.98
(0.050)
(0.102)
(0.043)
(0.087)
(187.67)
(330.36)
-0.034
-0.032
0.014
0.026
95.16
90.28
(0.046)
(0.099)
(0.042)
(0.089)
(174.60)
(349.71)
0.031
351
0.020**
0.043
484
0.047**
0.013
351
0.832
0.043
351
0.250
0.041
484
0.914
0.021
484
0.608
Significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows estimation results where the sample has been narrowed to +-4 months around
the reform. The block-bootstrapped standard errors are reported in parentheses below the estimates
Column 1 and 2 show the estimated effects of the reform on subsequent unemployment.
The size of the estimated effects in the short run increases in comparison to the original
estimates from table I.3. However, the volatility of the estimates also increases as the span
narrows. Hence, the table offers no definitive guidance as to the exact size of the effect of the
reform, as the estimates from table I.3 are well within any conventional confidence intervals.
Column 3 and 4 show the estimates with dependency on other public transfers as outcome.
There are some differences between the two columns the original estimates in column 3 and
4 of table I.3. The numerical size of the estimates increases somewhat compared to the
full-sample estimates, especially for one specific DDD estimate. Yet, none of the estimates
are close to being significant, neither when tested alone nor jointly.29 Column 5 and 6 show
29
Again, I have estimated the model using total dependency on public transfers. The results were not
significantly different from those for unemployment. Therefore, they suggest that the rate of unemployment
dropped as a consequence of the reform, while there was no attrition from the labor market, as the reform
did not affect dependency on other public transfers.
30
the estimates with earnings as outcome. Comparing the estimates to those from column 5
and 6 of table I.3 the estimates for the first two years after release have similar sign and
size, while the remaining reduced sample estimates diverge from the full sample estimates.
Also, the estimates from the reduced sample the standard errors increase as the sample is
reduced.
Overall, the estimated parameters of the effect on the unemployment rate and dependency
of other public transfers appeared robust to the reduction in sample size and the significant
reduction of the unemployment rates appears robust as it shifted in the opposite direction of
the probable macro-trend bias. Still, there is little evidence as to whether the shorter time
span affected the estimates for earnings as the sample size reduction more than doubled the
standard errors.
To confirm the findings for unemployment and elucidate the effect on earnings, I define a
series of placebo-reforms for each month from November 1999 to November 2004 and test for
joint significance related to the effects on unemployment and earnings. Around each placeboreform I have constructed a new sample as described in section 3, including individuals who
committed crimes within an 18 month span on each side of the placebo-reform.30 Figure I.4
shows the p-value for a Wald-test for joint significance for the estimated effect of the placeboreforms from the DDD model31 with unemployment and earnings as outcomes, respectively.
If the reform is the causal catalyst driving the estimates, the placebo-reform-samples before
January 2001 and after December 2003 should be insignificant as the 18 month span on each
side does not coincide with the true timing of the reform at June 2002. Between January
2001 and December 2003, the estimation samples will increasingly coincide with the true
30
The sample size of each placebo-reform is approximately equal to the sample size of the main sample
constructed around the actual reform. The individual placebo-control groups and placebo-treatment groups
are also approximately of equal size.
31
I have also estimated the effects of the placebo-reform for the DD model. The results and overall pattern
do not differ qualitatively form DDD results reported in figure I.4. The DD placebo results can be obtained
from the author on request.
31
timing of the reform as the timing moves towards the vertical line at June 2002. I.e., the
placebo-reforms should increase in significance as the gap to June 2002 closes from each side.
Figure I.4: Significance Level for Joint Tests of Placebo-Reforms
Level of significance (p-value)
1
0.1
0.05
Nov-04
Jul-04
Sep-04
Mar-04
May-04
Jan-04
Nov-03
Jul-03
Sep-03
May-03
Jan-03
Mar-03
Nov-02
Sep-02
Jul-02
May-02
Jan-02
Mar-02
Nov-01
Jul-01
Sep-01
Mar-01
May-01
Jan-01
Nov-00
Sep-00
Jul-00
May-00
Jan-00
Mar-00
Nov-99
0
Timing of pseudo-reform
Earnings
Unemployment
Note: Figure shows p-values for pseudo-reforms before and after the actual timing of the reform. The vertical
dashed line marks the time of the reform. The data for each placebo-reform includes crimes convicted 18
months prior to and 18 months after the given placebo-reform. Hence, “treatment” and “control” groups of
placebo-reforms between January 2001 and December 2003 will coincide with the true timing of the reform
in June 2002 to greater or lesser extent.
The figure shows insignificant effects on earnings and unemployment for all sets of placeboreforms that do not include June 2002. As the timing of the placebo-reforms approaches the
timing of the real reform, from the left and from the right, the levels of significance increase
for both models. Only placebo-reforms where around half or more of the placebo-reform
data coincide with the data constructed around the true reform are significant. Hence, the
figure confirms that the DDD estimates are robust to trends and fluctuations, and that
the main estimation results are valid. The figure also shows that the estimated effects on
32
unemployment around the true timing of the reform are highly significant for a longer time
span than the estimated effects on earnings. The dominant effect on unemployment relative
to the effect on earnings could suggest that the reform causes average earnings to increase
because the reform lowers unemployment and not because longer incarceration spells result
in higher rates of productivity and labor income.
In 2006 the eligibility rules for reception of social assistance where tightened. If this
change affected the sample’s unemployment rates, then it should translate into significant
effects for the full sample from around 24 months following release and onwards, while it
should not affect the estimates from the reduced sample. However, tables I.3, I.4, and I.5
showed that the estimates to unemployment rates were significant from the timing of release.
Moreover, the placebo-reforms around the timing of change to the eligibility rules in March
2006 should be significant, which they are not. Therefore, the estimated effects are not
results of the tightening of the eligibility rules for reception of social assistance.
5.2
Mechanisms
With the range incarceration lengths that this paper focuses on in mind, it seems unreasonable that the results stem from changes in human capital. Instead, the effects of the increase
in incarceration length could work through different channels. The survey results from table
I.1 discussed previously in the paper shows a positive relationship between incarceration
length and participation in rehabilitating programs which introduces a likely mechanism:
The reform may affect employment through increased participation rates in jail for which
an offender’s pre-reform sentence would otherwise have been too short, leaving the offenders solely with the possible stigma, job-loss, and general alienation from the labor market
which incarceration might involve. This proposition is in accordance with Balvig (2006),32
32
Produced by Flemming Balvig, Professor of Criminal Law, in cooperation with The Danish Bar and
Law Society.
33
who describes the chances of entering rehabilitation during a short incarceration spell in a
Danish jail as follows:
“Convicted offenders who are sentenced to the shortest incarceration spells are in practice
only able to use the jails’ rehabilitating services to a very limited degree (...) Jails do not
draft plans of action for the time of incarceration and for the release of the offenders, as a
consequence of the short incarceration spells.” [Balvig (2006, pp. 12), own translation].
Hence, the longer incarceration spells induced by the reform may have increased labor
market outcomes simply by giving prison authorities additional time to aid the offender at
the time of release. Also, if jail is no longer an exception to everyday life but something
more persistent, incarceration may be perceived quite differently, so e.g. an increase from
one month of incarceration to two months causes the offender to update his perception of
the payoff to crime to a lower level, thereby reducing the likelihood of recidivism (Abrams
(2012); Owens (2009); Sah (1991)) and thus increasing chances finding employment. In order
to gain further insight into the estimated effects, I calculate the average characteristics of
the group whose incarceration lengths the reform affected the most. Almond & Doyle (2011)
provide a framework for estimating complier characteristics in estimations of Local Average
Treatment Effects. I adapt this technique in order to estimate the average characteristics of
those who experienced the largest increase in incarceration length as a result of the reform.
Figure I.2 showed that a large proportion of offenders served two months instead of one
month. I define a dummy variable P equal to 0 if individual i served 35 days or less in jail
and equal to 1 if i served more than 35 days. Let πa be the fraction of always-takers who
would have served more than 35 days disregarding of whether they committed their crime
before or after the reform. Let πn be the fraction of never-takers who would have served less
than 35 days disregarding of whether they committed their crime before or after the reform.
πa is estimated as the fraction of pre-reform offenders who served more than 35 days and πn
is estimated as the fraction of post-reform offenders who did not serve more than 35 days.
34
Finally, πc is those who only served more than 35 days in jail as a result of the reform. By
monotonicity I can estimate πc = 1 − πa − πn and identify the average characteristics for the
offenders who served more than 35 days as a result of the reform as:
πa
πc + πa
E (X | P = 1, D = 1) −
E (X | P = 1, D = 0)
πc
π c + πa
(5)
Table IA.5 in the appendix shows the average characteristics of the group that only served
more than 35 days in jail as a result of the reform and the full sample. The table shows that
those who experienced the largest effect from the reform were younger, not married, had
very little education, and had lower pre-incarceration unemployment rates compared to the
full sample. Also, the criminal trajectory of those who served around two months in stead
of one month were shorter, and very few had a previous convictions of violent crimes. This
finding sheds light on the size of the main estimation results presented earlier. The compliers
(younger offenders at the onset of a long criminal trajectory) are likely much more malleable
and benefit much more from a change to their life course compared with the average offenders
(older offenders with a long criminal history).
The results also imply that incarceration may benefit the young offenders with a short
criminal record at the intensive margin, as opposed to the extensive margin, where e.g., Aizer
& Doyle (2011) show that incarceration has large negative effects for juvenile offenders.
I.e. once the offender is convicted to imprisonment, young offenders may benefit more
from rehabilitating programs or be more likely to change their perception of the payoff to
crime than older offenders. Moreover, the sizes of the estimates on unemployment rates and
earnings also suggest a positive long run effect of the reform using a back-of-an-envelope
cost-benefit calculation. I derive this by using the estimated effects on unemployment and
earnings to proxy savings on social assistance and increased tax revenue while correcting for
35
the average costs per offender of the increased incarceration length caused by the reform.33
The approximation yields a positive net present value within the first two years after release.
6
Conclusion
This paper investigates how incarceration length affects unemployment rates, dependency
on other public transfers, and earnings for offenders who receive short jail sentences. I use a
reform of the Danish penal code in 2002 to facilitate causal inference.
The estimates showed that an increase in incarceration length resulted in lower rates of
unemployment in a sample of violent offenders. In the first years following release, unemployment rates were reduced by as much as approximately 10 percentage points as an effect
of the reform, though the estimates were ambiguous on the persistence of the effect beyond
two years after release. The results to unemployment were robust with respect to limitation
of the time-span and also to a series of placebo-reforms. In contrast, dependency on other
public transfers was not affected by the reform. This implies that the increase in incarceration length increased the residual outcome self-dependency and employment. Furthermore,
the initial estimates suggested a positive effect on earnings that increased with time after
release. While the estimated effect on earnings was robust to differential time trends according to pre-incarceration characteristics and a series of placebo-reforms, the increases in
earnings were not highly significant. This suggests that the effect on average earnings may
be a second order effect that works through the reduction to unemployment and not e.g.
through higher wage rates.
The conclusion that longer incarceration spells lower unemployment is in accordance
with the results from Kling (2006). The stronger effects found in this paper may arise
from the margin of evaluation. This paper focuses strictly on offenders who received short
33
The average cost of one week of incarceration in 2002 was approximately USD 1,000 in 2005 prices,
according to the Danish Prison and Probation Service.
36
incarceration spells, which constitute the majority of Danish offenders who are sentenced to
imprisonment, whereas Kling (2006) included a wider range of offenders to estimate average
general effects that may have offset heterogeneous effects. The larger effects could also arise
due to the characteristics of the group of offenders who experienced the largest increases in
incarceration lengths due to the reform. The reform mainly affected men that were younger
and had a shorter criminal history compared to the full sample. As younger individuals may
be more malleable than older offenders, young offenders may benefit significantly more from
rehabilitating programs or change their perception of the payoff to crime to a larger degree
compared to their older peers with longer criminal records.
The results of this paper rely on the exogeneity of the reform and for the DDD estimates
on the use of property offenders as an additional control group. If the reform was not
exogenous and caused the average offender to change, it is reasonable to assume that longer
sentences would result in a treatment group that has weaker socioeconomic potential than the
control group - or in other words, a group with less employment-security and poorer affiliation
to the labor market, etc. However, the results (especially for the rate of unemployment)
suggest the opposite. If the use of the reform in this setting is endogenous, the likely direction
of bias is thus not towards zero. The direction of the bias will be changed indeterminately if
the two groups experienced different trends in the outcomes or alternatively if the dips/spikes
prior to incarceration differed. The paper shows that this was not the case. Nevertheless,
the pre-incarceration dips/spikes call for further study, which should elucidate whether the
dips/spikes are a general phenomenon for all offender types and further, how they are related
to the criminal acts themselves and the severity of the crimes, in order to uncover any selfselection.
It is worthwhile to consider whether very short sentences only serve to stigmatize offenders
without providing any proper aid or incentive to rehabilitate. Policy-makers and judges,
for instance, may consider whether very short sentences of imprisonment could usefully be
37
replaced by suspended sentences or community service, without violating the victims’ sense
of justice. And where imprisonment is deemed necessary, the various stakeholders should
perhaps consider the offender’s possibilities of rehabilitation to a greater degree.
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42
A
Supplementary Results
Table IA.1: Estimation Results Using Log Earnings
Periods
1-6 months after release
DD
0.216
(0.173)
(0.341)
7-12 months after release
0.489***
0.416
13-18 months after release
19-24 months after release
25-30 months after release
31-36 months after release
R2
N
Wald statistic (p-val)
(0.193)
0.583***
(0.206)
0.689***
(0.222)
0.609***
(0.221)
0.919***
(0.217)
DDD
0.270
(0.368)
0.446
(0.384)
0.740*
(0.395)
0.511
(0.406)
0.413
(0.425)
0.015
0.031
1,748
2,388
<0.001*** 0.158
Significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows DD and DDD regression results until 36
months after release from jail with log earnings as outcome.
The block-bootstrapped standard errors are reported in
parentheses below the estimates
43
44
(0.043)
(0.020)
(0.020)
-0.098***
(0.021)
-0.065***
(0.021)
-0.075***
(0.021)
-0.048***
(0.021)
(0.043)
-0.068
(0.042)
-0.054
(0.039)
-0.121***
(0.041)
-0.106***
(0.041)
-0.134***
(0.039)
0.016
0.021
0.022
0.025
1,748
2,388
1,748
2,388
<0.001*** <0.001*** <0.001*** <0.001***
-0.066
(0.042)
-0.097***
-0.054
-0.065***
(0.021)
(0.040)
(0.021)
(0.041)
-0.120***
(0.021)
-0.074***
-0.108***
(0.041)
(0.021)
-0.050***
-0.138***
-0.057***
-0.055**
(0.043)
-0.067
(0.042)
-0.054
(0.039)
-0.120***
(0.411)
-0.106***
(0.042)
-0.124***
(0.043)
0.064
0.056
1,748
2,388
<0.001*** <0.001***
(0.020)
-0.098***
(0.021)
-0.065***
(0.021)
-0.075***
(0.021)
-0.049***
(0.021)
-0.051***
(0.019)
(0.017)
(0.018)
(0.039)
Unem. as before jail Full unem. in jail
DD
DDD
DD
DDD
-0.032*** -0.094***
-0.001
-0.063
Full emp. in jail
DD
DDD
-0.029
-0.097*
Significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows DD and DDD regression results where time 0 is the start of incarceration instead of release from jail.
The table shows the results for unemployment as outcome using three different imputations of in-jail unemployment:
Full employment, unemployment rate as before incarceration, and full unemployment.
The block-bootstrapped standard errors are reported in parentheses below the estimates
R2
N
Wald statistic (p-val)
31-36 months after incarceration start
25-30 months after incarceration start
19-24 months after incarceration start
13-18 months after incarceration start
7-12 months after incarceration start
1-6 months after incarceration start
Periods
Table IA.2: Estimation Results From Start of Incarceration
Table IA.3: Estimation Results Discounted Earnings
Periods
1-6 months after release
DD
86.391
(62.512)
(114.950)
7-12 months after release
149.878**
167.508
13-18 months after release
19-24 months after release
(75.598)
(123.980)
125.534
125.339
(77.224)
(136.473)
253.323*** 299.236**
(81.590)
25-30 months after release
R2
N
Wald statistic (p-val)
(143.677)
233.744*** 202.546
(86.992)
31-36 months after release
DDD
142.046
(153.984)
389.898*** 222.889
(85.764)
(163.696)
0.023
1,748
<0.001***
0.026
2,388
0.059*
Significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows DD and DDD regression results with
discounted earnings as outcome. Discount rate is 0.04.
The block-bootstrapped standard errors are reported in
parentheses below the estimates
45
Table IA.4: Summary Statistics by Treatment Status for Reduced Sample Window
Variable
Measured 12 months prior to incarceration
Unemployed
Dependent on other public transfers
Earnings (USD 2005)
Age
Married
Cohabitant
Have children
Non-western immigrants or descendants
No job-qualifying education
Vocational or skilled
Upper secondary or higher
Measured at the start of incarceration
Have been convicted before
Have been convicted of a violent crime before
Have been convicted of a property crime before
Months since 1st date of crime leading to an indictment
Months since 1st date of crime leading to an conviction
Months since 1st incarceration
Number of previous convictions
N
Full sample
Control
Treatment
0.32
(0.45)
0.18
(0.35)
1,532
(1,891)
28.99
(7.91)
0.21
(0.41)
0.29
(0.46)
0.39
(0.49)
0.13
(0.34)
0.67
(0.47)
0.23
(0.42)
0.10
(0.30)
0.33
(0.46)
0.17
(0.37)
1,427
(1,964)
29.27
(7.97)
0.25
(0.43)
0.32
(0.45)
0.41
(0.49)
0.16
(0.37)
0.63
(0.48)
0.26
(0.44)
0.11
(0.31)
0.30
(0.44)
0.16
(0.33)
1,481
(1,925)
28.71
(7.87)
0.18
(0.38)
0.27
(0.47)
0.37
(0.48)
0.10
(0.30)
0.70
(0.46)
0.21
(0.41)
0.09
(0.29)
0.87
(0.33)
0.52
(0.50)
0.68
(0.47)
117
(84)
106
(86)
52
(78)
4.96
(6.06)
351
0.90
(0.31)
0.56
(0.50)
0.67
(0.46)
118
(83)
106
(85)
50
(75)
4.95
(6.01)
172
0.85
(0.35)
0.48
(0.50)
0.69
(0.47)
117
(85)
106
(87)
55
(81)
4.937
(6.12)
179
Sign. diff.
∗
T-test for differences in the means; significance levels: ∗ : 10% ∗∗ : 5%
∗ ∗ ∗ : 1%
Note: Table shows summary statistics for the full sample and divided by treatment status for the reduced sample window.
Sign. diff. indicate significant difference in means between the control and treatment groups.
46
Table IA.5: Summary Statistics for the Compliers and the Full Sample
Variable
Increased incarceration Full sample
length to +35 days
Measured 12 months prior to incarceration
Unemployed
Dependent on other public transfers
Earnings (USD 2005)
Age
Married
Cohabitant
Have children
Non-western immigrants or descendants
No job-qualifying education
Vocational or skilled
Upper secondary or higher
Measured at the start of incarceration
Have been convicted before
Have been convicted of a violent crime before
Have been convicted of a property crime before
Months since 1st date of crime leading to an indictment
Months since 1st date of crime leading to an conviction
Months since 1st incarceration
Number of previous convictions
0.24
0.12
1,406
24.89
0.00
0.42
0.25
0.17
0.72
0.18
0.10
0.33
0.15
1,473
28.13
0.23
0.28
0.36
0.12
0.67
0.23
0.10
0.83
0.05
0.56
101
83
25
2.90
0.83
0.48
0.67
109
98
46
4.44
Note: Table shows summary statistics for the full sample and compliers if the reform is used as an IV for jail¿35 days
and not reduced form as in the remainder of the paper.
47
Figure I.1: Trends in Number of Crime Convictions, Males Aged 18-45 at Time of Crime
((a)) All crime, excl. traffic
((b)) Property crime
((c)) Ordinary violence
Note: Figures show monthly number of crimes, excluding crimes against the Traffic Act, number of
property crimes (Penal Law), number of simple violent crimes (as in the paper) indexed to the number of
crimes in each category in May 2002 for males aged between 18 and 45 at the time of the crime. The
vertical red lines mark the period where the paper’s sample is drawn from.
B
Data Appendix
This section describes the construction of the main sample and variables as outlined in
section 3. The construction of the auxiliary sample (for the DDD estimations) is described
in the appendix.
As noted previously, the paper uses full population Danish register data. I make use of
48
the criminal registers for incarcerations, convictions and charges, the DREAM database, the
educational registers, the demographics registers, and the earnings registers.
Construction of Sample and Crime Variables
First, I select all incarceration spells between 1980 and 2007. Second, I merge the relevant
case specific variables to the individual observations of incarceration spells, by using the
unique combination of the case and social-security numbers. I then exclude individuals
who were not sentenced to imprisonment. This includes individuals who were convicted
to detainment (as these are de facto mentally ill) and all individuals who were not found
guilty. If a given case has been appealed, I only include the information from the final trial.
At this point, the sample includes an individual specific entry for all incarceration spells
as results of convictions to imprisonment. To this information, I merge information former
and subsequent charges and convictions from the various criminal registers. I also merge
information on former and subsequent incarceration spells, by merging the information from
the first and second step, as described above, to this data set. I also merge information
on demographic characteristics to the data. Limiting the data to men between the age of
18 and 45 and dividing by type of crime allows me to create the upper panel of figure I.3.
I create the lower panel of figure I.3 by combining the data of incarceration spells with
data on all crimes, together with type of crime and type of conviction (suspended sentence,
imprisonment, acquitted, etc.).
I only keep individuals who were convicted of ordinary violence as defined by Statistics
Denmark’s coding34 in the sample. I also limit the sample to men aged 18 to 45. Finally, I
limit the data according to the desired time span (e.g., 18 or 4 months) around the timing
of the reform. By plotting the lengths of the various incarceration spells I create figure I.2.
34
See
http://dst.dk/tilsalg/forskningsservice/Dokumentation/hkt4forsker/hkt4 variabel liste forsker/
hkt4 variabel.aspx?fk=13217, for a list of codes for the different types of crime,
49
Construction of Outcome Variables The DREAM database contains weekly information on all recipients of public transfers in Denmark along with a specification on type of
public transfer (unemployment benefits, social assistance, public pensions, etc.) from 1991
until 2011. I merge the DREAM database to the data introduced above by the individualspecific social security number. I summarize the weekly entries to monthly entries. I also
merge information on yearly wage earnings (which is available from 1980 to 2010) to the
data. I deflate earnings to 2005 dollars. The individual information on reception of public
transfers (e.g., when a given individual received unemployment benefits, social assistance,
educational support, public pensions, etc.) allows me to identify the months where a given
individual was earning his wages. Hence, I compute monthly earnings. From the information
on monthly earnings, unemployment rates, and reception of other public transfers I estimate
the content of figure I.1.
Construction of Covariates I merge information on educational attainment and various demographics to the data by the individual-specific social security number. The data
is reported on yearly basis. However, it also includes information on the date of last entry
change, e.g., date of last change to marital status. From this I compute monthly variables. At this point, each individual incarceration spell is a panel of monthly observations of
earnings, unemployment, dependency of other public transfers, educational attainment, and
marital status together with information on ethnicity, and prior and future crimes. From
this information I can estimate the contents of table I.2. Also, I can use the information on
each individual’s date of crime relative to the timing of the reform, incarceration length, and
covariates in order to estimate the content of table IA.5.
Finalizing the Data and Placebo Reforms Finally, I limit the sample only to include
information from 12 months prior to beginning of and 36 months following release from
the incarceration in question. I discard all observations between the first and the last date
50
of incarceration and pool the monthly observations to biannual observations. The data
construction is complete and I can estimate the effects of the reform as reported in section
5.
To estimate the content of figure I.4, I construct the data as described in this section,
but change the time span conditions to the relevant dates around the timing of the placebo
reform in question. I then create a new dummy variable indicating the timing of the placebo
reform, which is used for the estimations. I do this for each of the placebo reforms reported
in figure I.4.
Construction of Auxiliary Sample
This auxiliary sample has been constructed as described in section B. First, I construct a
sample that consists of men who were aged 18 to 45 at the date of the crime for individuals
convicted of various types of fraud, robbery, theft, and tax evasion. Second, I limit the
sample to include individuals who committed the crime in focus between December 2000
and November 2003.
Table IB.1 shows summary statistics for the auxiliary sample. The table shows that the
auxiliary sample also had a low level of resources as measured by socioeconomic variables.
The majority were either unemployed or not in the labor force. Most had not completed
any education beyond secondary school and few were married or cohabiting. The table also
shows that the only significant difference across the reform is the number of immigrants and
descendants.
51
Table IB.1: Summary Staticstics of Auxiliary Sample
Variable
Unemployment
Depedendency of other public transfers
Earnings
Age
Married
Cohabitant
Have children
Non-western immigrants or descendants***
No job-qualifying education
Vocational or skilled
Upper secondary or higher
N
Full sample
0.37
Control
0.36
Treatment
0.39
(0.47)
(0.47)
(0.47)
0.17
0.19
0.15
(0.36)
(0.38)
(0.34)
864
802
926
(1,521)
(1,454)
(1,585)
26.84
27.28
26.41
(7.62)
(7.67)
(7.55)
0.19
0.20
0.19
(0.40)
(0.40)
(0.39)
0.25
0.25
0.25
(0.43)
(0.43)
(0.43)
0.28
0.30
0.26
(0.45)
(0.46)
(0.44)
0.20
0.17
0.24
(0.40)
(0.37)
(0.43)
0.73
0.73
0.73
(0.45)
(0.44)
(0.45)
0.15
0.15
0.16
(0.36)
(0.36)
(0.37)
0.12
0.12
0.11
(0.32)
(0.32)
(0.32)
640
318
320
T-test for differences in the means; significance levels: ∗ : p<10% ∗∗ : p<5%
∗ ∗ ∗ : p<1%
Note: Table shows summary statistics for the full sample and divided by treatment status.
52
Part II
School Starting Age and the
Crime-Age Profile
53
School Starting Age and the Crime-Age Profile
Rasmus Landersø, Helena Skyt Nielsen? , and Marianne Simonsen?
Abstract
This paper uses register-based data to investigate the effects of school starting age
on crime. Through this, we provide insights into the determinants of crime-age profiles.
We exploit that Danish children typically start first grade in the calendar year they
turn seven, which gives rise to a discontinuity in school starting age for children born
around New Year. Our analysis speaks against a simple invariant crime-age profile as
is popular in criminology: we find that higher school starting age lowers the propensity
to commit crime at young ages and that this to some extent is driven by incapacitation.
We also find persistent effects on the number of crimes committed for boys.
JEL: I21, K42
Keywords: old-for-grade, school start, criminal charges, violence, property crime.
Acknowledgments: Comments from Matthew Lindquist, Lance Lochner, Naci Mocan, Magne Mogstad,
Bas van der Klaauw, Peter Sandholt Jensen, Anna Piil Damm, as well as seminar participants at BeNA
Humboldt University, ISER, University of Essex, University of Sussex, KORA, CAM, University of St. Gallen, Xiamen University, the joint University of Bergen & UCL workshop 2013, the workshop on “Economics
of Successful Children” at Aarhus University 2013, the University of Chicago’s Life Cycle and Inequality
working group as well as participants at ESPE 2013, EALE 2013, ASSA 2014, the IZA YSW at Georgetown
University 2014, and at the DGPE workshop are appreciated. Financial support from the Danish Council
for Strategic Research (CSER, 09-070295) and CIRRAU (Simonsen) is gratefully acknowledged. The usual
disclaimer applies.
Revise and resubmit requested from the Economic Journal.
?
Department of Business and Economics, Aarhus University
1
Introduction
This paper investigates long-term effects of school starting age on crime while exploiting a
discontinuity in school starting age for children born around New Year. Through this, we
provide novel insights into the determinants of life-cycle criminal behavior. The crime-age
profile refers to an almost universally observed relationship between crime rates and age,
where crime rates increase continuously until around age 18-20 and then decrease for the
remainder of the life. We use the mechanical relationship between delayed school entry and
delayed life-course to address whether the crime-age relationship is entirely caused by age
(Gottfredson and Hirschi (1990)) or can be mediated by the timing of key life experiences
(Sampson and Laub (1995)).
A large literature is concerned with effects of school starting age and subsequent educational outcomes and has convincingly shown that starting school later leads to improved test
scores (e.g. Bedard and Dhuey (2006)). Black et al. (2011) and Crawford et al. (2010) refine
this type of analysis and show that this result is completely driven by an age-at-test effect:
children who start school later are simply older when they perform tests and this leads to
better performance. Just as these authors show in the case of test scores, we show that it is
important for our analysis whether crime is aligned in terms of age or life-course.
In contrast to existing studies, our paper is concerned with crime outcomes. School
starting age may affect crime through several channels. Firstly, to some extent, enrollment
leads to locking-in or incapacitation: when youth are in school, they simply have less time to
commit crime (Lochner (2011)). Previous studies confirm this mechanism: Jacob and Lefgren
(2003) and Luallen (2006) exploit plausibly exogenous changes in number of school days,1
1
They study urban schools and find that increasing the number of school days reduce arrests for property
crimes but increases arrests for violent crimes. While the effect on property crime is thought to be due
to incapacitation, the effect on violent crime is thought to be a network effect (spending more time with
criminal peers).
55
while Anderson (2014) uses changes in compulsory schooling laws.2,3 Secondly, postponing
school start delays graduation, which may in turn affect opportunity costs of crime at a given
age (Grogger (1998), Uggen (2000)). Thirdly, skill formation and behavior may play a role.
Cunha and Heckman (2008) show that cognitive and (especially) non-cognitive skills at preschool ages are key determinants of later skill acquisition, behavior, and adult outcomes. If
different school starting ages are associated with different levels of skills (school readiness),
then these differences may be amplified and affect other outcomes such as the tendency
to engage in criminal activities. Lubotsky and Kaestner (2014) find some support for such
complementarity as cognitive skills of pupils who are old-for-grade grow faster in kindergarten
and first grade, but the gap fades away after first grade. Black et al. (2011) show that higher
school starting age leads to improved mental health (for boys) and a lower risk of teenage
pregnancies (for girls), while there is conflicting evidence regarding the risk of receiving
ADHD diagnoses (Dalsgaard et al. (2012); Elder (2010); Evans et al. (2010)). A final channel
is the individuals placement in the age hierarchy. Increasing school starting age by one year
will most likely move the individual from being one of the youngest to being one of the oldest
children in the classroom (e.g., Gaviria and Raphael (2001) and Sacerdote (2001)). However,
the potential effects of such a change are ambiguous. On the one hand, having older peers
who are more likely to engage in risky behavior may spark risky behavior at an earlier stage.
On the other hand, having older peers might also increase skill acquisition and maturity,
thus lowering delinquent behavior and improving educational outcomes. Fredriksson and
Öckert (2005) and Black et al. (2013) find no substantial impact of the age composition of
peers on educational and labour market outcomes or on teenage pregnancies among girls,
and thus rule out that the relative age composition in class explains the impact of school
starting age.
2
Anderson estimates that a minimum dropout age of 18 decreases arrest rates for 16-18 year-olds by 17%.
The effect is present for both violent and property crime.
3
One note of caution is that crime reports to the police may differ according to whether youth are in
school or not. If criminal events taking place in school are treated differently than criminal events taking
place outside school, this would lead to similar findings. This issue is likely more relevant for violent crime
than for property crime or traffic incidents.
56
To the best of our knowledge, Cook and Kang (forthcoming) is the only other study of
the relationship between school starting age and crime. They use administrative data for
five cohorts of public school children in North Carolina to show that school starting age
decreases juvenile delinquency but increases serious adult crime. As opposed to our study,
their analysis is, however, complicated by grade retention and the existence of compulsory
school leaving age legislation that creates a mechanical relationship between school starting
age and length of compulsory education.
Our empirical analyses rely on exogenous variation in school starting age generated by administrative rules. In particular, we exploit that Danish children typically start first grade in
the calendar year they turn seven, which gives rise to a fuzzy regression discontinuity design.
By comparing children born in December with children born in January we investigate the
effects of starting first grade at the age of 6.6 compared to 7.6. Our analysis uses Danish
register-based data for children born in the period from 1981-1993 with crucial information
on exact birth dates, a range of crime outcomes, and a rich set of background characteristics.
We find that higher age at school start lowers the propensity to commit crime at young
ages but the effects begin to fade out in the 20s. Hence the crime-age profile can be modified
by life-course and is not only determined by age per se. In addition to a delay in the onset of
a criminal trajectory, for boys a higher school starting age also causes a persistent reduction
in the number of crimes committed, indicating that the persistence of criminal behavior is
affected by age and criminal opportunity in unison. Furthermore, we investigate potential
mechanisms behind the crime reductions during the teen-years and find that incapacitation
does seem to play an important role. For boys, a higher school starting age reduces criminal
charges significantly until age 19, and the effect is mainly driven by property crime. For
girls, a higher school starting age postpones the initiation of crime, and the effect is driven
by violent crime. Finally, we find that the relative age of classroom peers does not seem to
be behind the reduction in crime.
57
The paper is structured as follows: Section 2 briefly reviews the Danish institutional
set-up and discusses mechanism through which child behavior may be affected by school
starting age and Section 3 describes the methodology. Section 4 presents our data, Section
5 the results and finally Section 6 concludes.
2
2.1
Institutional settings and mechanisms
Educational Institutions and School Starting Age
During the period relevant for this study, Danish law stipulated that education was compulsory from the calendar year of the child’s 7th birthday and until completion of 9th grade.4
This school system is fortunate for a study like ours because there is no automatic relationship between school starting age and minimum required schooling as there would be in
the US and the UK systems, for instance. After 9th grade, education was voluntary and
could follow an academic path (starting with high school) or a vocational path (starting with
vocational school).5
The year before entering first grade, children could enroll in a voluntary preschool class.
The preschool class, compulsory schooling from 1st to 9th grade and post-compulsory schooling were free of charge. Furthermore, most children below the age of six were inscribed into
some form of public child care, which was heavily subsidized.6
Parents and administrators have considerable leeway in deciding when children should
4
The school starting regulations are not strictly enforced and exemptions are granted based on applications
from the parents. Exemptions are granted by the local municipality if it is considered beneficial for the child’s
development. School start can only be delayed by one year, and school is no longer compulsory from July 31
in the calendar year of the child’s 17th birthday even if 9th grade has not been completed. School children
do not pass or fail grades, but in collaboration with the parents, the school principal can decide that child
repeats a grade or jumps a grade again if this is considered beneficial for the childs development. For more
details consult the Danish Law of public schools.
5
It was also possible to complete a voluntary 70th grade before continuing on to a vocational or academic
path.
6
A minimum of 67 % of the expenses is covered by the local authorities, c.f. the Danish Law of day care.
58
start school.7 Therefore, school starting age is not random and is most likely affected by
a range of factors that may also correlate with the child’s outcomes, behavioral as well as
academic. For example children’s overall school readiness and behavior in preschool are likely
to affect the timing of school start.8 But other factors may impact on the decision as well:
as shown by the previous literature, starting later is likely to increase test scores. While
this has not been found to impact significantly on long term outcomes such as earnings,9
higher grades may improve the consumption value of attending school and allow for a more
extensive educational choice set. Finally, there is considerable variation in school starting
age culture across municipalities even conditional on a rich set of observable characteristics.
For completeness, we will investigate some of these hypotheses towards the end of the paper.
To meaningfully address consequences of school starting age, our empirical analysis will
make use of the following observation: because the formal age at school start is defined by
the year of birth, each January 1st provides a cut-off point at which children born on each
side are subject to a one year difference in timing of administratively determined school
start, even though they are born very close in time. Section 3 will formalize this idea. Some
parents of children born close to this cut-off date do choose to manipulate their childrens
actual school starting age: children born at the end of the year are more likely to postpone
school start one year, whereas children born early in the year are more likely to start school
one year earlier than the law stipulates.10 In consequence, some children born in December
will start school one year later than they are supposed to - approximately at age 7.6 years whereas the remainder of the children born in December will start when their age is around
6.6 years. Likewise, some children born in January will start school at age 6.6, which is
7
UNI-C (2009) documents this and describes background characteristics of children across school starting
age.
8
This pattern is clear from Figure A1 that shows the distributions of social and emotional difficulties at
age 4 among punctual and late school starters, drawn from an auxiliary data source (the Danish Longitudinal
Survey of Children).
9
Fredriksson and Öckert (2013) do find earnings gains for individuals with low-educated parents.
10
A recent white-paper on school start concluded that ’many parents worry whether their children are
ready to start school, and these concerns are supported by the preschool staff’, cf. God Skolestart (2006).
59
Figure II.1: Fraction Punctual, Early, and Late School Start, by Birth Date (selected cohorts)
((a)) Girls
((b)) Boys
Note: Figure shows the school starting pattern of the full population of children born January 1 1994 January 1 1995. Early school start refers to school start the calendar year the child turns 6, punctual school
start refers to school start the calendar year the child turns 7, and late school start refers to school start the
calendar year the child turns 8.
one year earlier than the law stipulates, while the remainder will start school at age 7.6.
As shown in Figure II.1, school starting age for children born around the cut-off date is
effectively reduced to a binary outcome: either children start at age 6.6 or they start at age
7.6. If children born around the cut-off date are 7.6 years old at school start, we label them
old-for-grade. Figure II.2 shows the fraction of children who are old-for-grade by date of
birth for each gender.
We see that there is a smooth upward trend in the fraction of girls and boys who are
old-for-grade in December followed by a large discontinuity around New Year. The figure
also shows that boys are much more likely than girls to be old-for-grade.
2.2
Institutions Guarding Juvenile Crime
Below we describe the institutions that may be relevant for understanding the potential
impact of schooling and school starting age, in particular, on criminal activity of teenagers.
In Denmark, the age of criminal responsibility is 15, which is high in an international
60
Figure II.2: Fraction who are Old-for-Grade, by Date of Birth
((a)) Girls
((b)) Boys
Note: Figure shows the fraction of children who are old-for-grade by date of birth around New Year (marked
by the vertical line). Being old-for-grade implies that the child starts school at age 7.6 instead of at age 6.6.
Averages for population of children born in December or January from December 1981 to January 1993.
comparison; England has an age of criminal responsibility of 10, while only few US states
have a formal limit and in those cases the limit is 6-12 years.11 Before their 15th birthday,
Danish children cannot be arrested, brought to court or imprisoned, although they may be
withheld up to 6 hours by the police in which case a social worker must be present during
interrogation. This is true regardless of the severity of the crime, and there is no such thing
as a youth court.12 At ages 15-17, youths are considered fully responsible for their criminal
acts, and may be imprisoned, though this should be separate from adult prisoners.13 Thus,
the focus is on prevention and rehabilitation rather than prosecution and punishment.
All local authorities have an interdisciplinary framework for prevention of juvenile crime
involving the schools, the social services and the police (denoted SSP). This is a network
of relevant players who collaborate to understand and prevent juvenile crime in the local
area. They are concerned with general, specific as well as individual-oriented policies and
interventions.
Reported victimisation rates in Denmark are falling like in the rest of the OECD. However,
11
http://www.unicef.org/pon97/p56a.htm.
The question of guilt is, in fact, never determined for children below the age of criminal responsibility.
The severity of the case is solely considered by the Attorney General.
13
See the Danish Service Act.
12
61
victimisation rates in Denmark are somewhat higher than in Norway and Sweden and also
higher than the OECD average (19 v. 16 %) while they are almost on par with the US (18
%) and the UK (21 %) rates.14 Therefore, we have no particular reason to expect that the
effects of school starting age on crime should be substantively different in Denmark compared
to other countries.
3
Methodology
Our goal is to estimate the effect school starting age (SSA) on associated crime outcomes.
Our equation of interest is the following:
Yi = α + βSSAi + Xi0 γ + εi
(1)
where Y denotes the outcome, X observable characteristics,15 and ε unobservable characteristics. ε is likely related to the choice of school starting age and would bias results
if ignored. To circumvent the problem that SSA is not randomly allocated, we formally
employ a strategy similar to Black et al. (2011), Evans et al. (2010), Elder (2010), and
Fredriksson and Öckert (2013). In particular, we exploit that school starting rules imply
that children born just prior to January 1st are on average younger when they enroll in
school than children born immediately after January 1st.
In some sense, we can think about administrative school starting age rules as imposing
time and effort costs on parents who choose to enroll their child later (or earlier) than prescribed. We can therefore instrument SSA with a dummy for being born immediately after
14
The reported victimisation rates reveal what proportion of a sample of 2000 individuals report that they
themselves or persons in their households had experienced one of ten types of conventional crimes (such as
vehicle-related crime, theft of personal property and contact crime), see OECD (2009).
15
X includes a constant and child and parental characteristics predictive of SSA and Crime: APGAR score,
birth weight, gestation length for children, mothers’ age at the birth of first child, both parents’ education
and labour market participation, a flexible function of distance in days to the cut-off, and a constant.
62
January 1st. As argued by the previous literature, such cut-off dates constitute valid instruments in the sense of being uncorrelated with unobserved characteristics of child outcomes.
Yet in order to estimate the local average treatment effect - the average effect of being
old-for-grade for the group of children who would be inclined to increase their school starting
age solely because they were born in January and not December - we also require that the
monotonicity assumption is satisfied. Barua and Lang (2012), Aliprantis (2012), and Fiorini
et al (2013) argue, however, that monotonicity is likely violated if the school starting age
distribution of children born just after the cut-off date does not stochastically dominate the
corresponding distribution for children born just before the cut-off date. In the US example
given by Barua and Lang (2012) for children born in the 1950s, children born in the last
quarter of the year were on average younger at school start than children born in the first
quarter of the year but the underlying choices were not monotonically related to the cut-off
date: while children born in the last quarter of the year were less likely to start school at
age 5 compared to children born in the first quarter of the year, they were at the same time
less likely to be very young (4 years or younger) and more likely to be very old (6 years or
older). Hence it seems that being born after the cut-off date increases school starting age
for some but reduces it for others.
We do not find this to be an issue in our setting because no children start more than
one year before/after the date at which they are supposed to start. This is illustrated by
Figure 1 where we show that school starting age in our case is effectively reduced to a binary
variable that indicates whether the child enrolls at age 6.6 or 7.6. Always-takers will start at
age 7.6 regardless of when they were born, never-takers will start at age 6.6, and compliers
will start at age 6.6 if born in December and 7.6 if born in January. For these groups, the
instrument monotonically increases school starting age. We assume away defiers: a child
whose parents choose to incur the costs of enrolling him earlier (at age 6.6) than at the age
specified by administrative rules if born in January but are at the same time also willing
63
to bear the additional costs of enrolling him later (at age 7.6) than at the age specified by
administrative rules if born in December. This type of behavior would both be inconsistent
with parental preferences for the child being among the youngest in his classroom as well
as preferences for him being the oldest. In practice, we consider a short bandwidth with
children born ± 30 days around January 1st. In our main specification, we model SSA as a
binary variable indicating a school starting age of 7.6 as opposed to 6.6. Along with various
standard robustness tests, we show that results are robust to modelling SSA as a continuous
variable. See more discussion in Section 5 below.
4
Data
We use Danish register-based data for children born in the period from mid-1981 until mid1993 with crucial information on exact birth dates, charges16 for property crime, violence
and other types of crime (in particular traffic incidents), together with the specific dates of
crime, and a rich set of background characteristics.
Crime Outcomes
As is true for most of the existing literature on school starting age, choosing the right
outcome is a challenge: on the one hand, one wants to align children in terms of age. This
is particularly relevant because crime is positively correlated with age in the age range
considered in this paper. On the other hand, one wants to align children in terms of length
of education because the agents that decide a child’s school staring age may focus on these
outcomes or because education may have a direct effect on the tendency to commit crime.
To address these issues, our main outcomes consist of age-specific measures but we also
separately consider criminal charges at a given point in the educational cycle.
16
Using charges instead of convictions enables us to use three additional years of data because the time
involved in processing cases through courts and subsequent appeals is obviated. Conclusions are robust to
using convictions instead of charges.
64
We consider two types of age-specific crime measures: one outcome measures whether an
individual has been charged with a crime at a given age from age 15 and onwards. This is
a memoryless measure, which simply informs about the tendency to commit crime at any
given age (i.e. from one birthday to the next). It is particularly useful for detecting sudden
changes in the crime-age profile caused by school starting age. Our other type of outcome
measures whether an individual has been charged with a crime at or before a given age and
in this way keeps track of earlier incidences. This is convenient if one wants to address more
permanent effects on crime. Because of considerable recidivism, both measures are required
to give a full picture of the consequences of school starting age on the crime-age curve. We
might see negative effects of school starting age on crime at a given age but not at crime
at or before a given age if those committing the crime are simply the same individuals.
Conversely, we could see effects on crime at or before a given age and not on crime at a
given age if school starting age has a longer-lasting effect on criminal behavior. It is clearly
important to be able to distinguish between these scenarios.
Due to space considerations some of our descriptive analyses and all robustness tests will
focus on the accumulated outcome but the full set of descriptives and formal results are
available on request. In addition to our main analyses, sub-analyses show results for types
of crime (’property crime’, ’violent crime’, and the residual ’other crime’) and number of
crimes to address differential effects on the intensive and extensive margin. Figure IIA.2
illustrates means of our main outcome variables. The figure replicates the well-known age
pattern where criminal activity peaks at ages 19-20 (Gottfredson and Hirschi (1990)). For
girls, 2% are charged with a crime at ages 19-20, while for boys 11% are charged with a crime
at ages 19-20, after which age the fraction declines. All over the age range, the proportion
charged with a crime is higher for individuals who are old-for-grade compared to individuals
who are young-for-grade. Our empirical analysis will reveal to what extent this reflects a
causal relationship.
65
To give a better sense of the nature of the crime committed, Table II.1 summarizes the
distribution of crime at or before a given age across three types of crime: property crime,
violent crime, and other crime.17 Throughout the age distribution, boys are three times more
likely to have been charged with a crime than girls. At the youngest ages, property crimes
tend to be most prevalent, but after age 18 when the individuals in the sample gradually
acquire a drivers license, other crimes including traffic incidents accumulate. For girls, other
crime dominates from age 22 onwards, while for boys it dominates already from age 18.
Table II.1: Means of selected outcome variables, by types of crime
Age
15
16
17
18
19
20
21
22
23
24
25
26
27
All
0.019
0.032
0.044
0.054
0.069
0.083
0.096
0.106
0.116
0.124
0.133
0.138
0.143
Property
0.018
0.029
0.037
0.043
0.049
0.053
0.055
0.056
0.056
0.057
0.057
0.057
0.057
Girls
Violence
0.002
0.003
0.005
0.007
0.009
0.010
0.010
0.011
0.011
0.012
0.012
0.012
0.011
Other
0.001
0.003
0.006
0.010
0.021
0.034
0.045
0.057
0.068
0.075
0.086
0.092
0.100
N
48,546
48,546
48,546
48,546
43,668
39,037
34,559
30.209
26,093
22,125
18,240
14,630
11,045
All
0.039
0.081
0.140
0.189
0.243
0.290
0.327
0.358
0.383
0.402
0.417
0.429
0.439
Property
0.033
0.059
0.081
0.101
0.118
0.131
0.141
0.147
0.151
0.154
0.156
0.156
0.157
Boys
Violence
0.006
0.014
0.025
0.036
0.047
0.057
0.065
0.070
0.074
0.076
0.079
0.081
0.082
Other
0.007
0.029
0.077
0.119
0.174
0.222
0.262
0.295
0.323
0.345
0.362
0.375
0.388
N
50,383
50,383
50,383
50,383
45,368
40,606
36,012
31,405
26,937
22,781
18,723
14,949
11,273
Note: Table shows fraction of sample who have commited crime until a given age, by age, gender, and crime type.
Violent crimes comprise the most severe types. The most common examples are ordinary
assaults, aggravated assaults, threats, and violence towards public servants. 80% of convictions for violence result in imprisonment or a suspended sentence for boys and 67% for girls.
Property crimes and other crime are typically less severe crime. The most frequent examples
of property crime are shoplifting, burglary, and vandalism. A quarter of all convictions for
property crime result in imprisonment or a suspended sentence for boys, while this number
falls below 10% for girls. The category of other crimes is dominated by traffic related crime
(50% for girls and 90% for boys) such as driving a car without a license, while the second
17
Due to space considerations, we have chosen only three broad categories of crimes. Different classifications would be possible.
66
largest category is drug or weapon related crime (e.g. selling drugs or possession of illegal
weapons). Convictions for other crimes rarely lead to imprisonment.
Table IIA.1 shows mean crime outcomes by birth-month and gender. Those born in
December tend to be more likely to have been charged with a crime compared to those born
in January. When we consider whether an individual has been charged with a crime at a
given age, we see that boys born in December are more likely to have been charged with a
crime at each age from 15 to 21, while the pattern is more scattered for girls (top panel).
This outcome will be important for our analysis of incapacitation. When we consider the
accumulated measure, namely whether or not the individual has been charged with a crime
at or before a given age, we see that the difference is significant up until age 24 (bottom
panel). As argued above, the accumulated outcome is more informative about potential
catching up effects and other long run effects.
Figure IIA.3 shows the standard regression-discontinuity plots for the accumulated crime
measures at ages 19 and 27. The figure reveals a discontinuity in the raw outcome variable
which is only statistically significant for boys at age 19.
Measuring School Starting Age
Unfortunately, we do not have information on the specific timing of school starting age for
the cohorts in question. Instead we use age in 8th grade as an approximation. We do observe
childrens exact ages at all grade levels from 2007 and onwards and we use this data to check
that the approximation of school starting age by age in 8th grade works very well (see Table
IIA.2). The vast majority of children who are old-for-grade at the end of elementary school
are old-for-grade already in preschool class, while very few children are redshirted from the
first grade and onwards.18 In addition, there is no relationship between the cut-off and being
held back or skipping grades during primary school.
18
As an additional check we report results from the first stage regression at various grade levels by use of
these recent data. Measurement errors in school starting age will impact on our results to the extent that
67
Background Characteristics
Using the registers we combine information on the childrens birth weight, gestational length,
APGAR score,19 demographic variables, educational variables, and crime by the unique individual identification number. In addition, we link these data to information about parents’
education and labour market outcomes as measured one year prior to the child’s birth. Importantly, we center all covariates and outcome variables on the cut-off dates instead of by
calendar year. Hence, we compare background information on children born in January year
t to the information on children born in December year t − 1 instead of comparing information on children born in January year t to the information on children born in December
year t.20 Similarly, outcome variables aligned by age for individuals born on each side of the
cut-off date are measured at the same point in time: exactly one’s birthday.
Table II.2 shows joint F-tests from a regression of the instrument on the rich set of
background variables for children born ± 30 days around January 1st for girls and boys
separately. These tests clearly suggest that the sample is balanced across the cut-off. Table
A3 in the Appendix shows mean background characteristics for December and January born
children. These are not jointly significantly different either (p=0.19). We see that for some
variables, means are significantly different but the differences are all very small in size21 and
the sign of the difference often varies by gender. We include all variables as covariates and
bound potential biases by the approach by Nevo and Rosen (2012); see discussion in Section
5.
they are correlated with the instrument. If children born in December are more likely to repeat a grade as
suggested by Elder and Lubotsky (2009), our results will be biased towards zero.
19
The APGAR score ranges from zero to 10 and summarizes the health of a newborn child based on five
simple criteria: Appearance, Pulse, Grimace, Activity and Respiration.
20
For children born in December 1981 or January 1982 we use parental characteristics measured in 1980,
while we for children born in December 1982 or January 1983 use parental characteristics measured in 1981
etc.
21
The difference in birth weight is for example 16 grams, which corresponds to 0.03 point difference in IQ
according to Black et al. (2007). Figure IIA.4 shows the variation of birthweight on either side of the cut
off. Even though the (numerically small) difference is significantly different for boys and girls, there is no
systematic pattern across dates.
68
Table II.2: Balancing Tests: Regression of Instrument on Background Characteristics
Girls
0.53
0.94
48,546
X
X
F-statistic
P-value
N
Distance to cut-off
Covariates
Boys
0.70
0.81
50,383
X
X
Note: Table shows F-statistics and associated pvalues from regressions of birth-month (January=1)
on the full set of covariates (background characteristics presented in Table IIA.3 and cohort fixed effects)
as well as distance to cut-off in days.
5
5.1
Results
Timing of Birth Within the Calendar Year and School Starting Age
Table II.3 presents our first stage results, using a dummy for birth in January as instrument
for school starting age. The table shows the first stage results estimated both with and
without controls. All specifications include cohort fixed effects (indicator variables for being
born Dec 1981-Jan 1982, Dec 1982-Jan 1983 etc.) and the distance in days to the cut-off
linearly.22 Remaining estimates may be found in Table IIA.4 in the Appendix.
In line with Figure II.2, we see that the instrument strongly predicts whether children
start school at age 7.6 or 6.6: children born in January are significantly more likely to be
relatively old when they start school compared to children born in December and the effect
is large. This is despite the tendency for some children born in December to delay enrolment
and start at age 7.6 instead. The instrument is highly significant and the associated Fstatistic easily passes the Staiger-Stock rule-of-thumb.With one endogenous variable and 1
instrument, F should be greater than 10,23
22
Results are robust to including more flexible polynomials of the running variable.
As discussed above, our measure of school starting age is based on age in grade 8 rather than actual
age at school start. In Table IIA.5, we use the richer data from 2007 onwards to demonstrate that the first
stage is literally unaffected by this approximation; for individuals born Dec 2000-Jan 2001, we can compare
first stage as measured by being old-for-grade in preschool versus 2nd grade, while for individuals born
Dec 1996-Jan 1997, we can compare first stage as measured by being old-for-grade in 4th versus 8th grade.
While the first stage differs slightly across cohorts, it does not differ by grade level and thus supports the
approximation
23
69
Table II.3: First Stage Estimation Results: Children Born in December and January
January=1
Days to cut-off, December
Days to cut-off, January
Constant
N
Cohort Fixed Effects
Remaining covariates
F-value for January dummy
Girls
0.245∗∗∗ 0.244∗∗∗
-0.005∗∗∗ -0.005∗∗∗
0.003∗∗∗ 0.003∗∗∗
0.714∗∗∗ 2.282∗∗∗
48,546
50,383
X
X
X
877.29
891.59
Boys
0.172∗∗∗ 0.171∗∗∗
-0.005∗∗∗ -0.005∗∗∗
0.001∗∗∗ 0.001∗∗∗
0.872∗∗∗ 1.540∗∗∗
X
574.01
X
X
576.22
Note: Table shows results from linear regressions of indicators for starting school
at age 7.6 instead of 6.6 while conditioning on the cut-off dummyies (January=1),
distance to cut-off, cohort fixed effects and background characteristics (see Table
IIA.3). p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗ .
5.2
Crime Results: 2SLS
The Propensity to Commit Crime
Figure II.3 shows our main estimation results; see also the corresponding Tables IIA.6 and
IIA.7. The left hand side figures show the estimation results for crime at a given age and the
right hand side figures show the estimation results for crime at or before a given age (conditional on the full set of covariates). We find that being old-for-grade leads to a significant
reduction in the propensity to commit crime at each age until age 19 for boys but only at
age 15 for girls. Point estimates at older ages are primarily negative for girls but become
very close to zero for boys.24 We cannot formally detect statistically significant differences in
coefficient estimates across ages because confidence bands are too wide. Note that individuals who are young-for-grade turn 15 during their final year in comprehensive school, while
individuals who are old-for-grade turn 16. Individuals who are young-for-grade turn 18 or
19 during their final year in high school, while individuals who are old-for-grade turn 19 or
20 (depending on whether they took the optional 10th grade or not). Formal analyses of the
impact of being old-for-grade on enrolment and completed years of schooling at a given age
show that a main effect of being old-for-grade is postponement of the educational cycle (see
24
This is not driven by the smaller sample for which we observe outcomes at all ages. The estimate profile
is in fact similar if we only include individuals born in 1985 or before.
70
Figure IIA.5). While short run effects are large and fluctuate widely at different steps of the
education-ladder, long-term effects of school starting age on educational outcomes are small
or zero (in line with Black et al. (2011)). We therefore interpret the age pattern in our crime
results as supportive of the incapacitation hypothesis. It suggests that compulsory school is
protective against crime for girls, while also high school is protective against crime for boys.
When we instead look at the propensity to commit crime at or before a given age in Figure
II.3, we find a statistically significant effect for girls until age 19. After age 19, estimates are
again primarily negative but imprecise. Hence it seems that for girls, a higher school starting
age initially reduces crime and we see no catching up at older ages. Estimates for boys are
significant until age 22, after which they become very close to zero. For boys therefore, we
see a longer-lasting initial effect that eventually fade. The fading effects suggest that crime
at the extensive margin is aligned to key life events rather than age. If criminal behavior
instead was fixed to age, any effects of school starting age on crime should shift the crime-age
profile in vertical direction. However, Figure II.3 show that the effects fade in the long run
when old-for-graders and young-for-graders educational attainment and life-course converge,
which is consistent with a horizontal shift in the crime-age profile. Moreover, the fact that
the effects only approach zero from below suggest that the crime-age profile is shifted in
both vertical and horizontal direction.
The ’delay’ in crime for late starters is large relative to the mean. The share of girls
with any criminal charges at or before age 18, for example, is 0.054 among children born
30 days around January first. The effect of starting school at age 7.6, in comparison, is 1.5
percentage points reduction, or just below 30 % of the mean. For boys, the effect of school
starting at age 7.6 on criminal charges at age 18 is a 4 percentage point reduction, which
should be seen relative to a share of boys with criminal charges of 0.19. Appendix A, Table
A6 shows detailed estimation results where we gradually add control variables.
Our results are robust to standard robustness checks: extended bandwidth, ’donut hole’
71
strategies or including polynomials of the assignment variable. In addition, we perform a
robustness check computing bounds according to Nevo and Rosen (2012), which allows for
imperfect instruments. Our results are robust although the confidence bands are much wider.
Finally, results are unchanged by modelling SSA as a continuous variable instead of a binary
variable indicating late (7.6 years) as opposed to early (6.6 year) school start. Appendix
Figures IIA.7-IIA.9 report a selection of these robustness checks for the outcome crime at or
before a given age.
Types of Crime
In Figure II.4 we distinguish between types of crime. For girls the significant effects of school
starting age on crime at or before a given age are mainly driven by the impact on violent
crimes, while for boys the effects are primarily driven by the impact on property crimes,
although the effects on the two other categories of crime are significant for some ages.
72
Figure II.3: Estimation Results: Crime Across Age
((a)) Girls, at age
((b)) Girls, at or before age
((c)) Boys, at age
((d)) Boys, at or before age
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the probability
of crime at (left) and at or before (right) a given age. Cut-off dummy (January=1) used as instrument.
Conditioning set includes distance to cut-off, cohort fixed effects, and background characteristics (see Table
IIA.3). Dashed lines indicate 95% confidence intervals.
73
74
((e)) Boys, violence
((d)) Boys, property
((f)) Boys, other crime
((c)) Girls, other crime
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the probability of property, violent, and other crime at
(left) and at or before (right) a given age. Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohort fixed
effects, and background characteristics (see Table IIA.3). Dashed lines indicate 95% confidence intervals.
((b)) Girls, violence
((a)) Girls, property
Figure II.4: Estimation Results: Crime At or Before Age by Types of Crime
Grade Alignment
Just as Black et al. (2011) show in the case of test scores, the way we align crime is
extremely important for our conclusions. In particular, when age is held constant, the
differences between individuals born before or after the cut-off reflect differences in age at
school start, educational attainment and the probability to be enrolled in school. On the
other hand, when outcomes are aligned by grade levels, the differences reflect the effects of
age at school start, age at measurement, and time of measurement. Here we use the grade
level that individuals are expected to attend given their timing of school start.
Figure II.5 shows results that align children in terms of grades instead of age. The top
figures show the estimation results for crime at a given grade and the bottom figures show
the estimation results for crime at or before a given grade (conditional on the full set of
covariates). If the effects of school starting age only originated from delayed life-course,
aligning grade should nullify the effects. The figure shows that the age-gradient is indeed
smaller than for the age-aligned crime (though not significantly so); it nullifies the effect
at some but not all grade levels (top part of figure). For girls, the effect of school starting
age on crime is significantly negative for the two final years in comprehensive school (grade
levels 8 and 9). This corresponds to the significantly negative results at age 15 in our main
analysis above. For boys the effect is only significant at the transitions from one level to the
next in the educational cycle (grade levels 10 and 13). For none of the genders the effects on
the accumulated crime measure are significant (bottom part of figure). These results speak
in favor of our interpretation of the results presented in Figure II.3; being old-for-grade
primarily lowers crime due to changes in the timing of life events, though we also see some
signs of lower crime per se around the transitions.
75
Figure II.5: Estimation Results: Crime Across School Grade
((a)) Girls, p(crime) at grade
((b)) Boys, p(crime) at grade
((c)) Girls, p(crime) at or before grade
((d)) Boys, p(crime) at or before grade
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the probability
of crime at a given grade level (years since actual school start). Cut-off dummy (January=1) used as
instrument. Conditioning set includes distance to cut-off, cohort fixed effects, and background characteristics
(see Table IIA.3). Dashed lines indicate 95% confidence intervals.
Number of Criminal Charges
In Figure II.6, we consider the effects on crime at the intensive margin. The figure presents
the effects of increasing school starting age on the number of charges at or before a given age.
The estimates for girls are significant in the same age range as the results for the indicator
variable above.
This is likely because the majority of girls only commit very few crimes and it suggests
that the school starting age mainly influences the extensive margin. For boys, however, this
76
Figure II.6: Estimation Results: Number of Crimes At or Before Age
((a)) Girls
((b)) Boys
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the number of
crimes before or at a given age. Cut-off dummy (January=1) used as instrument. Conditioning set includes
distance to cut-off, cohort fixed effects, and background characteristics (see Table A3). Dashed lines indicate
95% confidence intervals.
exercise reveals interesting additional insights that were not clear from the simple indicator
analysis: estimates are much larger and effects last long into the twenties. In their midtwenties young men who started school later as a consequence of being born in January have
been charged with half a crime less than those who did not. This is a substantial effect
which has large consequences for both the offenders and potential victims. Moreover, these
large and persistent effects also show that on the intensive margin, the crime-age profile for
boys is more strongly related to age than the extensive margin crime-age profile which we
investigated earlier.25 Criminal behavior is thus not only determined by either age or key
events but by both in interaction; it matters at what age one is exposed to different key
events.
25
Even when we align outcomes by grade levels, we see a negative significant effect of being old-for-grade
on the accumulated number of crimes at grade levels 11 to 14 for boys (available on request).
77
5.3
Heterogeneity
In this section we first investigate characteristics of those individuals who comply with the instrument and then study whether effects vary by subgroups defined by parental background.
Complier Characteristics
In Table II.4 we summarize the average characteristics of the compliers (those who shift to
being old-for-grade because of a change in the value of the instrument; see Abadie (2003))
along with the average characteristics of the full sample as comparison. Families who change
the school start decision as a consequence of being born in January rather than December
tend to have more favorable characteristics: parents are more often living together, birth
weight is higher, and parents have higher education and stronger attachment to the labour
market.
Heterogeneity by Observable Characteristics
Figure II.7 presents heterogeneous effects. When we divide the sample according to mother’s
education, we find that the effect of school starting age on crime is numerically smaller and
insignificant when mothers have completed at least 12 years of education, which is what we
would expect. However, when we divide the sample according to the employment status
of the father, the picture is different: for girls, the effect of school starting age on crime
is numerically smaller and insignificant when fathers are not employed, while for boys, the
effects are of the same magnitude in either case.
78
Table II.4: Complier Characteristics
Variable
Immigrant
Parents married/cohabiting
Apgar score=9
Apgar score=8
Apgar score lower
Birth weight, grams
Gestational length, weeks
Mother:
Months of schooling
Completed HS or equivalent
Unemployed
Out of the labour force
Age at birth of first child
Father:
Months of schooling
Completed HS or equvalent
Unemployed
Out of the labour force
Girls
Sample Compliers
0.04
0.02
0.79
0.81
0.18
0.17
0.07
0.06
0.08
0.09
3349.43 3414.11
39.55
39.61
T-value
4.99∗∗∗
-2.72∗∗
1.39
2.74∗∗
-0.12
-5.90∗∗∗
-1.59
Boys
Sample Compliers
0.04
0.02
0.79
0.83
0.19
0.17
0.07
0.08
0.10
0.08
3473.43 3589.40
39.47
39.62
T-value
3.91∗∗∗
-3.45∗∗∗
1.25
-2,39∗
1.78
-7.21∗∗∗
-2.67∗∗
137.41
0.29
0.13
0.11
24.85
139.08
0.29
0.11
0.10
24.91
-2.49∗
0.08
3.00∗∗
1.29
-0.76
137.75
0.30
0.13
0.11
24.92
142.92
0.34
0.10∗
0.09
25.18
-5.87∗∗∗
-3.51∗∗∗
2,31∗
1.59
-2.18∗
140.15
0.19
0.08
0.06
143.26
0.18
0.07
0.04
-3.85∗∗∗
2.58∗∗
1,67
4.51∗∗∗
140.38
0.20
0.07
0.06
146,86
0.23
0.06
0.04
-5.71∗∗∗
-3.29∗∗∗
2.28∗
3.26∗∗
Note: Table shows selected mean characteristics of the full sample and compliers (i.e. those who are induced
to be old-for-grade because they are born on January 1st and not December 31st) following Abadie (2003).
Standard errors calculated from 100 bootstraps. p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗
5.4
Potential Mechanisms and Effects on Alternative Outcomes
This section first attempts to shed light on some of the different channels through which
school starting age may affect crime outcomes. Specifically, we further investigate the importance of incapacitation and also consider the role played by the relative age of peers as
in Black et al. (2013). We next address effects on an alternative range of outcomes. We
discussed above that parents may choose to enroll their child later in school even if there are
no long run effects on income, for example. Because school starting age is linked to grades,
it may also be linked to the quality of and consumption value associated with the type of
degree. Finally, municipality based variation in culture may impact on parents choices.
We first address incapacitation. In Figure IIA.6, we investigate how school starting age
affects crime across the week. For boys, the effect is driven by crime committed during
weekdays (Mon-Fri) and to a smaller extent by crime committed during weekends (SatSun). For girls, the effect during the weekdays is not statistically different from zero, while
79
80
((f)) Boys, mother ≥12yos
((e)) Boys, mother <12yos
((g)) Boys, father employed
((c)) Girls, father employed
((h)) Boys, father not empl.
((d)) Girls, father not empl.
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the probability of crime at or before a given age
by mothers education (≥12 years of education (40%) v. <12 years of education (60%)) and fathers employment status (employed (86%) v. not
employed (14%)). Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohort fixed effects, and background
characteristics (see Table A3). Dashed lines indicate 95% confidence intervals.
((b)) Girls, mother ≥12yos
((a)) Girls, mother <12yos
Figure II.7: Estimation Results: Crime At or Before Age by Types of Crime
it is for weekends until age 19. We interpret these findings as supportive of incapacitation
effect for boys throughout high school, which the age pattern of the main results already
pointed at above. For girls the effects are smaller and the mechanism is more subtle: the
effect is driven by violent crimes, crimes taking place on weekends and the effect dies out at
a younger age. Thus is appears that girls who are old-for-grade are less likely to be involved
in this type of crime while they are still in school.
Table IIA.8 analyzes the effect of the age of peers in line with Fredriksson and Öckert
(2005) and Black et al. (2013). Formally, we include the average age of peers in one’s
school in 8th grade as an additional control variable in our models of crime outcomes. To
handle endogeneity of the average age of peers, we instrument with the predicted average
age of peers had everybody started on time.26 We see that the mean age of peers has no
statistically significant effect on crime outcomes and that the effect of own school starting
age is completely unaffected by the inclusion of this extra control variable.27 This is in line
with the findings in the mentioned previous studies for Norway and Sweden.
We finally investigate other mechanisms that may explain why parents choose to postpone
school start even when effects on childrens primary long-term outcomes are moderate in size.
Table II.5 shows the estimated effects of being old-for-grade on alternative outcomes
such as grades and type of degree that may enhance the consumption value of school for
children and parents. We find that the impact of school starting age on standardized math
grades is statistically significant and large in magnitude.28 This is in line with previous
studies supporting large age-at-test effects (Crawford et al. (2010) and Black et al. (2011)).
If such grades make a difference for educational preferences or feasible choices, they may
influence long term outcomes. Indeed we do see that girls are more likely to enroll in one
of the selective and competitive Medical Schools, while boys tend to obtain a slightly longer
26
We impute average age of peers for observations with fewer than 10 other children enrolled at the school
in grade 8.
27
Compare the results presented in Table IIA.6 to those in Table IIA.8.
28
Danish grades are not affected (not shown).
81
Table II.5: Effects of School Starting Age on Other Outcomes
Variable
Grades
Math
Effort
N
Years of schooling, age 27
N
College enrollment
Med School
Law School
N
Distance to cut-off
Covariates
OLS
Girls
2SLS
2SLS
OLS
Boys
2SLS
2SLS
-0.028∗
(0.011)
-0.116∗∗∗
(0.011)
27,909
0.502∗∗∗
(0.101)
0.036
(0.090)
27,909
0.510∗∗∗
(0.093)
0.065
(0.088)
27,909
-0.052∗∗∗
(0.014)
-0.093∗∗∗
(0.015)
27,974
0.356∗
(0.145)
0.201
(0.150)
27,974
0.295∗∗∗
(0.135)
0.195
(0.146)
27,974
-0.448
(0.050)
11,045
-0.048
(0.136)
11,046
-0.045
(0.124)
11,047
-0.335
(0.052)
11,273
0.234
(0.147)
11,274
0.165
(0.135)
11,275
-0.007∗∗∗
(0.001)
-0.007∗∗∗
(0.002)
30,209
0.026∗
(0.011)
-0.013
(0.013)
30,209
X
0.026∗
(0.011)
-0.013
(0.013)
30,209
X
X
-0.006∗∗∗
(0.001)
-0.003∗∗∗
(0.001)
31,405
0.019
(0.011)
-0.006
(0.012)
31,405
X
0.019
(0.011)
-0.006
(0.012)
31,405
X
X
X
X
Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions of alternative
education outcomes. Cut-off dummy (January=1) used as instrument. Conditioning set includes
distance to cut-off, cohort fixed effects, and background characteristics (see Table II.A3).
p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗
education if they are old-for-grade as a consequence of being born on the other side of the
cut-off. Organisation (or effort) grades are not affected for boys or girls.
To investigate the variation in the enforcement of the stipulated school starting age across
municipalities we look at the distribution of predicted school starting age using a rich set
of observable characteristics against the actual school starting age across municipalities.
Results are available upon request. We find little relationship between the predicted and
actual school starting pattern on municipal level. Moreover, in 10% of all municipalities, less
than 68% (49%) of all boys (girls) born ±30 days from the cut-off are old-for-grade, while
in another 10% of all municipalities more than 84% (67%) are old-for-grade conditional
of observables. These numbers would be 50% if all families followed the stipulated school
starting rule. This suggests that local school start culture and legal enforcement of the
regulations may play a role for the parents decision.
82
6
Conclusion
This paper uses Danish register-based data to investigate the effect of school starting age
on crime-age profiles while using exogenous variation in school starting age generated by
administrative rules. We find that a higher school starting age lowers the propensity to
commit crime in youth. In addition, boys experience a persistent reduction in the number of
crimes committed. We show that crime at the extensive margin is largely driven by life events
whereas crime at the intensive margin is a complex function of both age and life-course.
Detailed studies of the age-profile of the effects indicate that the reductions to crime
are likely to be caused by an incapacitating effect of schooling, as those who start school
later graduate later. Although not directly testable, the pattern of results supports this
hypothesis: Boys who are old-for-grade are less likely to be charged during the period until
age 19 years, and this effect mainly stems from property crime. Girls who are old-for-grade
are less likely to be charged until age 16, and this effect stems from violent crimes. For boys
we find significant effects of school starting age on the accumulated number of crimes at
or before a given age throughout the twenties. For girls the effects on accumulated crime
measures die out which suggests that school starting age only influences the criminal debut.
For boys mainly property crime is reduced while for girls violent crime is reduced. We also
find that the effects are not caused by relative age of peers but by ones own school starting
age.
Our results suggest that increasing school starting age could lower crime more so for boys
than for girls. Yet, our findings do not necessarily suggest that school starting age should be
increased for everybody: our heterogeneity analyses show, for example, that children born to
parents with favorable characteristics gain relatively little from an increase in school starting
age. More fundamentally, we only analyze school start choice at the individual level and not
a policy change influencing all children.
83
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vol.4. Elsevier
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Economics and Statistics 94(3): 659-671.
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86
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87
A
Supplementary Results
Table IIA.1: Means of Selected Outcome Variables by Month of Birth
Criminal charge
(0/1) at age
15
16
17
18
19
20
21
22
23
24
25
26
27
December
0.021
0.016
0.015
0.014
0.021
0.021
0.021
0.022
0.020
0.020
0.023
0.019
0.019
Girls
January Difference N
0.017
0.003∗∗
48,546
0.015
0.001
48,546
0.013
0.002∗
48,546
0.013
0.001
48,546
0.020
0.001
43,668
0.022
-0.001
39,037
0.019
0.002
34,559
0.020
0.001
30,209
0.019
0.001
26,093
0.018
0.003
22,125
0.018
0.005∗
18,240
0.016
0.002
14,630
0.020
-0.001
11,045
December
0.042
0.058
0.093
0.095
0.114
0.117
0.112
0.105
0.101
0.093
0.085
0.081
0.080
Boys
January Difference
0.036
0.007∗∗∗
0.051
0.007∗∗∗
0.081
0.012∗∗∗
0.084
0.010∗∗∗
0.102
0.012∗∗∗
0.108
0.009∗∗
0.103
0.008∗∗
0.097
0.008
0.097
0.005
0.092
0.002
0.082
0.003
0.077
0.004
0.071
0.009
N
50,383
50,383
50,383
50,383
45,368
40,606
36,012
31,405
26,937
22,781
18,723
14,949
11,273
Criminal charge
(0/1) at or before age
15
16
17
18
19
20
21
22
23
24
25
26
27
December
0.021
0.035
0.047
0.057
0.073
0.086
0.098
0.109
0.116
0.125
0.136
0.140
0.142
Girls
January Difference
0.017
0.003∗∗∗
0.030
0.004∗∗
0.041
0.006∗∗∗
0.051
0.006∗∗∗
0.065
0.008∗∗∗
0.081
0.005
0.093
0.005
0.104
0.005
0.115
0.001
0.123
0.003
0.130
0.006
0.136
0.004
0.144 0.001
December
0.042
0.086
0.147
0.196
0.252
0.298
0.336
0.368
0.391
0.410
0.423
0.433
0.446
Boys
January Difference
0.036
0.007∗∗∗
0.076
0.010∗∗∗
0.133
0.014∗∗∗
0.181
0.015∗∗∗
0.234
0.018∗∗∗
0.282
0.017∗∗∗
0.318
0.018∗∗∗
0.348
0.020∗∗∗
0.374
0.018∗∗∗
0.395
0.016∗∗
0.410
0.013
0.424
0.009
0.433
0.013
N
50,383
50,383
50,383
50,383
45,368
40,606
36,012
31,405
26,937
22,781
18,723
14,949
11,273
N
48,546
48,546
48,546
48,546
43,668
39,037
34,559
30,209
26,093
22,125
18,240
14,630
11,045
Table shows fraction of individuals who have been charged for crime at (upper panel) and at or before (lower panel) a given age by gender.
Population of children born December 1981 to January 1993. T-test for difference in means across month of birth: p<0.05: ∗ , p<0.01: ∗∗ ,
p<0.001: ∗∗∗
88
Table IIA.2: Fraction of Students Being Retained at Each Grade Level
Grade level
Kindergarten
1st grade
2nd grade
3rd grade
4th grade
5th grade
6th grade
7th grade
8th grade
9th grade
Fraction being
delayed/retained
0.136
0.014
0.003
0.004
0.003
0.003
0.003
0.002
0.003
0.005
Note: Table shows fraction of children
who are retained / red-shirted at each
grade level.
Calculation based of grade level data
from 2007 and onwards.
89
Table IIA.3: Summary Statistics of the Sample
Variable
December
Immigrant
0.043
0.001
Parents married/cohabiting 0.788
0.003
Apgar score=9
0.181
0.002
Apgar score=8
0.071
0.002
Apgar score lower
0.084
0.002
Birth weight. grams
3341
3.987
Gestational length, weeks
39.564
0.012
Father:
Months of schooling
137.276
0.230
Completed HS or equvalent 0.292
0.003
Unemployed
0.130
0.002
Out of the labour force
0.104
0.002
Age at birth of first child
24.819
0.027
Father:
Months of schooling
139.736
0.281
Completed HS or equvalent 0.191
0.003
Unemployed
0.078
0.002
Out of the labour force
0.065
0.002
Observations
24,279
Girls
January
0.037
0.001
0.784
0.003
0.184
0.002
0.067
0.002
0.085
0.002
3358
3.813
39.543
0.011
T-value
0.006∗∗
0.004
-0.002
0.004
-0.001
-16.59∗∗
0.021
137.502
0.235
0.287
0.003
0.125
0.002
0.111
0.002
24.886
0.027
-0.226
140.507
0.277
0.190
0.003
0.077
0.002
0.062
0.002
24,267
-0.771
0.005
0.005
-0.006∗
-0.068
0.002
0.001
0.003
December
0.042
0.001
0.789
0.003
0.187
0.002
0.066
0.002
0.097
0.002
3466
4.152
39.482
0.012
Boys
January
0.034
0.001
0.792
0.003
0.184
0.002
0.070
0.002
0.094
0.002
3481
3.909
39.464
0.012
136.986
0.229
0.290
0.003
0.128
0.002
0.105
0.002
24.851
0.026
138.480
0.226
0.302
0.003
0.122
0.002
0.105
0.002
24.990
0.026
139.544
0.277
0.195
0.002
0.076
0.002
0.064
0.064
25,157
141.215
0.273
0.204
0.003
0.073
0.002
0.061
0.001
25,226
T-value
0.008∗∗∗
-0.003
0.004
-0.004
0.003
-15.02∗∗
0.019
-1.494∗∗∗
-0.013∗∗
0.006∗
0.000
-0.139∗∗∗
-1.671∗∗∗
-0.009∗
0.004
0.003
Note: Table shows summary statistics of the sample by month of birth and gender. Std. errors shown below
sample means. Columns T-value shows results from t-test of difference in sample means. p<0.05: ∗ , p<0.01:
∗∗
, p<0.001: ∗∗∗
90
Table IIA.4: First Stage Results (suppl. to Table II.3 in main text)
Variable
January=1
Days to cut-off, December
Days to cut-off, January
0.245∗∗∗
(0.008)
-0.005∗∗∗
(0.000)
0.003∗∗∗
(0.000)
Apgar score=9
Apgar score=8
Apgar score lower than 8
Immigrant
Birth weigth
Gestation length
Gestation length squared
Mother’s months of schooling
Mother’s months of schooling sq.
Father’s months of schooling
Father’s months of schooling sq.
Mother has compl. high school
Father has compl. high school
Mother unemployed
Mother out of labour force
Father unemployed
Father out of labour force
Mother’s age at first child
Parents are married
Girls
0.245∗∗∗ 0.244∗∗∗
(0.008)
(0.008)
-0.005∗∗∗ -0.005∗∗∗
(0.000)
(0.000)
0.003∗∗∗ 0.003∗∗∗
(0.000)
(0.000)
0.005
0.005
(0.005)
(0.005)
0.014
0.012
(0.008)
(0.008)
0.015
0.011
(0.008)
(0.008)
∗∗
-0.033
-0.041∗∗∗
(0.011)
(0.012)
-0.000∗∗∗ -0.000∗∗∗
(0.000)
(0.000)
-0.065∗∗∗ -0.070∗∗∗
(0.019)
(0.019)
0.001∗∗
0.001∗∗
(0.000)
(0.000)
0.001∗∗∗
(0.000)
-0.000∗∗∗
(0.000)
0.001∗∗
(0.000)
-0.000∗∗∗
(0.000)
-0.026∗∗∗
(0.006)
-0.065∗∗∗
(0.007)
0.020∗∗
(0.006)
0.002
(0.007)
0.017∗
(0.008)
0.009
(0.009)
0.002∗∗∗
(0.001)
0.001
(0.005)
Cut-off 1981-1982
Cut-off 1982-1983
Cut-off 1983-1984
Cut-off 1984-1985
Cut-off 1985-1986
Cut-off 1986-1987
Cut-off 1987-1988
Cut-off 1988-1989
Cut-off 1989-1990
Cut-off 1990-1981
Cut-off 1992-1993
Constant
N
0.714∗∗∗
(0.006)
48,546
2.294∗∗∗
(0.369)
48,546
2.282∗∗∗
(0.368)
48,546
0.246∗∗∗
(0.008)
-0.005∗∗∗
(0.000)
0.003∗∗∗
(0.000)
0.005
(0.005)
0.012
(0.008)
0.013
(0.008)
-0.067∗∗∗
(0.012)
-0.000∗∗∗
(0.000)
-0.068∗∗∗
(0.019)
0.001∗∗
(0.000)
0.001∗∗∗
(0.000)
-0.000∗∗∗
(0.000)
0.000∗
(0.000)
-0.000∗∗
(0.000)
-0.022∗∗∗
(0.006)
-0.060∗∗∗
(0.007)
0.017∗∗
(0.006)
-0.003
(0.007)
0.020∗
(0.008)
-0.002
(0.009)
0.000
(0.001)
0.004
(0.005)
-0.143∗∗∗
(0.010)
-0.132∗∗∗
(0.010)
-0.135∗∗∗
(0.010)
-0.145∗∗∗
(0.010)
-0.117∗∗∗
(0.010)
-0.088∗∗∗
(0.010)
-0.045∗∗∗
(0.010)
-0.029∗∗
(0.010)
-0.032∗∗∗
(0.010)
0.006
(0.009)
0.006
(0.009)
2.372∗∗∗
(0.365)
48,546
0.172∗∗∗
(0.007)
-0.005∗∗∗
(0.000)
0.001∗∗∗
(0.000)
0.872∗∗∗
(0.005)
50,383
Boys
0.171∗∗∗ 0.171∗∗∗
(0.007)
(0.007)
-0.005∗∗∗ -0.005∗∗∗
(0.000)
(0.000)
0.001∗∗∗ 0.001∗∗∗
(0.000)
(0.000)
-0.001
-0.001
(0.005)
(0.005)
0.003
0.001
(0.007)
(0.007)
0.006
0.004
(0.006)
(0.006)
∗∗∗
-0.097
-0.070∗∗∗
(0.009)
(0.011)
-0.000∗∗∗ -0.000∗∗∗
(0.000)
(0.000)
-0.035∗
-0.034∗
(0.017)
(0.017)
0.000
0.000
(0.000)
(0.000)
0.001∗∗∗
(0.000)
-0.000∗∗∗
(0.000)
0.001∗∗∗
(0.000)
-0.000∗∗
(0.000)
-0.005
(0.005)
-0.051∗∗∗
(0.006)
0.007
(0.006)
-0.025∗∗∗
(0.006)
0.001
(0.007)
0.009
(0.008)
0.004∗∗∗
(0.001)
0.002
(0.005)
1.707∗∗∗
(0.321)
50,383
1.540∗∗∗
(0.321)
50,383
0.171∗∗∗
(0.007)
-0.005∗∗∗
(0.000)
0.001∗∗∗
(0.000)
-0.003
(0.005)
-0.002
(0.007)
0.004
(0.006)
-0.097∗∗∗
(0.011)
-0.000∗∗∗
(0.000)
-0.031
(0.017)
0.000
(0.000)
0.001∗∗∗
(0.000)
-0.000∗∗∗
(0.000)
0.000∗∗
(0.000)
-0.000∗
(0.000)
-0.002
(0.005)
-0.048∗∗∗
(0.006)
0.005
(0.006)
-0.029∗∗∗
(0.006)
0.004
(0.007)
-0.000
(0.008)
0.002∗∗∗
(0.000)
0.005
(0.005)
-0.147∗∗∗
(0.009)
-0.136∗∗∗
(0.009)
-0.117∗∗∗
(0.009)
-0.109∗∗∗
(0.009)
-0.095∗∗∗
(0.009)
-0.070∗∗∗
(0.009)
-0.042∗∗∗
(0.009)
-0.010
(0.008)
-0.012
(0.008)
0.016∗
(0.008)
0.002
(0.008)
1.590∗∗∗
(0.318)
50,383
Note: Table shows results from linear regressions of indicators for starting school at age 7.6 instead of 6.6 while conditioning on cut-off
dummies (January=1), distance to cut-off, cohort fixed effects and background characteristics (see Table IIA.3). p<0.05: ∗ , p<0.01: ∗∗ ,
p<0.001: ∗∗∗
91
92
8th grade
Born
December 1996
January 1997
0.231∗∗∗ 0.215∗∗∗ 0.129∗∗∗
(0.023)
(0.023)
-0.005∗∗∗
-0.005∗∗∗
(0.001)
(0.001)
0.003∗∗∗
0.003∗∗∗
(0.001)
(0.001)
0.795∗∗∗
0.797∗∗∗
(0.017)
(0.017)
5,264
5,264
275.32
262.96
Girls
4th grade
Boys
Preschool 2nd grade 4th grade 8th grade
Born
Born
December 2000
December 1996
January 2001
January 1997
0.134∗∗∗
0.112∗∗∗
0.109∗∗∗
(0.017)
(0.018)
(0.018)
(0.018)
-0.004∗∗∗
-0.004∗∗∗
-0.004∗∗∗ -0.003∗∗∗
(0.001)
(0.001)
(0.001)
(0.001)
0.001∗∗∗
0.001∗∗∗
0.001∗∗∗
0.001∗∗∗
(0.001)
(0.001)
(0.001)
(0.001)
0.941∗∗∗
0.941∗∗∗
0.923∗∗∗
0.928∗∗∗
(0.013)
(0.013)
(0.013)
(0.013)
5,328
5,328
5,433
5,433
162.94
173.46
146.03
132.19
Note: Table shows results from linear regressions of indicators for starting school at age 7.6 instead of 6.6 while conditioning on cut-off dummies
(January=1), distance to cut-off, cohort fixed effects and background characteristics (see Table A3). School starting age is measured at different grade
levels in the period 2007-2013. p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗ .
N
F-value for January dummy
Constant
Days to cut-off, January
Days to cut-off, December
January=1
Preschool 2nd grade
Born
December 2000
January 2001
0.249∗∗∗
0.251∗∗∗
(0.024)
(0.024)
-0.005∗∗∗
-0.005∗∗∗
(0.001)
(0.001)
0.003∗∗∗
0.003∗∗∗
(0.001)
(0.001)
0.792∗∗∗
0.809∗∗∗
(0.016)
(0.017)
4,977
4,977
280.69
287.42
Table IIA.5: First Stage Result at Different Grade Levels
Table IIA.6: Detailed Estimation Results: Crime At or Before Age
Criminal charge
(0/1) at or before age
15
16
17
18
19
20
21
22
23
24
25
26
27
Distance to cut-off
Yearly cut-off FE
Covariates
OLS
-0.005∗∗∗
(0.001)
-0.003
(0.002)
-0.003
(0.002)
-0.003
(0.002)
-0.003
(0.002)
-0.001
(0.003)
-0.004
(0.003)
-0.005
(0.004)
-0.002
(0.004)
-0.001
(0.004)
-0.002
(0.005)
-0.004
(0.006)
0.001
(0.007)
X
X
Girls
2SLS
2SLS
-0.009∗ -0.008∗
(0.003) (0.003)
-0.011∗ -0.010∗
(0.004) (0.004)
-0.016∗∗ -0.015∗∗
(0.005) (0.005)
-0.017∗∗ -0.016∗∗
(0.006) (0.006)
-0.020∗∗ -0.019∗∗
(0.007) (0.007)
-0.012
-0.011
(0.008) (0.007)
-0.012
-0.011
(0.008) (0.008)
-0.012
-0.011
(0.009) (0.009)
-0.002
-0.000
(0.010) (0.010)
-0.006
-0.005
(0.012) (0.011)
-0.015
-0.013
(0.013) (0.013)
-0.011
-0.010
(0.015) (0.014)
0.004
0.004
(0.017) (0.017)
X
X
X
X
X
N
48,546
48,546
48,546
48,546
43,668
39,037
34,559
30,209
26,093
22,125
18,240
14,630
11,045
OLS
-0.005∗
(0.002)
-0.009∗∗∗
(0.003)
-0.006
(0.004)
-0.002
(0.004)
0.001
(0.005)
0.000
(0.005)
0.004
(0.005)
0.004
(0.006)
0.008
(0.006)
0.005
(0.007)
0.003
(0.008)
0.005
(0.009)
0.004
(0.010)
X
X
Boys
2SLS
2SLS
-0.025∗∗∗ -0.019∗∗
(0.007) (0.006)
-0.035∗∗∗ -0.025∗∗
(0.009) (0.009)
-0.051∗∗∗ -0.037∗∗
(0.012) (0.012)
-0.054∗∗∗ -0.038∗∗
(0.013) (0.013)
-0.066∗∗∗ -0.045∗∗
(0.015) (0.015)
-0.058∗∗∗ -0.036∗
(0.016) (0.016)
-0.061∗∗∗ -0.039∗
(0.017) (0.017)
-0.068∗∗∗ -0.043∗
(0.019) (0.018)
-0.057∗∗
-0.035
(0.020) (0.019)
-0.049∗
-0.030
(0.021) (0.020)
-0.038
-0.018
(0.023) (0.022)
-0.026
-0.006
(0.025) (0.024)
-0.036
-0.019
(0.028) (0.027)
X
X
X
X
X
N
50,383
50,383
50,383
50,383
45,368
40,606
36,012
31,405
26,937
22,781
18,723
14,949
11,273
Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions on crime at or before a given age.
Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohort fixed effects, and
background characteristics (see Table A3). p<0.10: + , p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗
93
Table IIA.7: Detailed Estimation Results: Crime At Age
Criminal charge
(0/1) at age
15
16
17
18
19
20
21
22
23
24
25
26
27
Distance to cut-off
Yearly cut-off FE
Covariates
OLS
-0.005∗∗∗
(0.001)
0.002
(0.001)
0.001
(0.001)
0.001
(0.001)
0.001
(0.001)
0.002
(0.002)
-0.001
(0.002)
0.001
(0.002)
0.002
(0.002)
-0.001
(0.002)
-0.000
(0.002)
-0.000
(0.002)
-0.000
(0.003)
X
X
Girls
2SLS
2SLS
-0.009∗ -0.008∗
(0.003) (0.003)
-0.003 -0.003
(0.003) (0.003)
-0.006∗ -0.006∗
(0.003) (0.003)
-0.002 -0.002
(0.003) (0.003)
-0.002 -0.002
(0.004) (0.004)
0.003
0.003
(0.004) (0.004)
-0.004 -0.004
(0.004) (0.004)
-0.003 -0.002
(0.004) (0.004)
-0.002 -0.002
(0.005) (0.004)
-0.007 -0.007
(0.005) (0.005)
-0.012∗ -0.011∗
(0.005) (0.005)
-0.006 -0.006
(0.006) (0.006)
0.002
0.002
(0.007) (0.007)
X
X
X
X
X
N
48,546
48,546
48,546
48,546
43,668
39,037
34,559
30,209
26,093
22,125
18,240
14,630
11,045
OLS
-0.005∗
(0.002)
-0.007∗∗
(0.002)
0.001
(0.003)
0.004
(0.003)
0.002
(0.003)
0.002
(0.004)
0.011∗∗
(0.004)
0.003
(0.004)
0.006
(0.004)
0.009∗
(0.004)
0.005
(0.004)
-0.002
(0.005)
0.002
(0.005)
X
X
Boys
2SLS
2SLS
-0.025∗∗∗ -0.019∗∗
(0.007)
(0.006)
-0.026∗∗∗ -0.019∗
(0.008)
(0.008)
-0.044∗∗∗ -0.036∗∗∗
(0.010)
(0.009)
-0.039∗∗∗ -0.030∗∗
(0.010)
(0.010)
-0.045∗∗∗ -0.033∗∗
(0.011)
(0.011)
-0.031∗∗
-0.021
(0.011)
(0.011)
-0.029∗
-0.019
(0.012)
(0.011)
-0.028∗
-0.018
(0.012)
(0.012)
-0.015
-0.005
(0.012)
(0.012)
-0.005
0.003
(0.012)
(0.012)
-0.009
-0.001
(0.013)
(0.013)
-0.011
-0.003
(0.014)
(0.013)
-0.026
-0.020
(0.015)
(0.015)
X
X
X
X
X
N
50,383
50,383
50,383
50,383
45,368
40,606
36,012
31,405
26,937
22,781
18,723
14,494
11,273
Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions of crime at or before a
given age. Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohort
fixed effects, and background characteristics (see Table A3). p<0.10: + , p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗
94
Table IIA.8: Absolute and Relative Effects of being ’Old-for-Grade’: Crime At or Before
Age
Criminal charge
(0/1) at or before age
15
16
17
18
19
20
21
22
23
24
25
26
27
Distance to cut-off
Yearly cut-off FE
Covariates
Old-for-grade
-0.008∗
(0.003
-0.010∗
(0.004)
-0.015∗∗
(0.005)
-0.016∗∗
(0.006)
-0.018∗∗
(0.007)
-0.010
(0.008)
-0.009
(0.00)8
-0.010
(0.009)
0.001
(0.010)
-0.002
(0.012)
-0.008
(0.013)
-0.006
(0.015)
0.005
(0.018)
X
X
X
Girls
Peer age
0.014
(0.028)
-0.033
(0.036)
-0.011
(0.042)
-0.006
(0.046)
-0.060
(0.054)
-0.063
(0.061)
-0.113
(0.068)
-0.116
(0.076)
-0.075
(0.083)
-0.124
(0.094)
-0.230
(0.102)
-0.152∗
(0.113)
-0.030
(0.130)
X
N
48,546
48,546
48,546
48,546
43,668
39,037
34,559
30,209
26,093
22,125
18,240
14,630
11,045
Old-for-grade
-0.019∗
(0.006)
-0.025∗
(0.009)
-0.037∗∗
(0.012)
-0.038∗∗
(0.013)
-0.046∗∗
(0.015)
-0.037∗
(0.016)
-0.041∗
(0.017)
-0.044∗
(0.018)
-0.036
(0.019)
-0.030
(0.021)
-0.017
(0.022)
0.005
(0.025)
-0.009
(0.028)
X
X
X
Boys
Peer age
0.002
(0.044)
-0.017
(0.062)
-0.058
(0.078)
0.049
(0.088)
0.116
(0.101)
0.065
(0.112)
0.093
(0.119)
0.027
(0.129)
0.054
(0.136)
0.022
(0.146)
-0.058
(0.159)
-0.321
(0.177)
-0.321
(0.201)
N
50,383
50,383
50,383
50,383
45,368
40,606
36,012
31,405
26,937
22,781
18,723
14,949
11,273
X
Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions on crime at or before
a given age. Cut-off dummy (January=1) used as instrument for own school starting decision, predicted school
starting age of peers if compliant with rules used as instrument for average peer age. In addition to average peer
age, conditioning set includes distance to cut-off, cohort fixed effects, and background characteristics (see Table
A3). p<0.05: ∗ , p<0.01: ∗∗ , p<0.001: ∗∗∗
95
Figure IIA.1: Age 4 Social and Emotional Difficulties Among Punctual and Late School
Starters
Note: Figure shows kernel density densities of social and emotional difficulties scores at age 4 by school
starting age. Data stem from the Danish Longitudinal Survey of Children that surveys children born in
September and October of 1995. ’Punctual school starters’ obey the rules and start school when they are
supposed to start according to the rules, while late school starters have been granted an exemption.
96
97
((d)) Boys, age 27
((b)) Girls, age 27
Note: Figures show Crime-Age Profiles: The fraction of individuals who have been charged with a crime at (left) and at or before (right) a given age.
Population of children born 1981-1993
((c)) Boys, age 19
((a)) Girls, age 19
Figure IIA.2: Crime At or Before Age
98
((d)) Boys, age 27
((b)) Girls, age 27
Note: Figures show scatterplots of crime at or before a given age (19 and 27) by date of birth. The solid line is a local polynomial smoothed line and
the corresponding dashed lines indicate 95% confidence intervals.
((c)) Boys, age 19
((a)) Girls, age 19
Figure IIA.3: Crime At or Before Age
Figure IIA.4: Mean Birthweight for Girls (bottom) and Boy (top) by Date of Birth
Note: Figure shows average birth weight measured in grams, by date of birth and gender. Population of
children born in December or January 1981-1993.
99
Figure IIA.5: Estimation Results: Years of Completed Schooling
((a)) Girls
((b)) Boys
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on years of
completed schooling at a given age. Cut-off dummy (January=1) used as instrument. Conditioning set
includes distance to cut-off, cohort fixed effects, and background characteristics (see Table A3). Dashed
lines indicate 95% confidence intervals.
100
101
((d)) Boys, weekend
((c)) Girls, weekend
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the probability of crime by weekdays (Mon-Fri) and
weekends (Sat-Sun). Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohort fixed effects, and
background characteristics (see Table A3). Dashed lines indicate 95% confidence intervals.
((b)) Boys, weekday
((a)) Girls, weekday
Figure IIA.6: Estimation Results: Crime At or Before Age by Weekday/Weekend
Figure IIA.7: Estimation Results: Crime At or Before Age by Continuous School Starting
Age
((a)) Girls
((b)) Boys
Note: Figures show the estimated effects of continuous school starting age based on 2SLS regressions on the
probability of crime at or before a given age. Cut-off dummy (January=1) used as instrument. Conditioning
set includes distance to cut-off, cohort fixed effects, and background characteristics (see Table A3). Dashed
lines indicate 95% confidence intervals.
102
103
((e)) Boys, ± 60 days
((d)) Boys, ± 30 days
((f)) Boys, ± 90 days
((c)) Girls, ± 90 days
Note: Figures show the estimated effects of being old-for-grade based on 2SLS regressions on the probability of crime at or before a given age using
varying sample bandwidths. Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohort fixed effects, and
background characteristics (see Table A3). Dashed lines indicate 95% confidence intervals.
((b)) Girls, ± 60 days
((a)) Girls, ± 30 days
Figure IIA.8: Estimation Results: Crime At or Before Age, Extended Bandwidth
Figure IIA.9: Estimation Results: Crime At or Before Age with Nevo-Rosen Bounds
((a)) Girls
((b)) Boys
Note: Figures show estimated effects of being old-for-grade on crime at or before a given age applying Nevo Rosen bounds (Nevo and Rosen (2012)) and using a uniform cut-off as instrument and no covariates. Because
the covariance between the instrument (here defined as January=1) and the treatment (old-for-grade) is
positive σOf G,Z , as being born in January predicts a higher probability of being old-for-grade, the bounds
are given as Bounds B ∗ =
σOf G (σOf G,Z −σZ σOf G )
σOf G σZ,y −σOf G σOf G,y ]
σOf G (σOf G,Z −σZ σOf G )
[ σOf G σZ,y −σOf G σOf G,y , βZIV ]
[βZIV ,
if σOf G,Z > 0
if σOf G,Z < 0
Where Z denotes the instrument, y crime at or before a given age ,and Of G a binary indicator of being
old-for-grade. Standard errors computed from 50 bootstraps
104
Part III
The Effects of Admissions to
Psychiatric Hospitals
105
The effects of admissions to psychiatric hospitals
Rasmus Landersø and Peter Fallesen?
Abstract
his paper studies the effects of an admission to a psychiatric hospital on subsequent
psychiatric treatments, self-inflicted harm, crime, and labour market outcomes. To
circumvent non-random selection into hospital admission we use a measure of hospital
occupancy rates the weeks prior to a patient’s first contact with a psychiatric hospital
as an instrument. Admission reduces crime rates and self-harming behaviour substantially in the short run, but leads to higher re-admission rates and lower labour market
attachment in the long run. Effects are heterogeneous across observable and unobserveable patient characteristics. We also identify positive externalities of admissions
on spouses’ employment rates.
Keywords: crime, inpatient care, labour market, mental health, treatment effects
JEL: I10, J10, K42
The authors thank Richard Breen, Mette Ejrnæs, Jane Greve, Eskil Heinesen, Helena Skyt Nielsen, Marianne
Simonsen, Torben Tranæs, Christopher Wildeman, Hanne-Lise Falgreen Eriksen, Erik Roj Larsen, Bas van
der Klaauw, Peter Sandholt Jensen, Anna Piil Damm, and seminar participants at the Health Economics
Workshop at University of Chicago, EEA Conference 2014, Labour and Public Policy Seminar at Aarhus
University, the Danish National Centre for Social Research, SDU Applied Micro Workshop, RES 2015
conference, and the SPP 1764 conference
?
Rockwool Foundation Research Unit, University of Copenhagen
106
1
Introduction
Psychiatric disorders are costly for society and may have substantial negative consequences
for both the patients and their relatives. Psychiatric patients have lower labour market
attachment, more somatic health problems, and higher crime rates than the general population, and may burden their next of kin (e.g. Ettner et al. , 1997; Greve & Nielsen, 2013;
Kupers & Toch, 1999; Noh & Turner, 1987). Finding the optimal strategy for treating psychiatric disorders will therefore reduce strain on society, patients, and their families. During
the past decades, most OECD countries have downsized treatment capacity at psychiatric
hospitals substantially (WHO, 2011a), even though little is known about the causal effects
of admitting a patient to a psychiatric hospital on the patient’s later outcomes. Hence, the
consequences of lowering hospital admission rates are largely unknown.
Our study examines the effects of admitting a patient as an inpatient upon first contact
with psychiatric health care on the patient’s subsequent contacts and admissions to psychiatric hospitals, criminal and self-harming behaviour, and on the patients’ and their spouses’
labour market outcomes. We use a sample of 24,277 adults aged 18–45 who had their first
contact with a psychiatric hospital between 1999 and 2001. We use Danish administrative
data containing information on all contacts to mental health facilities for all Danish citizens.
We address the fundamental differences between the counterfactual outcomes of individuals who are admitted as inpatients and individuals who are not admitted by using an
instrumental variable: the intensity of patient contacts to a hospital during the weeks before
an individual’s first contact, which serves as a proxy for a given hospital’s occupancy rate.
By exploiting the variation in contact intensity we can identify the causal effect of admitting
individuals as inpatients at first contact relative to not providing immediate care.
Our results show that immediate hospital admissions have large but ambiguous effects.
In the short run, inpatient care reduces the patients’ adverse behaviour. In particular, we
107
find that inpatient treatment leads to large reductions in crime shortly after the admission.
Admitting an extra 100 marginal patients to inpatient care at first contact leads to 10 fewer
crimes during the subsequent six months. We show that the reduction in crime is caused by
incapacitation during the period of the most severe mental distress. In a similar vein, we also
find that inpatient admission lowers the risk of hospitalisation for health issues likely resulting
from self-harming behaviour in the months following admission. Thus, failing to admit a
patient or only offering outpatient care leaves the patient’s immediate needs unaddressed1
resulting in large negative externalities.
In the longer run, however, people admitted to inpatient care experience a higher degree
of institutionalisation, which is likely to leave them with poorer long term labour market
outcomes. In line with the previous medical literature, we find that an inpatient admission increases the probability of subsequent admission to psychiatric treatment facilities
by as much as 20 percentage points. There is on average no significant increase in patients’ subsequent number of contacts to the psychiatric system. We therefore attribute
the increase in admission rates to an institutionalising effect. In addition, we show that
inpatient admission reduces employment and labour market attachment further strengthening the institutionalisation hypothesis. We also identify large effect heterogeneity across
both observable and unobservable characteristics. Males experience the largest reductions
to crime whereas females experience the largest increase in re-admissions and reductions to
labour market attachment. By estimating Marginal Treatment Effects we find that patients
with the largest unobservable gains from treatment (more serious conditions) experience the
largest reductions to crime and self-harming behaviour, whereas patients with the smallest
unobservable gains (less serious conditions) experience the largest increase in the probability
of re-admission. Finally, we show that inpatient admission increases the employment rates
of spouses, most likely because hospital admissions reduces the strain otherwise experienced
when living with and being the main caretaker of a(n) (untreated) psychiatric patient.
1
A concern voiced also in an editorial in The Lancet (2011).
108
We contribute to the existing literature in four ways. First, we consider the effects of the
foremost assessment made when a patient contacts a psychiatric hospital; namely whether
to immediately admit and treat the patient or not. To our knowledge we are the first to
investigate this pivotal point. Patients may be affected by in-, out- or day patient treatments
later on, but any subsequent effects of one or the other form of psychiatric treatment are
conditional on the foremost decision. Second, we consider a wider range of outcomes, such
as labour market outcomes, self-harming behaviour, and crime, compared to the existing
literature that focuses on re-admissions and subjective well-being questionnaires. Third, we
use a rich data set based on administrative register data which provides us with a sample size
that is more than 20 times larger than used by previous studies. Fourth, we consider effects
on externalities by studying how admittance affects crime rates and patients’ spouses.2
The article progresses as follows: Section 2 introduces the study’s background, relevant
literature, and the institutional framework in Denmark. Section 3 describes the data and
the construction of the main variables and section 4 describes the econometric framework.
Section 5 presents the results. Finally, section 6 concludes.
2
Background
Psychiatric treatment facilities in the Western world have seen substantially downsizing over
the past decades.3 Few will cast doubt on the improvements in psychiatric treatments in
this period; both with respect to civil rights and quality of treatment.4 However, the vast
2
We do not explicitly address the degree to which various treatment forms reduce core symptoms of
psychiatric illnesses or improve the quality of life for patients, but only the derived effects on realised
outcomes.
3
Since the 1960s a comprehensive change has taken place in the psychiatric treatment systems in the
majority of developed countries.The change is sometimes labelled the third revolution of psychiatry (Castel
et al. , 1982). As a result, psychiatric treatment has moved out of the hospitals and into the community
(Goodwin, 1997; Killaspy, 2006; Oosterhuis, 2005). Psychiatric health care today has its focus on on treating
the patients core symptoms, and no longer only on being a safe haven for the patients (Castel et al. , 1982).
Advances in psychopharmacological treatments and an increasing focus on the benefits from ongoing contact
with the familiar community, family, and friends during treatment have contributed highly to these changes.
See also Knowles (2005) for a discussion of the negative consequences of the downsizing of inpatient care.
4
See Frank & Glied (2006) and Gijswijt-Hofstra et al. (2005) for in-depth discussions.
109
changes raise a central question: Has the move away from treatment in hospitals and the
reductions of hospital beds reached its limits or even gone too far? Are patients, whose
illnesses are of a nature where immediate inpatient care would be the best option, instead
receiving outpatient care, only medical treatment, or no treatment at all?
A substantial body of literature has convincingly shown that individuals with psychiatric
disorders fare significantly worse compared to the average population, measured on a wide
range of outcomes. Psychiatric disorders reduce subsequent employment rates and earnings
(Ettner et al. , 1997), and people with mental disorders are heavily overrepresented in crime
statistics (Fazel et al. , 2015) and jails and prisons (Kupers & Toch, 1999). A recent Danish
study (Greve & Nielsen, 2013) find similar results for schizophrenics in Denmark. Several
studies have investigated the demand, cost and determinants of different types of psychiatric
care (e.g. Davis & Russell, 1972; Scheffler & Watts, 1986; Vitikainen et al. , 2010).5 We
add to the literature by taking a first step in investigating the optimal response to mental
illnesses and focusing on the social consequences rather than on demand and supply issues.
Several medical studies have investigated the effects of inpatient versus outpatient or
day-patient treatment in adult psychiatry on recidivism and well-being (see Marshall et al. ,
2009; Shek et al. , 2010, for recent reviews). Except for an increased tendency to higher readmission rates for inpatients, the literature generally finds few or no differences between the
effects of inpatient and day treatments. The lack of significant findings may be driven by the
small sample sizes investigated,6 which also reduce the external validity of the studies.7 In
addition, these studies only consider individuals who actually receive some form of treatment.
Instead, we evaluate the effects of inpatient admission for all individuals who seek treatment.
5
See Frank & McGuire (2000) for a review of the literature on mental health economics.
One exception is Kallert et al. (2007) who use a cross country RCT with a sample size of 1,055 to
investigate the differences between the outcomes of inpatient and day patients. As for the remaining studies,
they find few significant differences between the two alternatives, and only consider the outcomes between
two types of treatment instead of the full sample of patients seeking treatment.
7
For an example see Creed et al. (1990) who find no differences between inpatient and day treatments
using a U.K. RCT with a sample size of 89 individuals.
6
110
Although previous work has found little evidence on the effects of admittance, there are
several reasons to suspect that admittance directly and indirectly can affect later health
and social outcomes; especially when studying the effect of the first admittance. Goffman
(1961) argued that mental patients have careers, just as Dahl et al. (2013) show with regard
to welfare recipients. That is, patients experience a trajectory through the mental health
system, which marks them as mentally ill. The pivotal moment in such a career may very
well be the treatment a patient receives at initial contact, since it marks the beginning of the
mental health system’s record of that patient and may affect the threshold for subsequent
admittances for that patient. Taking a patient in immediate mental distress to inpatient
care might also alleviate public safety risks through incapacitation (see, e.g. Anderson, 2014;
Appelbaum, 2001; Jacob & Lefgren, 2003; Winerip, 1999), for example of patients whose
mental illness makes them a threat to themselves. If the psychiatric system fails to identify
all patients with illnesses that makes them prone to commit crime if untreated, lowering the
number of inpatient beds could directly lead to an increase in criminality.
2.1 Institutional framework - mental health care in Denmark
In Denmark, basic health care (including treatment at psychiatric hospitals) is fully publicly
funded and thus not directly affected by individual credit constraints. A person with psychiatric problems may gain access to psychiatric treatment in two ways. First, the person can
contact an emergency room at a hospital. Alternatively, the patient’s general practitioner
(GP) may refer him or her (the GP serves as the gatekeeper to the entire public health care
sector).8 If the GP assesses that the patient should receive treatment from trained psychiatrists, the GP has three options: (1) refer the patient to a psychiatric practitioner (the
8
GPs may also prescribe most antidepressants themselves, but only do so in mild cases (WHO, 2011b).
The Danish prescription practice stands in contrast to e.g. the practice in the U.S. In the U.S. GPs prescribe
most psychopharmaceuticals such as antidepressants (Mojtabai & Olfson, 2011).
111
mildest cases); (2) refer the patient to psychiatric hospital (the mild to severe cases); (3) or
admit the patient to a psychiatric hospital by force (the most severe cases).9
The publicly funded psychiatric treatment regime consists of inpatient treatments and
outpatient treatments. Inpatient treatment takes place at hospitals or at designated facilities
and outpatient care in the patient’s home or local community.10 We refer to Appendix B for
a brief overview of the trends in number of inpatient beds and patients.
3
Data
This section describes the construction of the data and the main variables. We obtain
information on contacts with psychiatric care facilities from the Danish national psychiatric
register. The register contains information on all contacts with public Danish psychiatric
facilities from 1980 to 2011 including date of initial contact, treatment (if any), location,
hospital and ward of contact, the date of admission, type of admission if any (inpatient
24-hour, inpatient part time, and from 1996 also information on outpatient), and diagnoses.
From the psychiatric register we identify the time of first contact with the psychiatric care
system and the corresponding relevant information. Each observation contains a unique
individual identifier (and a unique case number), which allows us to link information on
gender, date of birth, country of origin, and educational attainment using demographic and
educational registers. We also link individuals to the labour market register and the criminal
registers. The demographic registers also include unique identifiers of parents and spouses,
9
In 2000, one third of all psychiatric patients received treatment from a specialist, with the last twothirds receiving treatment from a public psychiatric treatment facility (Bengtsson, 2011). An unknown,
but relatively small group of patients, received treatment from a privately funded psychiatric practitioner
(Bengtsson, 2011).
10
Both types were until 2004 governed and funded by individual counties. The outpatient treatments where the individuals are treated while remaining at home or in residential care - are coordinated by local
social services together with psychiatrists and funded and governed by the individual municipalities. During
the period in question, Denmark consisted of 279 municipalities and 13 counties. Hoff et al. (2012) provide
an overview of the Danish system compared to the English and the Dutch. With the exception of the funding
schemes, these two strands of treatment possibilities resemble those of many OECD countries, including the
U.S. and the U.K.
112
Table III.1: Average Treatment Length
Total length of treatment as inpatient
Outpatient treatment at psych. hospitals
Total length of treatment as outpatient
Observations
Not admitted
0.502
(0.500)
68.398
(152.048)
16928
Admitted
30.203
(76.790)
7349
Note: Table shows the means and std. dev. of treatment status. Standard deviation in parentheses.
which allows us to identify parental information on educational attainment, age, and previous
contacts with psychiatric facilities, as well as spouses’ labour market outcomes. We limit
our sample to individuals who have their first contact between the age of 18 and 45 from
1999 to 2001 as we neither wish to focus on child or geriatric psychiatric treatments.11 This
results in a final sample of 24,277 individuals.12
Treatment Variable
We define our main explanatory variable of interest as a dummy variable which is equal
to 1 if an individual is admitted either as a 24-hour or part-time patient to a psychiatric
care facility and 0 otherwise. Importantly, 0 comprises all outcomes where the individual
is not immediately admitted to the facility but sent home. This includes both scheduled
outpatient treatments and complete rejections, as Table III.1 shows by summarizing the
treatment characteristics for those who are admitted and the subsequent treatment statuses
of those who are not admitted upon first contact.
11
Danish psychiatric facilities have been the focus of gradual budget cuts and capacity reductions during
the past two decades, especially with respect to inpatient treatments (Bengtsson, 2011). However, the
period between 1998 and 2001 is a relatively stable period without any major reforms and reductions on
adult psychiatric treatment possibilities. Different conditions apply for child and geriatric patients relative
to the average adult population once in contact with a psychiatric care facility.
12
We also discard individuals who are diagnosed with mental retardation, dementia, or disorders of early
psychological development (because these patient groups suffer from chronic disorders and have little or no
labour market attachment), and individuals who are diagnosed with eating disorders (mainly teenage girls)
or non-organic sexual dysfunctions in order to obtain a more homogeneous sample. Finally, we exclude
individuals who contact the few countryside treatment facilities that only treat 10-50 individuals per year.
113
Table III.1 presents data on the 7,349 people who are admitted as inpatients and on the
16,928 who are not admitted as inpatients over the study period. We denote the former the
treatment group and the latter the control group. The average admission length is 30.2 days
for those admitted as inpatients (treatment=1). Of those who are not admitted as inpatients
(treatment=0), around 50 percent receive treatment as outpatients. Table III.1 also shows
that the average treatment length is larger for outpatients than inpatients, because many of
those who are admitted as inpatients continue into outpatient treatment once deemed ready.
Lengths of subsequent outpatient treatments for inpatients are not included in the summary
measure in Table III.1.
Sample Descriptives
The first three columns of Table III.2 summarise the characteristics of the overall sample
and the sample divided by whether they individuals received immediate inpatient treatment
or not. The fourth column shows the corresponding average characteristics for a random
sample of the Danish population between ages 18 and 45.13
In Table III.2, columns 2 and 3 show that more women than men contact psychiatric
hospitals, but men are more often admitted to inpatient care at first contact. Admitted
patients are also older, more likely to have committed a crime previously, have higher unemployment rates, and lower welfare dependency the year prior. In addition, admitted patients
have parents with less education than individuals who are not admitted. Individuals who
suffer from either disorders associated with substance use, psychosis or schizophrenia, or
adult-onset affective disorders are more likely to be admitted. Individuals who suffer from
nervous or stress related disorders, personality disorders, or pre-adult onset affective or emotional disorders are less likely to be admitted. When comparing column 2 to column 5 we see
large differences between the individuals who contact psychiatric hospitals and the average
13
The random sample has been weighted by the age-distribution of our main sample for comparison.
114
Table III.2: Descriptive Statistics for Sample
Full sample Not admitted
Admitted
Representative sample
0.463
0.423
0.555
0.509
(0.499)
(0.494)
(0.497)
(0.500)
Immigrant
0.126
0.126
0.124
0.081
(0.331)
(0.332)
(0.330)
(0.273)
Age at admission
31.141
30.821
31.879
31.995
(7.535)
(7.522)
(7.515)
(7.794)
Gross income in year -1 (2000DKK)
194426.591
193501.875
196556.785
264456.310
(130354.872) (131851.746) (126822.629)
(207096.723)
Committed crime prior to year
0.280
0.255
0.337
0.138
(0.449)
(0.436)
(0.473)
(0.345)
Unemployment degree in year -1
0.183
0.179
0.193
0.071
(0.305)
(0.304)
(0.308)
(0.199)
Welfare dependency in year -1
0.334
0.344
0.311
0.215
(0.383)
(0.387)
(0.371)
(0.347)
Mother’s months of schooling
125.239
126.928
121.348
125.526
(34.248)
(34.427)
(33.510)
(38.394)
Father’s months of schooling
135.892
137.235
132.801
137.650
(35.023)
(34.924)
(35.058)
(40.440)
Mother’s age at birth
26.206
26.215
26.188
25.360
(5.035)
(5.007)
(5.099)
(5.164)
Admitted in own municipality
0.164
0.166
0.157
(0.370)
(0.372)
(0.364)
Admitted in Copenhagen
0.193
0.207
0.161
(0.395)
(0.405)
(0.368)
Admitted in metropolitan area
0.152
0.150
0.158
(0.359)
(0.357)
(0.365)
Disorder associated with substance use
0.152
0.125
0.213
(0.359)
(0.331)
(0.410)
Psychosis, schizophrenia
0.074
0.037
0.161
(0.262)
(0.188)
(0.368)
Affective disorder
0.199
0.180
0.243
(0.399)
(0.384)
(0.429)
Nervous or stress-related
0.444
0.504
0.305
(0.497)
(0.500)
(0.460)
Personality disorder
0.103
0.118
0.071
(0.305)
(0.322)
(0.256)
Affective/emotionel, pre-adult origin
0.028
0.036
0.007
(0.164)
(0.187)
(0.086)
Admitted
0.303
0.000
1.000
(0.459)
(0.000)
(0.000)
Observations
24277
16928
7349
716411
Note: Table shows the means and std. dev. of covariates for the full sample and divided by treatment status.
T-tests of differences between inpatient and outpatient sub-samples. Far right coloumn shows summary statistics
of a randomly selected sample of individuals aged between 18-45 in 1999-2001.
Male
115
population. Individuals who seek access to psychiatric treatment have weaker labour market
attachment and lower income, come from more disadvantaged backgrounds, and are more
likely to have committed crime.
Outcome Variables
Below we introduce the outcome variables: later psychiatric inpatient admissions and contacts, criminal convictions, self-harming behaviour, and labour market outcomes. We measure all variables for the first three years after the initial contact with a psychiatric hospital.
We use the psychiatric register to identify the probability of subsequent contacts and
admissions to psychiatric hospitals. We define subsequent contact as appearing in the psychiatric registers with at least one new entry after the date of discharge for admitted patients
or date of first contact for not admitted patients. We define subsequent inpatient admission
as at least one admission taking place after first contact (and in the case of inpatient admission after first discharge). This is by construction a subset of contacts. We also link the
data to the criminal registers containing criminal convictions, charges, and incarcerations.
We combine the exact date of contact with the exact date of committing a criminal act and
we define crimes as convictions with no ongoing appeals. The combined information allows
us to determine the exact time between the time of contact to psychiatric hospitals and the
crime. We measure crimes as an accumulated count variable over the entire three year period
following first contact, and later contact and admission as a binary, absorbing indicator.
We use two measures of self-harm: (a) hospitalisations for overdoses; and (b) hospitalisations for lesions. We construct the two variables using information on exact dates of somatic
hospital-treatments relative to date of first contact to a psychiatric hospital together with the
main diagnosis. We obtain labour market outcomes from the national register on labour force
statistics (RAS). The register includes annual listings of type of occupation, unemployment
status, and dependency on other forms of welfare benefits. We generate three categories:
116
employment, unemployment, and not in the labour force. Contrary to the other outcome
variables, we only have access to an annual measure of labour market outcomes measured
ultimo November each year. Tables III.3 and III.4 summarise the outcome measures by
treatment status (immediate inpatient admission vs. no immediate inpatient admission).
Table III.3: Summary of Outcomes for Admission, Contact, Crimes, Overdose, and Lesion
3 months
6 months
9 months
12 months
15 months
18 months
21 months
24 months
27 months
30 months
33 months
36 months
Observations
Admission
Not adm. Adm.
0.017
0.030
(0.145)
(0.186)
0.035
0.059
(0.219)
(0.285)
0.055
0.086
(0.291)
(0.373)
0.072
0.110
(0.355)
(0.447)
0.088
0.135
(0.400)
(0.511)
0.103
0.158
(0.450)
(0.564)
0.117
0.180
(0.496)
(0.615)
0.132
0.203
(0.541)
(0.665)
0.147
0.228
(0.592)
(0.733)
0.160
0.251
(0.634)
(0.800)
0.172
0.276
(0.671)
(0.865)
0.186
0.301
(0.717)
(0.925)
16928
7349
Contact
Not adm. Adm.
0.088
0.220
(0.283)
(0.414)
0.123
0.284
(0.329)
(0.451)
0.143
0.317
(0.350)
(0.465)
0.153
0.346
(0.360)
(0.476)
0.162
0.366
(0.368)
(0.482)
0.169
0.382
(0.375)
(0.486)
0.176
0.398
(0.380)
(0.489)
0.181
0.408
(0.385)
(0.492)
0.187
0.419
(0.390)
(0.493)
0.192
0.427
(0.394)
(0.495)
0.196
0.433
(0.397)
(0.496)
0.200
0.440
(0.400)
(0.496)
16928
7349
Crimes
Not adm. Adm.
0.226
0.497
(0.418)
(0.500)
0.281
0.572
(0.450)
(0.495)
0.313
0.602
(0.464)
(0.490)
0.333
0.623
(0.471)
(0.485)
0.351
0.638
(0.477)
(0.481)
0.365
0.649
(0.482)
(0.477)
0.381
0.660
(0.486)
(0.474)
0.393
0.668
(0.488)
(0.471)
0.403
0.675
(0.490)
(0.468)
0.413
0.683
(0.492)
(0.466)
0.421
0.688
(0.494)
(0.464)
0.429
0.693
(0.495)
(0.461)
16928
7349
Overdose
Not adm. Adm.
0.010
0.019
(0.101)
(0.135)
0.016
0.030
(0.127)
(0.172)
0.020
0.041
(0.140)
(0.199)
0.024
0.049
(0.154)
(0.215)
0.028
0.054
(0.165)
(0.227)
0.031
0.060
(0.174)
(0.237)
0.035
0.064
(0.184)
(0.245)
0.038
0.067
(0.190)
(0.251)
0.040
0.072
(0.196)
(0.258)
0.043
0.077
(0.202)
(0.267)
0.045
0.082
(0.208)
(0.274)
0.048
0.087
(0.213)
(0.281)
16928
7349
Lesion
Not adm. Adm.
0.001
0.002
(0.034)
(0.042)
0.002
0.003
(0.047)
(0.055)
0.003
0.005
(0.054)
(0.069)
0.004
0.006
(0.059)
(0.079)
0.005
0.007
(0.067)
(0.083)
0.005
0.008
(0.073)
(0.088)
0.006
0.009
(0.077)
(0.094)
0.007
0.010
(0.082)
(0.097)
0.007
0.011
(0.085)
(0.104)
0.008
0.012
(0.089)
(0.107)
0.009
0.013
(0.093)
(0.112)
0.009
0.013
(0.096)
(0.114)
16928
7349
Note: Table shows means and std. dev. of outcome variables for the sample dependent on treatment status. Time 0 is month of initial
contact. Crimes are aggregating count variables. Admission, Contact, Overdose and Lesion are absorbing state dummies. Standard
deviation in parentheses.
117
Table III.4: Summary of Labor Market Outcomes
12 months
24 months
36 months
Observations
Empl.
Not adm. Adm.
0.550
0.455
(0.498)
(0.498)
0.537
0.444
(0.499)
(0.497)
0.532
0.431
(0.499)
(0.495)
16928
7349
Unempl.
Not adm. Adm.
0.169
0.202
(0.375)
(0.402)
0.166
0.190
(0.372)
(0.393)
0.160
0.177
(0.367)
(0.382)
16928
7349
Out of labor force
Not adm.
Adm.
0.282
0.343
(0.450)
(0.475)
0.297
0.366
(0.457)
(0.482)
0.308
0.391
(0.461)
(0.488)
16928
7349
Note: Table shows means and std. dev. of outcome variables for the sample dependent
on treatment status. Time 0 is month of initial contact. Standard deviation in parentheses.
From the tables we see that the average rates of subsequent admissions and crime are
substantial and that, overall, the individuals who received inpatient care at first contact
have worse outcomes than individuals who did not receive inpatient treatment in terms of
readmissions, criminal convictions, and labour market attachment.
We do not explicitly address how inpatient treatment upon initial contact reduces core
symptoms of psychiatric illnesses or improve patients’ the quality of life, as these are highly
subjective variables that may relate spuriously to realised treatment status. Instead, we
investigate the derived effects on realized objective outcomes. We implicitly assume that
hospital contacts largely reflect patients’ subjective need of treatment. Consequently, we
expect that institutional settings predominately drive estimated increases (reductions) in
admission rates above (below) estimated increases (reductions) in hospital contacts.
Instrumental Variable
As an instrument for inpatient admission we use hospital specific contact intensity. We
construct our instrumental variable as the fraction, for each date and each hospital, of the
number of weekly contacts relative to the maximum number of contacts within a given seven
day period during the past year. We use the complete psychiatric register to identify the
number of daily contacts and admissions to wards that receive or treat 24-hour or part-time
admitted patients at each hospital. We compute the number of contacts with inpatient
118
admission potential within the past week for each individual contact from 1998 to 2001
(excluding the day of an individual’s first contact). This variable will be the numerator
in our instrumental variable. It contains information on the total demand for psychiatric
treatments at a given date at a given hospital. In order to control for hospital size, we create
a similar variable that contains the maximum number of contacts within a given seven day
interval during the past year from the date of each individual contact. This will be the
denominator in our instrumental variable.14 For individual i at hospital h the instrument
equals:
lag(1week)
Zi
lag(2weeks)
Zi
=
=
P−1
d=−7
d=−7
Contactshd ,
P−2
Contactshd
P−359
d=−8 Contactshd , ...,
d=−365
P−8
d=−14 Contactshd
P−1
P−2
P
max( d=−7 Contactshd , d=−8 Contactshd , ..., −359
d=−365
max(
P−1
Contactshd )
(1)
Contactshd )
Figure III.1 shows the probability of being admitted for different values of the instrumental
variable. The probability of being admitted is unambiguously downward sloping across the
entire interval of hospital specific contact intensity in the two weeks preceding initial contact.
The figures also show that the relationship is strongest at low numbers of contacts during
the past weeks but monotone across the entire sample space. We therefore assess that the
IVs are both relevant and monotonous. Section 5 will present the first stage results formally.
Although there is little reason to believe that information related to the IVs is readily
available to patients, GPs may observe a hospital’s vacancy rate and react to this (e.g.,
if the GP delays referring a patient until there is room at a hospital or commences the
treatment him- or herself). In this case, we should find correlation between the contact
intensity and patient’s number of visits to the GP prior to first contact. Table IIIA.1 in
the Appendix shows estimates from regressions of GP and specialist visits on the two IVs.
Because patients may postpone contacts to hospital as a result of high contact intensity in
14
Importantly, we only count an individual once within a given week in order to avoid that e.g. high
admission thresholds affects the number of contacts as patients keep reappearing.
119
Figure III.1: Probability of Inpatient Admission Across the Instrument
((a)) Contact within last 7 days relative to max within last year
((b)) Contact within last 8-14 days relative to max within last year
Note: Figures show observed fraction of inpatient admissions across the values of the two intruments.
120
the two weeks preceding initial contact, we consider the number of visits during the year
of initial contact as well as during the previous year. Table IIIA.1 shows that none of the
estimates are significant on any conventional significance level; i.e., hospitals’ deviations in
contact intensity are independent of patients’ contacts to other sources of treatment for their
disorder.15
In addition, systematic relationships between the IVs and covariates could indicate endogeneity. Besides the explanatory variables described in Table III.2 we also include one year
lagged information on crime and labour market attachment, as well as indications on whether
the patient’s mother was ever admitted. Table IIIA.2 in the Appendix presents estimates of
the IVs regressed on these variables. The table shows that there is no significant relationship
between the past weeks’ contact intensity and the patients’ diagnoses, prior unemployment,
welfare dependency, prior crime, or parents’ psychiatric history. Only mothers’ schooling
and region are significant for both of the instruments. We have performed the analyses with
metropolitan areas excluded16 finding no qualitative differences from the overall results (see
Table IIIA.6 in the Appendix). As all other central estimates are insignificant, we consider
our key assumptions met.
4
Econometric Framework
This paper investigates the effects of admittance/non-admittance to a psychiatric hospital
for an individual i — a person in psychiatric distress — on his or her subsequent psychiatric
admissions and contacts, labour market outcomes, self-harming behaviour, and crime Yi :
∆i = Y1i − Y0i
15
(2)
If rejected patients turn up at other hospitals with more vacant beds and are admitted there, this could
result in a misspecification of the treatment variable and result in attenuation bias. But as only 1.7% of
the no-admission group contacts another hospital within the first week of their initial rejection, we do not
consider this to be a problem.
16
Major cities also constitute the areas most likely to allow for selection between hospitals according to
occupancy rate.
121
Y1i denotes person i’s potential outcome if treated, and Y0i denotes the potential outcome
if not treated. ∆i is our parameter of interest. Yet, we face several obstacles in estimating
∆i , foremost that we do not observe both counterfactual treatment states. Let Di = {0, 1}
be a dummy variable indicating whether a hospital admits a person upon initial contact.
We may describe the potential outcomes Y0 , Y1 (suppressing the subscript i) as functions of
observable characteristics X and unobservable characteristics U (Heckman & Honore, 1990;
Heckman et al. , 2006):
Yk = µk (X) + Uk , k = {0, 1}
(3)
Individuals “select” into inpatient admission (D = 1) if the total potential net gain of
admission is positive:
D = 1[Y1 − UC > Y0 ]
(4)
= 1[µ1 (X) − µ0 (X) > U0 − U1 + UC ]
where −V = U1 − U0 − UC is unobserved net gains of selecting into treatment. UC refers to
costs; psychic and monetary. The definition implies that the outcomes we observe equal:
Y = µ0 (X) + D(µ1 (X) − µ0 (X) + U1 − U0 ) + U0
(5)
If ignored, unobserved characteristics will be embedded in the error term when estimating a
basic OLS, which will thus be biased.
Therefore, to circumvent that the counterfactual unobservable components of the outcomes are likely to differ, we employ an instrumental variable Z = {z1 , z2 }, which is the
fraction of the number of contacts one and two weeks prior to initial contact relative to the
maximum number of contacts within a given week during the past year at a given hospital.
Inserting Z in equation (4) and implementing the instrument in a 2SLS approach yield the
following 1st stage equation:
D = π10 X + π20 Z − Ṽ
122
(6)
A pivotal assumption is that the fraction of the number of weekly contacts relative to the
maximum number of contacts within a given week during the past year is independent of
other unobservable selection mechanisms captured by (U1 , U0 ). I.e., neither the number of
contacts during the past couple of weeks, nor the maximum number of contacts during a
week in the past year, is allowed to affect whether a patient chooses a specific day and a
specific hospital to have his or her first contact with the psychiatric system. In addition to
independence between the instrument and the unobservable characteristics, we also need a
monotonic effect of the instrument on the endogenous regressor for all values of the instrument. Figure III.1 confirms that this is indeed the case. Because Z constitutes an exogenous
and monotonous instrument for Admitted, we can identify the Local Average Treatment
Effect17 of being admitted as:
β2LAT E = E[β2 |π10 X + π20 Z < Ṽ < π10 X + π20 Z ∗ ], f or Z > Z ∗
(7)
The LATE captures the average effect of being admitted for those who are moved from ’no
admission’ to ’admission’ when Z decreases to Z ∗ .18 Consequently, β2LAT E may incorporate
heterogeneous treatment effects across individuals with different levels of unobservable characteristics, such as severity of mental disorder. Some may be on the margin of treatment
assignment only for very low values of Z and others might be on the margin of treatment
assignment at the highest values of Z. To allow for heterogeneity across the different levels
of pre-admission levels of unobservable characteristics we estimate the Marginal Treatment
17
We estimate the first stage equation using the instrument linearly. The results are robust to using
alternative specifications that allow for non-linear relationships between the probability of admission and
previous weeks’ contact intensity. These results are presented in Figure IIIA.3 in the Appendix.
18
Alternatives to treatment (inpatient admission upon initial contact) comprise e.g., no treatment at all,
subsequent outpatient treatment, and a new subsequent contact to the hospital that results in an inpatient
admission. Our treatment effects will identify the effect of inpatient admission upon initial contact relative
to an average of all of these individual alternatives. Identifying each individual alternative would require
at least one instrument per margin of treatment. Authors refer to Heckman & Urzua (2010) for a general
discussion of this issue and Kirkebøen et al. (2014) for an application (investigating field of study) where
all individual treatment margins are identified.
123
Effects (MTE) of admission (Björklund & Moffitt, 1987; Heckman & Vytlacil, 2005):
β2M T E = E[β2 |UD = u∗D , X = X ∗ ]
(8)
where UD = FUD [V ] (see eq. (4)). β2M T E captures the effect of being admitted on the
outcomes for those who are on the margin of treatment at each level of unobservable net
gains UD (V ).19 The smaller the UD (V ), the larger the unobserved net gains of being selected
into inpatient admission. To be on the margin of treatment, a given level of observed
probability of admission (observed gains) must be matched by a corresponding inverse level of
unobserved net gains. As unobserved gains of admission are arguably an increasing function
of the severity of mental disorder, we interpret UD (V ) as an aspect of severity (though
interpretations may differ by the content of and interaction with UC ), where low values of
UD (V ) correspond to severe mental disorders and vice versa.20
5
Results
This section presents the estimation results. First, we show that our instrumental variable
is appropriate. Thereafter, we present our main results: the effects of inpatient admission
on the probability of subsequently contacting a psychiatric hospital again, the probability
of later admissions to psychiatric hospitals, crime, (somatic) hospitalisations due to drug
overdoses or lesions, and labour market outcomes. Finally, we present results from Marginal
Treatment Effects of admission and the effect of admission on spouses’ LMOs.
19
We estimate the first stage equation of the MTE by a probit. We report estimates of the parametric
version of the MTE, see Heckman et al. (2006).
20
The MTE is a generalisation of treatment effects such as the LATE:
β2LAT E =
1
UD − UD ∗
Z
UD ∗
UD
β2M T E dU
where UD is the random/latent variable for those who are affected by Z.
124
5.1
2SLS Results
Table III.5 presents the results of the first stage regression of our instrumental variables on
a dummy for inpatient admission. The first column shows the first stage estimates without
any additional control variables, the second column shows the estimates with a set of socioeconomic and demographic control variables, and the third column shows the estimates with
additional dummies for the patient’s diagnosis.
Table III.5: 1st stage Estimation Results
Average occupancy rate,
deviation from hospital mean
Previous 1-7 days
Previous 8-14 days
F-value
Observations
SES and demograpic controls
Diagnosis controls
Inpatient adm.
Inpatient adm.
Inpatient adm.
-0.154∗∗∗
(0.030)
-0.143∗∗∗
(0.030)
-0.142∗∗∗
(0.027)
-0.103∗∗∗
(0.029)
99.372
24277
-0.092∗∗
(0.028)
82.671
24277
X
-0.089∗∗∗
(0.026)
87.776
24277
X
X
+
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
Note: Table shows OLS regression results of inpatient admission (0/1) on the two instrumental
variables; hospital specific contact intensity the two week prior to the individual’s initial contact. Standard errors clustered by hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth,
mothers years of schooling, father’ age at birth, father’s years of schooling, mother has prior
psych. history (dummy), admitted in own municipality (dummy), greater CPH area (dummy),
other metropolitan area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
The relationships are highly significant across the three different specifications when tested
individually or jointly (the F-values all exceed the Staiger-Stock rule-of-thumb of 10 (Staiger
& Stock, 1997)). This confirms the findings from Figure III.1, that also showed that the
probability of inpatient admission decreased unambiguously as both contact intensity rates
increased.
125
Subsequent Admissions and Contacts
Figure III.2 shows OLS and 2SLS results of the effect of inpatient admission on the probability of later admission to psychiatric care from three months after first contact and until 36
months after first contact. The estimates are also reported in table IIIA.3 in the appendix.
From Figure III.2(a) we see that inpatient admission at first contact correlates positively
with the likelihood of later admissions—on average inpatients have just below 10%-points
higher likelihood of inpatient admission three months after first contact than the patients
whom the psychiatric hospital chose not to admit at first contact. The association increases
to just below a 20%-points increase at 30 months after first contact. Figure III.2(b) reports
the 2SLS estimates of the effect of inpatient admission. For the first half of the period the
likelihood of inpatient re-admission is increased by about 15%-points, whereas for the second
half of the period the effect size is an increase in the likelihood of about 20%-points. The
estimates are at least borderline significant for the entire period, and significant at the 5%
level for the first couple of months, and from month 15 and onwards. The 2SLS estimates
are of similar sign and larger or as large as the OLS estimates.21 In order to investigate the
mechanisms behind this notable result, we consider the effects of admission on the likelihood
of subsequently contacting a psychiatric hospital again after first contact.
Figure III.3 shows OLS and 2SLS estimates of the effect of inpatient admission on the
probability of later contact to psychiatric hospitals from three months after first contact
and until 36 months after first contact. The estimates are also reported in Table IIIA.4 in
the appendix. From the OLS estimates in Figure III.3(a) we see that inpatient admission is
associated with an increase of around 20%-points in the likelihood of subsequent contact with
the psychiatric health care system for the following three to 36 months after first contact.
Yet, when we examine the causal effect of admitting the patient on the margin, Figure
21
The variance of estimates is large. This could indicate the use of a weak instrument. However, the first
stage results from Table III.5 show that this is not the case.
126
III.3(b) shows that there is no significant effect across the period. Again, the estimates
retain the same sign as the OLS estimates but are significantly smaller in size. The figures
show that admitting people to inpatient treatment leads to a higher re-admission rate for
the subsequent 36 months after initial contact, but does not lead to significantly higher
re-contact rates in the same period. These findings indicate that institutionalisation is a
pivotal mechanism behind the size of the estimates in Figure III.2(b).22 I.e., if a person gets
his or her foot in the door at first contact, he/she is much more likely to be re-admitted as
an inpatient in subsequent years.
Crimes
Figure III.4 shows the OLS and 2SLS estimates of inpatient admission on the future number
of criminal convictions. The estimates are also reported in Table IIIA.5 in the appendix.
Figure III.4(a) shows that individuals admitted to inpatient care at first contact have higher
crime rates during all of the first 36 months after initial contact. Moreover, their overrepresentation in the criminal justice system grows as the time from first contact approaches
36 months. When we focus on the causal effect of admitting the marginal person to inpatient
care in Figure III.4(b), we see a significant and substantial decrease in crime for the first six
months after first contact. Moreover, the effect persists as borderline significant up until 22
months after first contact. Admitting 100 patients on the margin of treatment to inpatient
care upon their first contact leads to ten fewer crimes during the subsequent six months.
Inpatient admittance reduces subsequent crime, either because of incapacitation or because
inpatient treatment better meets the immediate medical needs of crime-prone patients at
first contact.
22
Note, however, that the 2SLS estimates for admittance and contacts are significantly different from each
other at the start of the period only (6 months).
127
Figure III.2: Effect on Probability of Subsequent Inpatient Admission by Months Since 1st
Contact
((a)) OLS estimates
((b)) 2SLS estimates
Note: Figure shows OLS and 2SLS regression results of inpatient admission (0/1) on subsequent
re-admission (0/1). The dashed lines indicate 95% confidence intervals and the dotted line indicate 90%
confidence intervals. Standard errors clustered by hospital and month in parentheses. Time 0 is month of
initial contact.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers
years of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history
(dummy), admitted in own municipality (dummy), greater CPH area (dummy), other metropolitan area
(dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category form ICD-10.
128
Figure III.3: Effect on Probability of Subsequent Contact to a Psychiatric Hospital by
Months Since 1st Contact
((a)) OLS estimates
((b)) 2SLS estimates
Note: Figure shows OLS and 2SLS regression results of inpatient admission (0/1) on subsequent contact to
psych. hospitals (0/1). The dashed lines indicate 95% confidence intervals and the dotted line indicate 90%
confidence intervals. Standard errors clustered by hospital and month in parentheses. Time 0 is month of
initial contact.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers
years of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history
(dummy), admitted in own municipality (dummy), greater CPH area (dummy), other metropolitan area
(dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category form ICD-10.
129
Figure III.4: Effect on Subsequent Crimes by Months Since 1st Contact
((a)) OLS estimates
((b)) 2SLS estimates
Note: Figure shows OLS and 2SLS regression results of inpatient admission (0/1) on subsequent crimes.
The dashed lines indicate 95% confidence intervals and the dotted line indicate 90% confidence intervals.
Standard errors clustered by hospital and month in parentheses. Time 0 is month of initial contact.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers
years of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history
(dummy), admitted in own municipality (dummy), greater CPH area (dummy), other metropolitan area
(dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category form ICD-10.
130
As earlier results showed that inpatient admissions increase the probability readmissions,
we suspect that the crime reductions are caused by an incapacitating effect of being admitted as an inpatient. To examine whether incapacitation drives the effect of inpatient
treatment, we also estimate models where we set time 0 at time of discharge, such that e.g.
12 months refer to one year after end of treatment and not 12 months after initial contact.
The figure shows that the estimates are now close to zero and insignificant (see Figure IIIA.1
in Appendix), so part of the effect of inpatient treatment on subsequent crime comes from
incapacitation of patients at the immediate time of need.
Self-harming Behavior
Figure III.5 shows the effect of admission on the subsequent risk of at least once experiencing
hospitalisation due to drug overdose or lesions. Individuals admitted at first contact are more
likely to experience hospitalisation due to drug overdose for the three following years as seen
from Figure III.5(a). Yet, when we focus on the 2SLS estimates, there is no significant
effect while the point estimates are negative. For lesions there is no significant association
with admission at first contact (Figure III.5(c)). However, the 2SLS estimates show that
admittance leads to a significant reduction in the risk of hospitalisation due to lesions in the
six months following first contact, after which the effect fades and becomes insignificant.23
23
This reduction is not driven by incapacitation. The estimates do not differ qualitatively when we center
outcomes around day of discharge.
131
Figure III.5: Effect on Subsequent Probability of Being Hospitalized for Self-harm by Months
Since 1st Contact
((a)) OLS overdose
((b)) 2SLS overdose
((c)) OLS lesion
((d)) IV lesion
Note: Figure shows OLS and 2SLS regression results of inpatient admission (0/1) on the risk of ever
experiencing hospitalization through overdoses (0/1) or lesions (0/1) the three years following first contact.
The dashed lines indicate 95% confidence intervals and the dotted line indicate 90% confidence intervals.
Standard errors clustered by hospital and month in parentheses. Time 0 is month of initial contact.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers
years of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history
(dummy), admitted in own municipality (dummy), greater CPH area (dummy), other metropolitan area
(dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category form ICD-10.
132
Labor Market Outcomes
To further investigate whether institutionalisation is more likely to happen when people
enter inpatient care at first contact, we also consider how entering inpatient care affects
subsequent labour market outcomes. If inpatient treatment has an lock-in effect, we should
expect inpatient admittance to also affect labour market outcomes. Table III.6 reports the
OLS and 2SLS results for admitting people to inpatient treatment at first contact on labour
market position the following three years. A person can either be in employment, registered
as unemployed, or registered as outside the labour force. Column 2 presents the OLS results
and columns 3-5 show the 2SLS estimates.
Table III.6: Estimation Results on Subsequent Labor Market Outcomes
OLS
Employment
First year since contact
Second year since contact
Third year since contact
Unemployment
First year since contact
Second year since contact
Third year since contact
Out of Labor Force
First year since contact
Second year since contact
Third year since contact
N
SES and demograpic controls
Diagnosis controls
2SLS
2SLS
2SLS
-0.054∗∗∗
(0.007)
-0.049∗∗∗
(0.007)
-0.053∗∗∗
(0.007)
-0.053
(0.098)
-0.053
(0.088)
-0.168∗
(0.083)
-0.112
(0.097)
-0.143
(0.088)
-0.253∗∗
(0.085)
-0.096
(0.095)
-0.126
(0.085)
-0.240∗∗
(0.083)
0.016∗∗
(0.006)
0.013∗
(0.006)
0.009+
(0.005)
-0.069
(0.069)
-0.020
(0.066)
0.017
(0.056)
-0.045
(0.073)
0.009
(0.068)
0.059
(0.060)
-0.053
(0.072)
0.003
(0.068)
0.054
(0.060)
0.038∗∗∗
(0.007)
0.036∗∗∗
(0.007)
0.044∗∗∗
(0.007)
24277
X
X
0.122
(0.075)
0.073
(0.080)
0.151∗
(0.072)
24277
0.158∗
(0.080)
0.134
(0.086)
0.194∗
(0.076)
24277
X
0.149+
(0.079)
0.124
(0.085)
0.186∗
(0.076)
24277
X
X
+
p<.10;∗ p<.05;∗∗ p<.01;∗∗∗ p<.001
Note: Table shows 2SLS regression results of inpatient admission (0/1) on subsequent employment (0/1), unemployment (0/1), and being out of the labor force (0/1). Standard errors
clustered by hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth,
mothers years of schooling, father’ age at birth, father’s years of schooling, mother has prior
psych. history (dummy), admitted in own municipality (dummy), greater CPH area (dummy),
other metropolitan area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
133
We see that inpatients are more often unemployed, more often outside the labour force,
and less often employed for the three years after initial contact than people who did not
enter inpatient care. When we examine the causal effect of admitting the marginal person to
inpatient care at initial contact (columns 3 to 5), we see that patients admitted to inpatient
treatment become gradually less employed for the following three years, and instead are
outside the labour force. Three years after first contact the marginal individual who is
admitted has 25 percentage point lower employment level, and are about 20 percentage
point more likely to be outside the labour force.
Although the estimates for labour market outcomes appear very large at first, they should
be viewed in the light of the large effects of inpatient admission on likelihood of later admission.24 Psychiatric hospital records are a strong indicator for whether social services
provide individuals with disability pension, early retirement, or other forms of social assistance without labour market requirements. Hence, by construction, being admitted at first
contact with a psychiatric hospital likely makes the patient eligible for permanent welfare
benefits; if not directly from first admission then from subsequent derived admissions.
5.2
Gender and age differences
Men and women might seek psychiatric help for different reasons and different illnesses,
and respond to admissions at different margins. Figure III.6 shows the LATE estimates
for admissions, contacts, and crime for men and women separately. Table III.7 reports the
effects on labour market outcomes by gender. We only report 2SLS results and only for the
models where we control for SES, demographics, and diagnosis types.25
24
Also, the changes from OLS to 2SLS appear counterintuitive if one has the likely selection bias of an
average population in mind. Yet, as we have shown, our sample is not drawn from the average population
and very different selection mechanisms may play a role here. For example, stronger patients may be better
at manipulating institutions (see Moustsen et al. (2015) for a similar example from cancer-treatment).
25
We also examine whether there exist heterogeneous effects across types of diagnoses, but find no significant or substantial differences. Results available on request.
134
Figure III.6: 2SLS Estimates of Effects of Inpatient Admission on Likelihood of Subsequent
Admission, Contact, and Number of Crimes by Months Since 1st Contact and by Gender
((a)) Males, admission
((b)) Females, admission
((c)) Males, contact
((d)) Females, contact
((e)) Males, crimes
((f)) Female, crimes
Note: Figures shows 2SLS regression results of inpatient admission (0/1) on subsequent re-admission (0/1),
contact to psych. hospitals (0/1), and crimes for males and females separately. The dashed lines indicate
95% confidence intervals and the dotted line indicate 90% confidence intervals. Time 0 is month of initial
contact. Standard errors clustered by hospital and month in parentheses. SES and demographic controls
include: Age at adm., mother’s age at birth, mothers years of schooling, father’ age at birth, father’s years
of schooling, mother has prior psych. history (dummy), admitted in own municipality (dummy), greater
CPH area (dummy), other metropolitan area (dummy), year dummies. Diagnosis controls include:
Dummies for each F. diagnosis category form ICD-10.
135
Figure III.6 shows a clear gender disparity in the way men and women react to inpatient
treatment. Men, across all ages, experience a borderline significant increase in the likelihood
of re-admissions until 24 months after first contact. Additional analyses across age (not
shown here) indicate that men below the age of 30 at the time of initial contact experience
a corresponding increase in the likelihood of subsequent contact, while men above the age of
30 experience a significant institutionalisation effect, as they suffer from significant increases
in re-admission rates but does not change contacting-behaviour correspondingly. Women
significantly increase re-admission and contact rates as time approaches 36 months after initial contact. The estimate of the effect of inpatient treatment on probability of re-admission
is almost three times as high for women as for men at month 30 (just below 0.30 for women
and around 0.12 and insignificant for men), while the likelihood of contacting a psychiatric hospital again has increased in similar magnitude for women. The results indicate that
(older) men are more likely to experience further institutionalisation if admitted to inpatient
care at first contact than is the case for women.
The effects of inpatient treatment by gender also differ for the crime outcome. 21 months
after first contact, the effect of inpatient admission on crime for men is around 45 criminal
acts less per 100 men admitted to inpatient treatment. For women, there is no significant
effect. As seen from Table III.7 there is no effect of inpatient treatment on men’s labour
market attachment, but there are significant effects for women. Three years after first
contact, female labour market attachment has dropped drastically, with women moving
from employment out of the labour force. The drop in employment dovetails with women’s
higher admission rates. Comparatively, men who enter the psychiatric treatment system
have generally lower SES, worse labour market attachment, and higher crime rates than
their female counterparts at time of first contact (see Table IIIA.7 in appendix), which could
suggest that the gender disparities in treatment effects of inpatient treatment originate from
gender differences in the pre-treatment levels.
136
Table III.7: 2SLS Estimation Results on Subsequent Labor Market Outcomes by Gender
Employment
First year since contact
Second year since contact
Third year since contact
Unemployment
First year since contact
Second year since contact
Third year since contact
Out of Labor Force
First year since contact
Second year since contact
Third year since contact
Observations
SES and demographic controls
Diagnosis controls
+
Male
Female
0.022
(0.113)
-0.006
(0.114)
-0.044
(0.112)
-0.231
(0.141)
-0.256+
(0.136)
-0.470∗∗∗
(0.136)
-0.017
(0.095)
-0.040
(0.103)
0.034
(0.083)
-0.093
(0.107)
0.045
(0.0900)
0.080
(0.090)
-0.004
(0.102)
0.045
(0.117)
0.010
(0.105)
0.324∗
(0.130)
0.211
(0.130)
0.390∗∗
(0.132)
11246
X
X
13031
X
X
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
Note: Table shows 2SLS regression results of inpatient admission
(0/1) on subsequent employment (0/1), unemployment (0/1), and
being out of the labor force (0/1) for males and females separately.
Standard errors clustered by hospital and month in parentheses.
SES and demographic controls include: Age at adm., mother’s
age at birth, mothers years of schooling, father’ age at birth,
father’s years of schooling, mother has prior psych. history
(dummy), admitted in own municipality (dummy), greater CPH
area (dummy), other metropolitan area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
137
5.3
Marginal Treatment Effects
In the previous section we documented heterogeneous effects across observable characteristics such as gender and age. We now examine heterogeneity across unobserved, or latent,
characteristics by estimating the marginal treatment effects of inpatient admission on later
admissions, contacts, crime, hospitalisations for drug overdose and lesions, and labour market
outcomes.26
Importantly, a sizable fraction of those who are not admitted as inpatients receive some
form of outpatient treatment. The counterfactual that people at different margins of treatment face (no admission or outpatient admission) is crucial to our interpretation of the
results. However, whether the compliers are on the margin between inpatient admission and
outpatient admission or no treatment is inherently unidentified. The differences in Marginal
Treatment Effect M T E = δ∆i /δp(Z, X) |UD =UD∗ across UD may be a composite of two different effects which may not be of equal sign. On the one hand, individuals with low UD ’s are
only at the margin of treatment when the contact intensity is high and vice versa. Hence UD
may be interpreted as an inverse scale of severity of the psychiatric disorder.27 The patients
with most severe disorders are likely to benefit more from an inpatient admission, which
would result in an upward sloping MTE for subsequent admissions, contacts, crime, hospitalisations due to drug overdose or lesions, and unemployment and a downward sloping MTE
for employment. On the other hand, we cannot rule out that various levels of Z also coincide
with different counterfactuals to inpatient admission. There is no a-priori knowledge about
the ordering of the vast multitude of every imaginable treatment state. Consequently, we
cannot identify margins within the alternative to treatment without making further (strong)
assumptions about one or both of our instrumental variables (Heckman & Urzua, 2010),
26
We abstain from presenting results from MTEs for spousal labour market outcomes as estimates are
inconclusive due to large variance. The results can be obtained from the authors.
27
Or as an alternative formulation in the Roy-model framework, UD = U0 − U1 assuming no costs of
admission (UC = 0), see Heckman & Vytlacil (2005).
138
but only note that the weights attached to each alternative embedded in the category No
treatment (D=0) may change across UD .
Figure III.7 reports the estimated MTEs for the likelihood of subsequent admission to,
and contact with, a psychiatric hospital, and crime. Figure III.8 reports the results for drug
overdose and lesions, and Figure III.9 reports the effects for the labour market outcomes.
Because we estimate the effects on a quarterly basis for admissions, contacts, and crimes, we
report the marginal treatment effects jointly across time after first contact and across the
latent variable UD (see section 4). We can only identify the marginal treatment effect across
the interval of common support, which ranges from .05-.80 (cf. Figure IIIA.2 in Appendix
A). As we cannot report confidence intervals in the three axis sub-figures shown in Figure
III.7, we instead colour-code the estimates based on whether they are significant and positive
at a 10 % level (dark blue), insignificant and positive (light blue), insignificant and negative
(light red), or significant and negative (dark red). For labour market outcomes we show 10%
confidence intervals for each of the three years after first contact.
Figure III.7(a) shows the marginal treatment effect of inpatient admission at first contact
on likelihood of later psychiatric hospital admission. The MTE is positive across the entire
distribution, but only significant for patients with a high value of UD . The MTE also has a
strong upward slope in UD , which suggests that the negative effect of being admitted as an
inpatient decreases in severity of disorder. These results also supports the institutionalisation
hypothesis – patients with more severe disorders would likely experience re-admission to
psychiatric hospitals in either case, whereas patients with milder conditions need to already
have a record of admittance to get re-admitted.
Figure III.7(b) shows the MTE of inpatient admission on the likelihood of contacting
a psychiatric hospital again. Results are insignificant for most values, though negative for
the lowest values of UD , while individuals with high values of UD have significantly higher
likelihood of contacting a psychiatric hospital again following an inpatient admission at first
139
contact. This support the notion that the benefits of inpatient admission increase as UD
decreases.
Figure III.7(c) shows the MTE of inpatient admission on number of crimes. The effect is
negative across the entire period and all values of latent characteristics. The effects are largest
and most persistent for patients with the lowest values of UD . The effects are insignificant
for all values of UD after 30 months. There is an overall crime reducing effect of admission
upon first contact with a psychiatric hospital that originates during the first months after
initial contact.
Figure III.8 shows the MTEs for self-harming behaviour through overdoses or lesions. For
overdoses (Figure III.8(a)) we find that patients with low values of UD decrease their risk
following an inpatient admission, and that this reduction is persistent across the three years
we study. In contrast, we find that the risk for hospitalisation due to lesions is significantly
lower for all values of UD , albeit the effect is only short-term (Figure III.8(b)). Thus,
inpatient admission lowers the likelihood of one dimension of self-harm or suicide attempts
persistently for the most at-risk patients, while another dimension of self-harm is uniformly
but only temporarily reduced.
140
Figure III.7: Marginal Treatment Effects of Inpatient Admission on Likelihood of Subsequent
Admission, Contacts, and Number of Crimes
((a)) Admission
(
((b)) Contact
(
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((c)) Crimes
(
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(
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&
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50
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&
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0
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(
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6
(
)*
+
,
-
.
Note: Figures show estimated Marginal Treatment Effects of inpatient admission (0/1) on subsequent
re-admission (0/1), contact to psych. hosptial (0/1), and crimes. Time 0 is month of initial contact.
Covariates include: Gender (dummy), age at adm., mother’s age at birth, mothers years of schooling,
father’ age at birth, father’s years of schooling, mother has prior psych. history (dummy), admitted in own
municipality (dummy), greater CPH area (dummy), other metropolitan area (dummy), year dummies,
dummies for each F. diagnosis category form ICD-10.
Confidence levels are color-coded. Dark blue = positive estimate, p < 0.10; light blue = positive estimate,
p > 0.10; light red = negative estimate, p > 0.10; dark red = negative estimate, p < 0.10.
141
Figure III.8: Marginal Treatment Effects of Inpatient Admissions on Subsequent Probability
of Being Hospitalized for Overdoses or Lesions During the Subseq. Three Years
((a)) Overdose
(
((b)) Lesion
6
(
$
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%
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A
F
D
D
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B
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H
F
E
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D
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A
B
F
B
J
Note: Figures show estimated Marginal Treatment Effects of inpatient admission (0/1) on the risk of ever
being hospitalized the next three years for self-harm due to overdose (0/1), or lesion (0/1). Time 0 is
month of initial contact.
Covariates include: Gender (dummy), age at adm., mother’s age at birth, mothers years of schooling,
father’ age at birth, father’s years of schooling, mother has prior psych. history (dummy), admitted in own
municipality (dummy), greater CPH area (dummy), other metropolitan area (dummy), year dummies,
dummies for each F. diagnosis category form ICD-10.
Confidence levels are color-coded. Dark blue = positive estimate, p < 0.10; light blue = positive estimate,
p > 0.10; light red = negative estimate, p > 0.10; dark red = negative estimate, p < 0.10.
Finally, Figure III.9 shows the MTEs for labor market outcomes one, two, and three years
after first contact. The patients with the lowest values of UD experience the largest drop in
employment three years after first contact, whereas the effect for patients with high values
of UD are negative but insignificant. The patients with low values of UD also have higher
risk of being out of the labor force following an inpatient admission at first contact.
142
Figure III.9: Marginal Treatment Effects of Inpatient Admissions on Labour Market Outcomes
((a)) Employment in year 1
((b)) Employment in year 2
((c)) Employment in year 3
((d)) Unemployment in year 1
((e)) Unemployment in year 2
((f)) Unemployment in year 3
((g)) Out of labor force in year 1 ((h)) Out of labor force in year 2
((i)) Out of labor force in year 3
Note: Figures show estimated Marginal Treatment Effects of inpatient admission (0/1) on subsequent employment (0/1), unemployment (0/1), and being out of the labor force (0/1). Time 0 is month of initial
contact. Covariates include: Gender (dummy), age at adm., mother’s age at birth, mothers years of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history (dummy), admitted in
own municipality (dummy), greater CPH area (dummy), other metropolitan area (dummy), year dummies,
dummies for each F. diagnosis category form ICD-10. The dashed lines indicates 90% confidence intervals.
143
Taken together, the MTE estimates suggest two very different dimensions through which
inpatient admission may affect the patients’ later life. One is institutionalizing and results in
increased admission rates and lower labour market attachment for patients with less severe
disorders. The other arises as patients with more serious disorders are given immediate help
and thus also incapacitated. This lowers the risks of overdoses and crime.
5.4
Effect of Admittance on Spouses’ Labour Market Outcomes
Mental illness may also have effects beyond the life of the patient. Therefore, we also consider
how an inpatient admission affects spouses to people who contact the psychiatric care system.
Table III.8 reports the effect of inpatient admission at first contact on the spouse’s labour
market outcomes. 5,763 people in the data had an identifiable spouse at their first contact
with the psychiatric system. Columns 2, 4, and 6 present outcomes from OLS models, and
columns 3, 5, and 7 report 2SLS results. We follow the spouses for three years, regardless
of whether they remain in the relationship across the period or not.
The spouses of inpatients have slightly higher employment rates (column 2) and are less
out of the labour force (column 6) one year after first contact than spouses of people who
do not receive inpatient treatment. The 2SLS results show that inpatient admission at first
contact has substantial and at least borderline significant effect on spouses’ labour market
outcomes, even though the table also shows that the smaller sample results in large standard
errors, as could be expected. Three years after first contact, spouses are significantly less
unemployed (23.9 percentage points drop) and borderline significantly more employed (26.6
percentage points increase). There is no effect on the probability of being outside the labour
force. The effect sizes in Table III.8 should be viewed in the light of the possible strain
posed by living with an untreated psychiatric patients. The counterfactual to life with an
untreated patient—admission as an inpatient—will not only result in short run relief to the
spouse, but also in subsequent admissions and consequently further relief, cf. Figure III.2.
144
Table III.8: Estimation Results on Spouses’ Labor Market Outcomes
First year since contact
Second year since contact
Third year since contact
Observations
Employment
OLS
2SLS
0.030∗ 0.246+
(0.013) (0.146)
0.008
0.221
(0.013) (0.145)
0.004 0.266+
(0.013) (0.156)
5763
5763
Unemployment
OLS
2SLS
-0.004 -0.195+
(0.009) (0.106)
-0.006 -0.161+
(0.009) (0.092)
0.009 -0.239∗
(0.009) (0.107)
5763
5763
Out of labor force
OLS
2SLS
-0.026∗
-0.052
(0.012) (0.113)
-0.002
-0.059
(0.011) (0.119)
-0.013
-0.028
(0.011) (0.119)
5763
5763
+
p < .10;∗ p < .05;∗ ∗p < .01; ∗ ∗ ∗p < .001
Note: Table shows 2SLS regression results of inpatient admission (0/1) on his/her
spouse’s subsequent employment (0/1), unemployment (0/1), and being out of the
labor force (0/1). Standard errors clustered by hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age
at birth, mothers years of schooling, father’ age at birth, father’s years of schooling,
mother has prior psych. history (dummy), admitted in own municipality (dummy),
greater CPH area (dummy), other metropolitan area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
6
Conclusion
Treatment of psychiatric patients in the Western world has gone through radical changes
during the 20th century. For several decades, the main function of psychiatric treatment
has been downsized and partly moved away from hospitals towards community-based care.
Although the quality of psychiatric treatment has increased substantially during the last
century, medical professionals and the medical research community have recently voiced
their concern that the move away from admitting patients into inpatient care may have been
too substantial.
In this paper we have used hospital specific contact intensity during the weeks prior to
a patient’s first contact with the mental health system to identify the effects of admitting
patients immediately to inpatient care at first contact relative to not admitting them at
first contact. Using a sample of all first contacts to psychiatric hospitals by individuals
aged 18-45 between 1999 and 2001, we showed that admitting a first time patient on the
margin of being admitted had large but ambiguous effects. We found that in the short run,
inpatient treatment leads to less crime and self-harming behaviour, especially among men
145
and the patients who suffer the most severe conditions. We also found significant effects on
the probability of subsequent admissions and labour market outcomes, especially for women
and, in the case of admission, for people with less severe disorders. For labour market
outcomes, we found that women and people with the most severe disorders left employment
and decreased labour force participation. Both the effects on admission and labour market
outcomes increased in magnitudes across the subsequent three years after first contact. We
found little or no effect on the likelihood of contacting a psychiatric hospital again, which
indicates that admission at first contact affects how the mental health system treats patients
after initial contact, but does not affect the patients’ demand for subsequent treatment. We
also found persistent effects on the labour market outcomes for patients’ spouses—inpatient
admission led to significant lower unemployment levels and borderline significant higher
employment levels for spouses the three subsequent years after first contact.
Mental health issues are causes of strain and distress for the patients, the immediate
family, and for society as a whole. To make the adverse impact of mental disorders as
small as possible, society should aim at optimizing the available treatment possibilities for
patients. Yet our study has shown that this is not a simple task. When only considering
whether to admit more patients as inpatients or not, we found that inpatient admission has
very different effects across the dimensions of social life and also depends on the severity of
a patient’s condition. If the aim is to lower crime rates among mental health patients with
more severe conditions, it would make sense to increase the number of available inpatient
beds. If the aim, however, is to increase labour market affiliation, we should decrease the
number of beds.
146
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151
A
Supplementary Results
Table IIIA.1: Regression of GP and Specialists Visits on the Instruments
GP visits, year of admission
IV, day 1-7
IV, day 8-14
GP visits, year prior to admission
IV, day 1-7
IV, day 8-14
Specialists visits, year of admission
IV, day 1-7
IV, day 8-14
Specialists visits, year prior to admission
IV, day 1-7
IV, day 8-14
SES controls
Diagnosis controls
Observations
Model 1
Model 2
Model 3
-0.558
(0.681)
-0.507
(0.653)
-0.495
(0.652)
-0.389
(0.704)
0.223
(0.672)
0.205
(0.673)
0.220
(0.593)
0.137
(0.577)
0.152
(0.580)
-0.582
(0.617)
-0.146
(0.600)
-0.153
(0.600)
0.239
(0.214)
0.132
(0.212)
0.127
(0.213)
0.333
(0.219)
0.259
(0.217)
0.259
(0.218)
0.122
(0.189)
0.033
(0.188)
0.030
(0.187)
0.008
(0.207)
-0.058
(0.204)
X
24,277
24,277
-0.054
(0.204)
X
X
24,277
Note: Table shows OLS regression results of the two intrumental variables (hospital
specific contact intensity the two week prior to the individual’s initial contact) on
number of visits to general practioners and specialists the year of and the year prior
to initial contact. Standard errors clustered by hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age
at birth, mothers years of schooling, father’ age at birth, father’s years of schooling,
mother has prior psych. history (dummy), admitted in own municipality (dummy),
greater CPH area (dummy), other metropolitan area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
+
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
152
Table IIIA.2: Estimation Results of Covariates Regressed on the Instruments
Male
Age at admission
Mother’s age at birth
Mother’s months of schooling
Year 1999
Year 2000
Mother has been admitted
Mother missing
Father’s months of schooling
Father missing
Admitted in own municipality
Admitted in Copenhagen
Admitted in metropolitan area
Disorder associated with substance use
Psychosis, schizophrenia
Nervous or stress-related
Personality disorder
Affective/emotionel, pre-adult origin
Previous crime (0/1)
Out of labor force in year -1
Unemployed in year -1
Observations
IV day 1-7 IV day 8-14
-0.006∗
-0.003
(0.002)
(0.002)
-0.000
-0.000
(0.000)
(0.000)
0.000
-0.000
(0.000)
(0.000)
0.000∗
0.000∗
(0.000)
(0.000)
-0.023
-0.026+
(0.015)
(0.015)
0.014
0.011
(0.015)
(0.015)
0.001
0.000
(0.004)
(0.004)
0.002
0.000
(0.005)
(0.005)
0.000
0.000∗
(0.000)
(0.000)
0.009∗
0.010∗
(0.004)
(0.004)
-0.002
-0.005
(0.005)
(0.005)
0.040∗∗∗
0.043∗∗∗
(0.009)
(0.009)
0.036∗∗
0.036∗∗
(0.012)
(0.012)
-0.001
-0.000
(0.005)
(0.005)
-0.000
-0.001
(0.006)
(0.006)
0.000
0.000
(0.005)
(0.005)
-0.006
-0.007
(0.005)
(0.006)
0.009
0.014
(0.009)
(0.009)
-0.001
-0.004
(0.003)
(0.003)
-0.005
-0.007∗
(0.003)
(0.003)
-0.003
-0.000
(0.004)
(0.004)
24,277
24,277
Note: Table shows OLS regression results of the two intrumental variables
(hospital specific contact intensity the two week prior to the individual’s initial contact) on gender (dummy), age at adm., mother’s age at birth, mothers
years of schooling, father’ age at birth, father’s years of schooling, mother
has prior psych. history (dummy), admitted in own municipality (dummy),
greater CPH area (dummy), other metropolitan area (dummy), year dummies, and dummies for each F. diagnosis category form ICD-10. Standard
errors clustered by hospital and month in parentheses.
+
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
153
Table IIIA.3: Estimation Results on Likelihood of Subsequent Admission to a Psychiatric
Hospital
3 months from 1st contact
6 months from 1st contact
9 months from 1st contact
12 months from 1st contact
15 months from 1st contact
18 months from 1st contact
21 months from 1st contact
24 months from 1st contact
27 months from 1st contact
30 months from 1st contact
33 months from 1st contact
36 months from 1st contact
Observations
SES and demograpic controls
Diagnosis controls
OLS
0.115∗∗∗
(0.005)
0.140∗∗∗
(0.005)
0.150∗∗∗
(0.006)
0.167∗∗∗
(0.006)
0.175∗∗∗
(0.006)
0.181∗∗∗
(0.006)
0.188∗∗∗
(0.006)
0.191∗∗∗
(0.006)
0.195∗∗∗
(0.006)
0.196∗∗∗
(0.006)
0.198∗∗∗
(0.006)
0.200∗∗∗
(0.006)
24,277
X
X
2SLS
0.152∗
(0.064)
0.134+
(0.078)
0.129
(0.081)
0.115
(0.081)
0.146+
(0.078)
0.148+
(0.078)
0.188∗
(0.078)
0.184∗
(0.078)
0.176∗
(0.078)
0.179∗
(0.079)
0.172∗
(0.078)
0.186∗
(0.078)
24,277
2SLS
0.160∗
(0.066)
0.162∗
(0.077)
0.158∗
(0.079)
0.146+
(0.080)
0.180∗
(0.078)
0.181∗
(0.077)
0.222∗∗
(0.078)
0.216∗∗
(0.079)
0.205∗
(0.080)
0.210∗∗
(0.081)
0.199∗
(0.080)
0.214∗∗
(0.080)
24,277
X
2SLS
0.160∗
(0.068)
0.160∗
(0.080)
0.155+
(0.082)
0.142+
(0.083)
0.176∗
(0.079)
0.176∗
(0.078)
0.217∗∗
(0.070)
0.211∗∗
(0.080)
0.199∗
(0.080)
0.204∗
(0.081)
0.193∗
(0.080)
0.208∗∗
(0.079)
24,277
X
X
Note: Table shows OLS and 2SLS regression results of inpatient admission
(0/1) on subsequent re-admisison (0/1) corresponding to Figure III.2. Time 0
is month of initial contact. Standard errors clustered by hospital and month
in parentheses.
SES and demographic controls include: Gender (dummy), age at adm.,
mother’s age at birth, mothers years of schooling, father’ age at birth, father’s
years of schooling, mother has prior psych. history (dummy), admitted in own
municipality (dummy), greater CPH area (dummy), other metropolitan area
(dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD10.
+
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
154
Table IIIA.4: Estimation Results on Likelihood of Subsequent Contact with Psychiatric
Hospitals
3 months from 1st contact
6 months from 1st contact
9 months from 1st contact
12 months from 1st contact
15 months from 1st contact
18 months from 1st contact
21 months from 1st contact
24 months from 1st contact
27 months from 1st contact
30 months from 1st contact
33 months from 1st contact
36 months from 1st contact
Observations
OLS
0.247∗∗∗
(0.006)
0.261∗∗∗
(0.007)
0.257∗∗∗
(0.0067)
0.256∗∗∗
(0.007)
0.251∗∗∗
(0.007)
0.247∗∗∗
(0.007)
0.243∗∗∗
(0.007)
0.236∗∗∗
(0.007)
0.233∗∗∗
(0.007)
0.228∗∗∗
(0.007)
0.225∗∗∗
(0.007)
0.223∗∗∗
(0.007)
24,277
2SLS
0.079
(0.091)
0.117
(0.096)
0.105
(0.092)
0.063
(0.091)
0.0790
(0.086)
0.0806
(0.086)
0.124
(0.087)
0.0977
(0.087)
0.109
(0.086)
0.109
(0.087)
0.0913
(0.088)
0.072
(0.088)
24,277
2SLS
0.093
(0.096)
0.160
(0.099)
0.147
(0.094)
0.098
(0.094)
0.110
(0.090)
0.110
(0.090)
0.157+
(0.090)
0.127
(0.091)
0.139
(0.091)
0.137
(0.091)
0.118
(0.092)
0.097
(0.093)
24,277
2SLS
0.096
(0.097)
0.160
(0.103)
0.145
(0.099)
0.094
(0.097)
0.105
(0.093)
0.105
(0.093)
0.152
(0.093)
0.122
(0.094)
0.133
(0.093)
0.130
(0.093)
0.111
(0.094)
0.090
(0.094)
24,277
Note: Table shows OLS and 2SLS regression results of inpatient admission
(0/1) on subsequentcontact to psych. hospitals (0/1) corresponding to Figure III.3. Time 0 is month of initial contact. Standard errors clustered by
hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), age at adm.,
mother’s age at birth, mothers years of schooling, father’ age at birth, father’s
years of schooling, mother has prior psych. history (dummy), admitted in
own municipality (dummy), greater CPH area (dummy), other metropolitan
area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from
ICD-10.
+
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
155
Table IIIA.5: Estimation Results on Subsequent Crimes
3 months from 1st contact
6 months from 1st contact
9 months from 1st contact
12 months from 1st contact
15 months from 1st contact
18 months from 1st contact
21 months from 1st contact
24 months from 1st contact
27 months from 1st contact
30 months from 1st contact
33 months from 1st contact
36 months from 1st contact
Observations
OLS
0.008∗∗∗
(0.002)
0.023∗∗∗
(0.005)
0.036∗∗∗
(0.010)
0.055∗∗∗
(0.015)
0.078∗∗∗
(0.020)
0.106∗∗∗
(0.027)
0.138∗∗∗
(0.034)
0.174∗∗∗
(0.041)
0.217∗∗∗
(0.050)
0.266∗∗∗
(0.059)
0.323∗∗∗
(0.069)
0.388∗∗∗
(0.079)
24,277
2SLS
-0.034
(0.026)
-0.101+
(0.061)
-0.182+
(0.110)
-0.275
(0.172)
-0.363
(0.242)
-0.468
(0.322)
-0.580
(0.409)
-0.678
(0.503)
-0.758
(0.602)
-0.786
(0.706)
-0.787
(0.821)
-0.781
(0.943)
24,277
2SLS
-0.054+
(0.0285)
-0.153∗
(0.0675)
-0.270∗
(0.121)
-0.405∗
(0.189)
-0.541∗
(0.265)
-0.706∗
(0.353)
-0.886∗
(0.449)
-1.057+
(0.551)
-1.223+
(0.660)
-1.339+
(0.774)
-1.437
(0.899)
-1.536
(1.033)
24,277
2SLS
-0.056+
(0.0291)
-0.156∗
(0.0690)
-0.277∗
(0.124)
-0.416∗
(0.193)
-0.557∗
(0.270)
-0.729∗
(0.360)
-0.916∗
(0.456)
-1.096+
(0.561)
-1.270+
(0.673)
-1.396+
(0.789)
-1.504
(0.916)
-1.615
(1.051)
24,277
Note: Table shows OLS and 2SLS regression results of inpatient admission (0/1)
on subsequent crimes corresponding to Figure III.4. Time 0 is month of initial
contact. Standard errors clustered by hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), Age at adm.,
mother’s age at birth, mothers years of schooling, father’ age at birth, father’s
years of schooling, Mother has prior psych. history (dummy), Admitted in own
municipality (dummy), Greater CPH area (dummy), Other metropolitan area
(dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category form ICD10.
+
p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
156
Table IIIA.6: Regional Robustness Checks
Without Copenhagen
OLS
2SLS
Crime
3 months after first contact
6 months after first contact
9 months after first contact
12 months after first contact
15 months after first contact
18 months after first contact
21 months after first contact
24 months after first contact
27 months after first contact
30 months after first contact
33 months after first contact
36 months after first contact
Admissions
3 months after first contact
6 months after first contact
9 months after first contact
12 months after first contact
15 months after first contact
18 months after first contact
21 months after first contact
24 months after first contact
27 months after first contact
30 months after first contact
33 months after first contact
36 months after first contact
Contacts
3 months after first contact
Without major cities
OLS
2SLS
0.008∗∗
(0.003)
0.013∗∗∗
(0.004)
0.013∗
(0.005)
0.0123∗
(0.006)
0.016∗
(0.007)
0.020∗∗
(0.007)
0.024∗∗
(0.008)
0.028∗∗
(0.009)
0.032∗∗∗
(0.010)
0.040∗∗∗
(0.011)
0.046∗∗∗
(0.011)
0.054∗∗∗
(0.012)
−0.040
(0.026)
−0.084∗
(0.040)
−0.096+
(0.056)
−0.118+
(0.068)
−0.115
(0.075)
−0.137
(0.086)
−0.152+
(0.091)
−0.146
(0.099)
−0.151
(0.105)
−0.096
(0.109)
−0.070
(0.119)
−0.065
(0.126)
0.010∗∗∗
(0.003)
0.014∗∗
(0.004)
0.012∗
(0.005)
0.0132∗
(0.006)
0.017∗
(0.007)
0.022∗∗
(0.008)
0.026∗∗
(0.009)
0.030∗∗
(0.010)
0.034∗∗
(0.011)
0.040∗∗∗
(0.012)
0.045∗∗∗
(0.012)
0.054∗∗∗
(0.013)
0.116∗∗∗
(0.005)
0.143∗∗∗
(0.006)
0.158∗∗∗
(0.006)
0.173∗∗∗
(0.006)
0.182∗∗∗
(0.006)
0.189∗∗∗
(0.006)
0.197∗∗∗
(0.006)
0.200∗∗∗
(0.007)
0.205∗∗∗
(0.007)
0.207∗∗∗
(0.007)
0.208∗∗∗
(0.007)
0.210∗∗∗
(0.007)
0.171∗∗
(0.066)
0.168∗
(0.077)
0.164∗
(0.079)
0.148+
(0.079)
0.185∗
(0.075)
0.181∗
(0.074)
0.212∗∗
(0.074)
0.214∗∗
(0.074)
0.202∗∗
(0.074)
0.204∗∗
(0.076)
0.195∗∗
(0.075)
0.211∗∗
(0.074)
0.115∗∗∗
(0.006)
0.137∗∗∗
(0.007)
0.152∗∗∗
(0.007)
0.167∗∗∗
(0.007)
0.175∗∗∗
(0.007)
0.182∗∗∗
(0.007)
0.188∗∗∗
(0.007)
0.192∗∗∗
(0.007)
0.196∗∗∗
(0.007)
0.197∗∗∗
(0.007)
0.199∗∗∗
(0.008)
0.202∗∗∗
(0.008)
0.124∗
(0.053)
0.133∗
(0.061)
0.140∗
(0.064)
0.140∗
(0.064)
0.153∗
(0.063)
0.143∗
(0.064)
0.180∗∗
(0.065)
0.184∗∗
(0.065)
0.176∗∗
(0.066)
0.180∗∗
(0.067)
0.172∗∗
(0.067)
0.179∗∗
(0.065)
0.252∗∗∗
(0.007)
0.121
(0.097)
0.251∗∗∗
(0.009)
0.121
(0.074)
157
−0.034
(0.021)
−0.053
(0.033)
−0.049
(0.046)
−0.0559
(0.055)
−0.059
(0.062)
−0.088
(0.070)
−0.090
(0.075)
−0.086
(0.081)
−0.089
(0.087)
−0.054
(0.095)
−0.023
(0.103)
−0.011
(0.110)
6 months after first contact
9 months after first contact
12 months after first contact
15 months after first contact
18 months after first contact
21 months after first contact
24 months after first contact
27 months after first contact
30 months after first contact
33 months after first contact
36 months after first contact
Employment
12 months after first contact
24 months after first contact
36 months after first contact
Unemployment
12 months after first contact
24 months after first contact
36 months after first contact
Out of Labor Force
12 months after first contact
24 months after first contact
36 months after first contact
Observations
0.268∗∗∗
(0.007)
0.264∗∗∗
(0.007)
0.264∗∗∗
(0.007)
0.259∗∗∗
(0.008)
0.256∗∗∗
(0.008)
0.252∗∗∗
(0.008)
0.246∗∗∗
(0.008)
0.243∗∗∗
(0.008)
0.239∗∗∗
(0.008)
0.236∗∗∗
(0.008)
0.233∗∗∗
(0.008)
0.160
(0.102)
0.148
(0.098)
0.0993
(0.095)
0.106
(0.092)
0.105
(0.092)
0.148
(0.092)
0.128
(0.092)
0.133
(0.091)
0.132
(0.091)
0.116
(0.091)
0.0980
(0.091)
0.263∗∗∗
(0.008)
0.260∗∗∗
(0.008)
0.259∗∗∗
(0.008)
0.253∗∗∗
(0.008)
0.249∗∗∗
(0.008)
0.245∗∗∗
(0.009)
0.239∗∗∗
(0.009)
0.236∗∗∗
(0.009)
0.232∗∗∗
(0.009)
0.229∗∗∗
(0.009)
0.227∗∗∗
(0.009)
0.153∗
(0.076)
0.138+
(0.072)
0.080
(0.073)
0.070
(0.072)
0.067
(0.072)
0.096
(0.074)
0.084
(0.074)
0.087
(0.074)
0.090
(0.074)
0.081
(0.074)
0.073
(0.073)
−0.0525∗∗∗
(0.008)
−0.0468∗∗∗
(0.008)
−0.0483∗∗∗
(0.008)
−0.0834
(0.092)
−0.130
(0.080)
−0.238∗∗
(0.077)
−0.0517∗∗∗
(0.009)
−0.0496∗∗∗
(0.009)
−0.0526∗∗∗
(0.009)
−0.160∗
(0.0726)
−0.189∗∗
(0.0658)
−0.272∗∗∗
(0.0669)
−0.039
(0.070)
0.066
(0.065)
0.056
(0.056)
0.019∗∗
(0.007)
0.016∗
(0.007)
0.007
(0.006)
0.050
(0.056)
0.111∗
(0.053)
0.109∗
(0.048)
0.033∗∗∗
(0.008)
0.034∗∗∗
(0.008)
0.046∗∗∗
(0.008)
0.110+
(0.061)
0.078
(0.064)
0.163∗∗
(0.060)
0.015∗
(0.006)
0.012∗
(0.006)
0.007
(0.006)
0.038∗∗∗
(0.007)
0.035∗∗∗
(0.007)
0.041∗∗∗
(0.007)
19595
0.123+
(0.074)
0.064
(0.081)
0.182∗∗
(0.070)
19595
15898
15898 )
Note: Table shows 2SLS regression results of inpatient admission (0/1) on subsequent re-admisison (0/1), contact to psych.
hospitals (0/1), and crimes while excluding the greater Copenhagen area. Time 0 is month of initial contact. Standard errors
clustered by hospital and month in parentheses.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers years of schooling, father’
age at birth, father’s years of schooling, mother has prior psych. history (dummy), admitted in own municipality (dummy),
greater CPH area (dummy), other metropolitan area (dummy), year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
+ p < .10;∗ p < .05;∗∗ p < .01; ∗∗∗ p < .001
159
Not Admitted, Female
0.120
(0.325)
30.401
(7.497)
179003.786
(107239.963)
0.123
(0.329)
0.168
(0.299)
0.386
(0.401)
128.149
(34.394)
137.994
(34.794)
26.275
(4.993)
0.170
(0.376)
0.214
(0.410)
0.145
(0.352)
0.050
(0.217)
0.022
(0.148)
0.203
(0.402)
0.571
(0.495)
0.123
(0.328)
0.031
(0.174)
9763
Admitted, Female
0.122
(0.327)
31.778
(7.593)
180252.508
(103035.132)
0.159
(0.366)
0.187
(0.309)
0.353
(0.387)
122.925
(33.387)
133.954
(34.734)
26.249
(4.935)
0.156
(0.363)
0.161
(0.368)
0.166
(0.372)
0.107
(0.309)
0.146
(0.353)
0.309
(0.462)
0.340
(0.474)
0.088
(0.284)
0.010
(0.100)
3268
Not Admitted, Male
0.135
(0.342)
31.394
(7.518)
213254.889
(157252.309)
0.435
(0.496)
0.192
(0.308)
0.300
(0.368)
125.263
(34.406)
136.200
(35.076)
26.132
(5.025)
0.161
(0.367)
0.196
(0.397)
0.156
(0.363)
0.228
(0.420)
0.056
(0.230)
0.148
(0.355)
0.413
(0.492)
0.111
(0.314)
0.043
(0.204)
7165
Note: Table shows means and std. dev. of covariates for the full sample divided by treatment status and gender.
Observations
Affective/emotionel, pre-adult origin
Personality disorder
Nervous or stress-related
Affective disorder
Psychosis, schizophrenia
Disorder associated with substance use
Admitted in metropolitan area
Admitted in Copenhagen
Admitted in own municipality
Mother’s age at birth
Father’s months of schooling
Mother’s months of schooling
Welfare dependency in year -1
Unemployment degree in year -1
Previous crime (0/1)
Gross income in year -1
Age at admission
Immigrant
Table IIIA.7: Summary statistics by gender and treatment status
Admitted, Male
0.126
(0.332)
31.959
(7.451)
209616.192
(141716.768)
0.479
(0.500)
0.196
(0.307)
0.284
(0.359)
120.085
(33.558)
131.877
(35.292)
26.138
(5.227)
0.158
(0.365)
0.161
(0.367)
0.152
(0.359)
0.298
(0.458)
0.174
(0.379)
0.189
(0.392)
0.276
(0.447)
0.057
(0.232)
0.005
(0.073)
4081
Figure IIIA.1: Effect on Subsequent Crimes by Months Since 1st Contact for Outpatients
and 1st Discharge for Inpatients
Note: Figure shows 2SLS regression results of inpatient admission (0/1) on subsequent crimes where time 0
is defined as hospital discharge instead of initial contact. The dashed lines indicate 95% confidence intervals
and the dotted line indicate 90% confidence intervals. Standard errors clustered by hospital and month in
parentheses.
SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers years
of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history (dummy),
admitted in own municipality (dummy), greater CPH area (dummy), other metropolitan area (dummy),
year dummies.
Diagnosis controls include: Dummies for each F. diagnosis category from ICD-10.
160
Figure IIIA.2: Common Support for Treated and Untreated
Note: Figure shows areas of common support for treatment and control groups from a probit model of
treatment on two instruments (hospital specific contact intensity the two week prior to the individual’s
initial contact)
and SES and demographic controls: Gender (dummy), age at adm., mother’s age at birth, mothers years
of schooling, father’ age at birth, father’s years of schooling, mother has prior psych. history (dummy),
admitted in own municipality (dummy), greater CPH area (dummy), other metropolitan area (dummy),
year dummies
and diagnosis controls: Dummies for each F. diagnosis category from ICD-10.
161
Figure IIIA.3: Effect on Admission on Outcomes using Non-Linear Slope in First Stage,
2SLS Estimates
((a)) Admission
((b)) Contact
((c)) Crimes
((d)) Crimes
((e)) Overdose
((f)) Lesion
Note: Figures show main results on probability of re-admission, contact, admission for lesions, admission
for overdoses, and number of crimes re-estimated with a non-linear function in the first stage of the form:
D = γ1 z1 + γ2 z2 + γ3 1[z1 > 0.4] + γ4 1[z2 > 0.4] + γ5 1[z1 > 0.4]z1 + γ6 1[z2 > 0.4]z2 X 0 Π
The dashed lines indicate 95% confidence intervals and the dotted line indicate 90% confidence intervals.
Time 0 is month of initial contact. Standard errors clustered by hospital and month in parentheses. SES
and demographic controls include: Age at adm., mother’s age at birth, mothers years of schooling, father’
age at birth, father’s years of schooling, mother has prior psych. history (dummy), admitted in own
municipality (dummy), greater CPH area (dummy), other metropolitan area (dummy), year dummies.
162
B
Data Appendix
First, this section provides a brief overview of the trends in the number of patients and
inpatient capacity at psychiatric hospitals during the period studied. Second, the section
describes the data construction in detail, as a supplement to section 3 from the main text.
Trends in Psychiatric Hospital Treatments
Figure IIIB.1 shows the number of inpatient beds in Danish psychiatric hospitals per 1,000
inhabitants and the number of 20 to 64 year old patients per 1,000 persons in that age group
between 1996 and 2011.
Figure IIIB.1: Psychiatric beds and admissions, 1996-2011
ϭ
ϰ
Ϭ͕ϳϱ
ϯ
Ϭ͕ϱ
Ϯ
Ϭ͕Ϯϱ
ϭ
Ϭ
Ϭ
ϭϵϵϲ ϭϵϵϳ ϭϵϵϴ ϭϵϵϵ ϮϬϬϬ ϮϬϬϭ ϮϬϬϮ ϮϬϬϯ ϮϬϬϰ ϮϬϬϱ ϮϬϬϲ ϮϬϬϳ ϮϬϬϴ ϮϬϬϵ ϮϬϭϬ ϮϬϭϭ
EŽ͘ĞĚƐͬϭϬϬϬŝŶŚĂďŝƚĂŶƚƐ
ĚŵŝƐƐŝŽŶƐͬϭϬϬϬϮϬͲϲϰǇĞĂƌŽůĚƐ
Source: Own calculations on data from Statistics Denmark.
163
The Danish psychiatric system gradually downsized the number of inpatient beds from
1996–2011. The reductions from 1997 to 2001 were relatively small, from 0.80 in 1997 to
0.75 in 2001. From 2002 and onwards, the reductions increased in magnitude. In 2011
there were 0.53 beds per 1,000 inhabitants. The figure also shows that the number of adult
inpatients between the age of 20 and 64 increased from 2.36 in 1996 to 3.05 in 2004, only
to stagnate at around 2.90 until 2011. The downward trend in the number of psychiatric
beds resembles that of many Western countries (WHO, 2011a). The reductions to inpatient
capacities relative to the number of treated patients moved treatment from a hospital setting
to the patients’ home environments while also reducing the costs of treatment.
Construction of Mental Health Data
We constructed the mental health data using the Danish national psychiatric register (a
subset of the Danish patient register (LPR)) made available by Statistics Denmark. We
study the period 1999 to 2001, and only consider patients who had their first contact in
this period. This yields 50,439 patients. Next, we only include individuals who had their
first contact between the ages of 18 and 45 as we do not wish to focus on child or geriatric psychiatric treatment as admittance or non-admittance of these patients is not likely to
influence the outcomes we are interested in. Also, once in contact with a psychiatric care
facility, different conditions apply for these two groups relative to the average adult population. The age limitation reduces the sample from 50,439 to 31,248. We discard individuals
who are diagnosed with mental retardation, dementia, or disorders of early psychological
development because these patient groups suffer from chronic disorders and have little or
no labor market attachment. We also discard individuals who are diagnosed with eating
disorders or non-organic sexual dysfunctions in order to obtain a more homogeneous sample.
Individuals who enter treatment via the criminal justice system are also discarded. Finally,
a few countryside treatment facilities only treat 10-50 individuals per year and we discard
individuals who contact these facilities in order to not skew our instrument. Limiting the
164
diagnoses used, disregarding criminal justice court ordered psychiatric treatments, and setting a lower threshold for facility size leave us with a final sample of 24,277 individuals. The
final sample contains the following ICD-10 diagnosis categories:
(a) F10-F19: Mental and behavioral disorders due to psychoactive substance use
(b) F20-F29: Schizophrenia, schizotypal and delusional disorders
(c) F30-F39: Mood (affective) disorders
(d) F40-F48: Neurotic, stress-related and somatoform disorders
(e) F60-F69: Disorders of adult personality and behavior
(f) F90-F98: Behavioral and emotional disorders with onset usually occurring in childhood
and adolescence
(g) F99: Unspecified mental disorder
We control for each diagnosis category. Only 52 people in the data receives a diagnosis in
the range F90-F98, so they are grouped together with F99 diagnoses. Results do not change
if we group them apart.
We define the outcome of a contact on the basis of a patient’s experiences across an
entire day. I.e., if a patient contacts a psychiatric emergency ward and later in the day is
admitted to a normal psychiatric ward, that is treated as one incident (contact) leading to
an admission. In order not to exclude people who show up late in the day, we use the same
procedure for patient who have their first contact at an emergency ward at day one and are
admitted to a normal word at day two. We distinguish between admittance to inpatient
care, admittance into outpatient care, and no admittance. We define the treatment variable
as admittance to inpatient care.
165
Construction of the Instrument
We used the Danish National Psychiatric Register to obtain the number of unique individual
contacts to each hospital each day for the period 1998-2001 for all ages and types of diagnoses.
We included the year 1998 in order to construct the instrument as a contact intensity measure
as shown in Equation 1. We then computed the number of weekly contacts separately for the
two seven day periods prior to a person’s first contact by aggregating the number across day
-1 to -7, and day -8 to -14. This gave us our numerators. In order to obtain the denominator,
which measures the seven day period with the highest number of contacts within the last
365 days, we calculated the aggregated number for all successive seven days combination
from the day prior to an individual’s contact and going backward 365 days. We then used
the highest number of contacts measured across a seven day period as the denominator. The
two fractions made up the instruments.
Construction of Covariates
We constructed covariate data using a number of databases. Unique individual identification
numbers allowed us to directly link observations across registers, and also link information
on patients with information on their parents and potential spouse. We used the following
databases:
(a) Danish demographic database (FAIN), from where we obtained age, ethnicity, and
municipality of residence for year of first contact.
(b) The register based labor force database (RAS), unemployment register (CRAM), and
the Danish Rational Economic Agents Model (DREAM) to obtain information on
unemployment degree and public dependency degree the year prior to first contact.
(c) The database of individual usage of health services (SYIN) to obtain information on
166
admittances to hospital for somatic reasons as well as visits to GP and specialist doctors
the year prior to first contact.
(d) The educational database (UDDA) to obtain information on parental schooling. We
obtain the information for each year since 1981, and use the information recorded
closest to the year of first contact.
(e) The criminal justice databases on convictions (KRAF) and indictments (KRIN) to
obtain information on prior criminality. We use information of whether an individual
ever has received a conviction for a non-traffic related offense or felony from 1980 and
until the year before first contact.
(f) The income database (INDK) to obtain information on gross income reported the year
before first contact.
Construction of Outcomes
We measured all outcomes for the following three years after first contact. Some were
measured quarterly, others annually. The following paragraphs provide details on how we
constructed the different measures.
Contacts and Admissions We followed each patient in the Danish national psychiatric
register data for the 36 subsequent months after first contact measured quarterly. Contact
was constructed as an absorbing state dummy, indicating if the patient had contact again to a
psychiatric hospital during this period. Admission was constructed as a subset of the contact
dummy, indicating if the patient ever was admitted as an inpatient following a contact after
first contact.
Crime Using the criminal justice databases on convictions (KRAF) and indictments (KRIN)
we constructed the crime variable as a quarterly count variable that aggregated all criminal
167
convictions received by an individual in the 36 months following first contact. We excluded
traffic violations.
Hospitalizations for Self-harm We constructed two quarterly outcomes for self-harm:
whether an individual was hospitalized due to (a) an overdose; and (b) lesions. We constructed both measures as absorbing state dummies over a 36 month period. We used data from
the Danish national patient register (LPR).
Labor Market Outcomes We use the register based labor force database (RAS) to obtain
annual information on individual’s labor market position for the three years after contact.
We define three categories: employed, unemployed, and outside the labor force. Employed
entails any form of paid work, either as an employee or as self-employed. Unemployed entails
receiving either social assistance or unemployment insurance while being available for the
labor market or undertaking workfare. Outside the labor force entails receiving public welfare
without work or workfare requirements. We also obtain the same information for patients’
spouses. The information is obtained at the end of November for each year.
168
DEPARTMENT OF ECONOMICS AND BUSINESS
AARHUS UNIVERSITY
SCHOOL OF BUSINESS AND SOCIAL SCIENCES
www.econ.au.dk
PhD Theses since 1 July 2011
2011-4
Anders Bredahl Kock: Forecasting and Oracle Efficient Econometrics
2011-5
Christian Bach: The Game of Risk
2011-6
Stefan Holst Bache: Quantile Regression: Three Econometric Studies
2011:12
Bisheng Du: Essays on Advance Demand Information, Prioritization and Real Options
in Inventory Management
2011:13
Christian Gormsen Schmidt: Exploring the Barriers to Globalization
2011:16
Dewi Fitriasari: Analyses of Social and Environmental Reporting as a Practice of
Accountability to Stakeholders
2011:22
Sanne Hiller: Essays on International Trade and Migration: Firm Behavior, Networks
and Barriers to Trade
2012-1
Johannes Tang Kristensen: From Determinants of Low Birthweight to Factor-Based
Macroeconomic Forecasting
2012-2
Karina Hjortshøj Kjeldsen: Routing and Scheduling in Liner Shipping
2012-3
Soheil Abginehchi: Essays on Inventory Control in Presence of Multiple Sourcing
2012-4
Zhenjiang Qin: Essays on Heterogeneous Beliefs, Public Information, and Asset
Pricing
2012-5
Lasse Frisgaard Gunnersen: Income Redistribution Policies
2012-6
Miriam Wüst: Essays on early investments in child health
2012-7
Yukai Yang: Modelling Nonlinear Vector Economic Time Series
2012-8
Lene Kjærsgaard: Empirical Essays of Active Labor Market Policy on Employment
2012-9
Henrik Nørholm: Structured Retail Products and Return Predictability
2012-10
Signe Frederiksen: Empirical Essays on Placements in Outside Home Care
2012-11
Mateusz P. Dziubinski: Essays on Financial Econometrics and Derivatives Pricing
2012-12
Jens Riis Andersen: Option Games under Incomplete Information
2012-13
Margit Malmmose: The Role of Management Accounting in New Public Management
Reforms: Implications in a Socio-Political Health Care Context
2012-14
Laurent Callot: Large Panels and High-dimensional VAR
2012-15
Christian Rix-Nielsen: Strategic Investment
2013-1
Kenneth Lykke Sørensen: Essays on Wage Determination
2013-2
Tue Rauff Lind Christensen: Network Design Problems with Piecewise Linear Cost
Functions
2013-3
Dominyka Sakalauskaite: A Challenge for Experts: Auditors, Forensic Specialists and
the Detection of Fraud
2013-4
Rune Bysted: Essays on Innovative Work Behavior
2013-5
Mikkel Nørlem Hermansen: Longer Human Lifespan and the Retirement Decision
2013-6
Jannie H.G. Kristoffersen: Empirical Essays on Economics of Education
2013-7
Mark Strøm Kristoffersen: Essays on Economic Policies over the Business Cycle
2013-8
Philipp Meinen: Essays on Firms in International Trade
2013-9
Cédric Gorinas: Essays on Marginalization and Integration of Immigrants and Young
Criminals – A Labour Economics Perspective
2013-10
Ina Charlotte Jäkel: Product Quality, Trade Policy, and Voter Preferences: Essays on
International Trade
2013-11
Anna Gerstrøm: World Disruption - How Bankers Reconstruct the Financial Crisis:
Essays on Interpretation
2013-12
Paola Andrea Barrientos Quiroga: Essays on Development Economics
2013-13
Peter Bodnar: Essays on Warehouse Operations
2013-14
Rune Vammen Lesner: Essays on Determinants of Inequality
2013-15
Peter Arendorf Bache: Firms and International Trade
2013-16
Anders Laugesen: On Complementarities, Heterogeneous Firms, and International
Trade
2013-17
Anders Bruun Jonassen: Regression Discontinuity Analyses of the Disincentive
Effects of Increasing Social Assistance
2014-1
David Sloth Pedersen: A Journey into the Dark Arts of Quantitative Finance
2014-2
Martin Schultz-Nielsen: Optimal Corporate Investments and Capital Structure
2014-3
Lukas Bach: Routing and Scheduling Problems - Optimization using Exact and
Heuristic Methods
2014-4
Tanja Groth: Regulatory impacts in relation to a renewable fuel CHP technology:
A financial and socioeconomic analysis
2014-5
Niels Strange Hansen: Forecasting Based on Unobserved Variables
2014-6
Ritwik Banerjee: Economics of Misbehavior
2014-7
Christina Annette Gravert: Giving and Taking – Essays in Experimental Economics
2014-8
Astrid Hanghøj: Papers in purchasing and supply management: A capability-based
perspective
2014-9
Nima Nonejad: Essays in Applied Bayesian Particle and Markov Chain Monte Carlo
Techniques in Time Series Econometrics
2014-10
Tine L. Mundbjerg Eriksen: Essays on Bullying: an Economist’s Perspective
2014-11
Sashka Dimova: Essays on Job Search Assistance
2014-12
Rasmus Tangsgaard Varneskov: Econometric Analysis of Volatility in Financial
Additive Noise Models
2015-1
Anne Floor Brix: Estimation of Continuous Time Models Driven by Lévy Processes
2015-2
Kasper Vinther Olesen: Realizing Conditional Distributions and Coherence Across
Financial Asset Classes
2015-3
Manuel Sebastian Lukas: Estimation and Model Specification for Econometric
Forecasting
2015-4
Sofie Theilade Nyland Brodersen: Essays on Job Search Assistance and Labor Market
Outcomes
2015-5
Jesper Nydam Wulff: Empirical Research in Foreign Market Entry Mode
2015-6
Sanni Nørgaard Breining: The Sibling Relationship Dynamics and Spillovers
2015-7
Marie Herly: Empirical Studies of Earnings Quality
2015-8
Stine Ludvig Bech: The Relationship between Caseworkers and Unemployed Workers
2015-9
Kaleb Girma Abreha: Empirical Essays on Heterogeneous Firms and International
Trade
2015-10
Jeanne Andersen: Modelling and Optimisation of Renewable Energy Systems
2015-11
Rasmus Landersø: Essays in the Economics of Crime
ISBN: 9788793195196