essays in the economics of crimeessays in the economics of crime by rasmus landersø a phd thesis...

Essays in the Economics of Crime

2015-11

Rasmus Landersø

PhD Thesis

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

1 Introduction 3

2 Background 72.1 The Reform of the Penal Code . . . . . . . . . . . . . . . . . . . . . . . . . . 102.2 Imprisonment in Denmark . . . . . . . . . . . . . . . . . . . . . . . . . . . . 14

3 Data 16

4 Econometric Framework 21

5 Results 245.1 Macroeconomic Trends . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 295.2 Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33

6 Conclusion 36

References 38

A Supplementary Results 43

B Data Appendix 48

II School Starting Age and the Crime-Age Profile 53

1 Introduction 55

2 Institutional settings and mechanisms 582.1 Educational Institutions and School Starting Age . . . . . . . . . . . . . . . 582.2 Institutions Guarding Juvenile Crime . . . . . . . . . . . . . . . . . . . . . . 60

3 Methodology 62

4 Data 64

5 Results 695.1 Timing of Birth Within the Calendar Year and School Starting Age . . . . . 695.2 Crime Results: 2SLS . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 705.3 Heterogeneity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 785.4 Potential Mechanisms and Effects on Alternative Outcomes . . . . . . . . . . 79

6 Conclusion 83

References 84


III The Effects of Admissions to Psychiatric Hospitals 105

1 Introduction 107

2 Background 1092.1 Institutional framework - mental health care in Denmark . . . . . . . . . . . 111

3 Data 112

4 Econometric Framework 121

5 Results 1245.1 2SLS Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1255.2 Gender and age differences . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1345.3 Marginal Treatment Effects . . . . . . . . . . . . . . . . . . . . . . . . . . . 1385.4 Effect of Admittance on Spouses’ Labour Market Outcomes . . . . . . . . . 144

6 Conclusion 145

References 147


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 job-

posting 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’ en-

devours. 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 psychiat-

ric 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 charac-

teristics. 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 experi-

ence 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. Fi-

nally, we identify additional sources of positive externalities of hospital admissions, as we

find that it increases the employment rates of patients’ spouses.

V

Resume

(Danish summary) Denne ph.d. afhandling bestar 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, sa fokuserer de tre artikler alle pa aspekter af risikoadfærd og forsøger at give en bedre

forstaelse 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 pavirker kriminelles efterfølgende indtægt, afhængighed

af overførselsindkomster og arbejdsløshedsrater. Den eksisterende litteratur om effekterne af

fængsling fokuserer primært pa den ekstensive margin og ikke pa den intensive margin: læng-

den af fængslingen. Pa 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 pavirkede primært kriminelle,

som aftjente domme pa 1 eller 2 maneder, 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 delta-

gelse i rehabilitering stiger med tiden brugt i fængsel, specielt i de første maneder. Derfor

er øget deltagelse i rehabilitering en sandsynlig mekanisme bag resultaterne. Indespær-

ringslængderne før reformen har sandsynligvis været sa 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 pavirkede 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 ogsa større chancer for at skifte opfat-

telse 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 ma-

nipulere 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 ar senere end loven

dikterer. For at omga denne højst selektive udvælgelse af, hvilke børn der starter senere og

tidligere, udnytter vi, at danske børn ofte starter i første klasse i det kalenderar, hvor de

fylder syv. Dette resulterer i et fuzzy regression discontinuity-design, der skubber SSA med

et ar for børn født lige omkring nytar. Herved undersøger vi sammenhænge mellem start

og fortsættelse af kriminel opførsel i forhold til et individs livsforløb og alder. Vi finder, at

starten pa kriminel løbebane er knyttet til et individs livsforløb og ikke til alder som sadan.

Til sammenligning er fortsat kriminel adfærd bade pavirket af alder savel 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 ogsa ny viden

omkring konsekvenserne af skolestartsalder pa længere sigt. Endelig finder vi, at effekterne

af skolestartsalder varierer mellem forældre med forskellige uddannelser og arbejdsmarked-

stilknytning.

I det tredje kapitel, The Effects of Admissions to Psychiatric Hospitals (skrevet sammen

med P. Fallesen) undersøger vi effekterne af at indlægge en patient pa et psykiatrisk hospital

ved første kontakt med psykiatrien, pa patientens videre kontakt og indlæggelse pa psykiat-

riske hospitaler, skade pa sig selv/selvmordforsøg, arbejdsmarkedstilknytning, kriminalitet

og pa patientens ægtefælles arbejdsmarkedsforhold. Vi tager højde for de fundamentale

VII

forskelle mellem individer, som bliver indlagt, og dem, der ikke bliver, ved at bruge in-

tensiteten 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. Pa kort sigt hjælper indlæggelse pa patientens direkte

behov, til fordel for bade patienten og eventuelle ofre af kriminelle handlinger. Indlæggelse

sænker selvpaførte skader savel som reducerer kriminalitet lige efter indlæggelse. Vi viser,

at reduktionen i kriminalitet er resultatet af fastholdelse/indespærring som følge af hospital-

sindlægelsen. Pa længere sigt viser indlagte individer en højere grad af institutionalisering,

som giver dem lavere arbejdsmarkedstilknytning. Vi identificerer ogsa en stor heterogen-

itet pa tværs af observerbare savel 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 op-

lever markante reduktioner i sandsynligheden for overdoser af alkohol/stoffer savel 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 im-

prove 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 spec-

ifications 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 confer-ence, the 2011 American Association of Criminology conference, Dennis Carlton, and an anonymous refereefor useful comments and suggestions. I also thank colleagues Signe Hald Andersen, Peer Skov, and LarsHøjsgaard Andersen for helpful discussions and Linda Kjær Minke for providing data from her study ofDanish 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., Fougere 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 out-

comes 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’ incar-

ceration 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’ unem-

ployment 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

1The 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.

2The time paths of the unemployment rates and earnings display a spike/dip prior to incarceration. Thespikes/dips could indicate the initiation of a criminal trajectory, while they also display great resemblanceto Ashenfelter’s dip (Ashenfelter (1978)). As noted with regard to effect evaluation in labor economics, thespikes/dips here could imply self-selection into incarceration. However, as there is no difference between thetreatment 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 character-

istics 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 PublicTransfers for the Control and Treatment Groups

0,3

0,4

0,5

0,6

0,7

0,8

0,9

1

600

800

1000

1200

1400

1600

1800

Ra

te

US

$, 2

00

5

0

0,1

0,2

0

200

400

-60 -48 -36 -24 -12 0 12 24 36 48Months

Earnings, control Earnings, treatment

Unemployment, control Unemployment, treatment

Other public transfers, control 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 pro-

ductivity 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.

3The economic literature on social capital is more sparse than that on human capital. For an introductione.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 crim-

inologist 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 com-

poses 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 in-

carceration, 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 signi-

ficant 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 signi-

ficant 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 endo-

genous nature of crime and labor market outcomes must be addressed. Different incarcera-

tion 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 time-

4A programme designed to help newly-released prisoners rehabilitate, see Needles (1996).5Inmates 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.

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 het-

erogeneous 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]

6Though an internal review (Ministry of Justice, Research Unit (2007)) concluded that the reform didnot 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 (pre-

and 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.

7I will introduce the sample formally in section 3.8The 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.

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 viol-

ent 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 Novem-

ber 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

9For a legal definition of the term see https://www.retsinformation.dk/Forms/R0710.aspx?id=126465. Ineveryday terms ordinary violence comprises assaults and fights from which the victim does not suffer majorpermanent injuries.

10In 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, environmentaloffences, or military crimes.

12

Figure I.3: Composition of Crimes from Dec. 2000 to Nov. 2003 for Men Aged 18-45

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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.

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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 Observations

Less than 1 month 0.202 109Between 1 and 2 months 0.244 41Between 2 and 3 months 0.414 29Between 3 and 6 months 0.500 72More than 6 months 0.534 442

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 incarcer-

11http://www.kriminalforsorgen.dk/Default.aspx?ID=1256, (accessed 04/11-2014)12After 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 admissioninterviews, except that the “incarceration lengths obviously limit the type of in-jail rehabilitation that canbe put into effect.” Nevertheless, Minke (2010), which to my knowledge is the only coherent analysis ofrehabilitation possibilities in Danish jails, finds that rehabilitation posibilities during short incarcerationspells are very limited, even if the inmates themselves request treatment, assistance or training.

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 re-

cords, 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

13See Appendix B for a detailed description of the construction of data.14Only Danish residents are included in the registers.15A supplementary register used in the Danish Rational Economic Agent Model (DREAM), an

general equilibrium model used for forecasting. The database contains information on every Dan-ish 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.

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

16Women and individuals aged 46 or older at the time of the crime made up 3.7% of the sample at thispoint.

17I exclude the individuals who are not included in data the for at least 12 months prior to the incarcerationin 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 thesefrom the sample. This censoring applies to 43 and 40 persons from the treatment and control groupsrespectively (2.5 and 2.2 percent of the final sample). The estimation results, with various imputations forthe attrites’ missing periods instead of the above mentioned censoring, do not differ qualitatively from theresults presented throughout the paper. The auxiliary estimation results can be obtained from the authoron 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 characterist-

ics 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 unemploy-

ment, 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 trans-

formed 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 depend-

18As 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 Control Treatment Significant Randomdifference weighted

Variable sampleMeasured 12 months prior to incarcerationUnemployed 0.33 0.33 0.33 0.05

(0.46) (0.46) (0.45) (0.21)

Dependent on other public transfers 0.15 0.15 0.15 0.15(0.48) (0.35) (0.34) (0.36)

Earnings (USD 2005) 1,473 1,510 1,417 2,993(1,922) (1,980) (1,862) (2,567)

Age 28.13 28.40 27.86 28.61(7.80) (7.83) (7.76) (7.70)

Married 0.23 0.26 0.20 ∗∗∗ 0.26(0.42) (0.44) (0.40) (0.44)

Cohabitant 0.28 0.28 0.27 0.45(0.45) (0.45) (0.44) (0.50)

Have children 0.36 0.38 0.34 ∗ 0.34(0.48) (0.49) (0.48) (0.47)

Non-western immigrants or descendants 0.12 0.11 0.13 0.07(0.48) (0.32) (0.34) (0.25)

No job-qualifying education 0.67 0.68 0.67 0.51(0.47) (0.47) (0.47) (0.50)

Vocational or skilled 0.23 0.23 0.23 0.31(0.42) (0.42) (0.42) (0.46)

Upper secondary or higher 0.10 0.09 0.10 0.18(0.30) (0.30) (0.30) (0.39)

Convicted before 0.83 0.83 0.83 0.21(0.37) (0.37) (0.37) (0.41)

Convicted of a violent crime before 0.48 0.50 0.47 0.04(0.50) (0.50) (0.50) (0.20)

Convicted of a property crime before 0.67 0.67 0.66 0.15(0.47) (0.47) (0.48) (0.36)

Months since 1st date of crime leading to an indictment 109 110 108 -(83) (81) (84)

Months since 1st date of crime leading to an conviction 98 99 97 -(84) (82) (85)

Months since 1st incarceration 46 47 44 -(73) (71) (75)

Number of previous convictions 4.44 4.45 4.43 -(5.89) (5.62) (6.15)

N 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 inmean sample by treatment status: + p < 0.10, ∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001Random sample has been drawn from the full Danish population in 2002 with similar age distribution as main sample (herelabelled 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 so-

cioeconomic 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:

δATT = 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 post-

reform 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 δATT 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 obser-

vation 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 rela-

tionship 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 differences-

in-differences (DD)19 model:

∆yis = β∆xis +s=6∑

s=2

γsds+s=6∑

s=1

δDDs Di +∆eis (3)

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 δDDs captures the

difference between the control and treatment group in each of the six month periods since

release. Hence, δDDs 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

19Here, differences-in-differences imply the difference between the pre- and post-incarceration outcomes ofthe post-reform offenders relative to the difference between the pre- and post-incarceration outcomes of thepre-reform offenders.

20∆x includes a constant term, changes in marital status, changes in children, three indicators of changesin 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 δDDs 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∑

s=2

µsds+s=6∑

s=1

γsds · Vi +s=6∑

s=1

ρsDi +s=6∑

s=1

δDDDs Di · Vi +∆eis (4)

21Using the reform as an instrumental variable is an alternative estimation strategy relying on similarassumptions. If an IV strategy was employed instead, the DD estimates would be normalized by a firststage regression. The DD estimates should be divided by the mean increase as result of the reform if thetreatment variable was measured in days of incarceration. This would result in smaller estimates than Iobtain with the differences-in-differences strategy. The DD estimates should be rescaled by the increase inthe fraction treated, if the treatment variable was defined as a dummy variable of experiencing incarcerationbelow or above a threshold (e.g. 35 days see table IA.5). This would result in larger estimates than I obtainwith 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 δDDDs 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 estim-

ates 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

22The wild bootstrap randomly assigns extra noise to the estimates. As proposed by Davidson & Flachaire

(2008); Flachaire (2005), I multiply each estimated error ∆eis with ρis ={

−1 with probability 0.51 with probability 0.5

, so

E (ρis) = 0 and σ2ρ = 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 Unemployment Dep. on other Earningstransfers

(1) (2) (3) (4) (5) (6)DD DDD DD DDD DD DDD

1-6 months after release -0.033* -0.105*** 0.005 0.044 87.49 147.45(0.019) (0.039) (0.014) (0.029) (63.00) (113.93)

7-12 months after release -0.055*** -0.129*** 0.005 0.009 150.99** 171.75(0.021) (0.043) (0.015) (0.033) (76.16) (122.52)

13-18 months after release -0.067*** -0.121*** 0.04 0.007 126.84 130.85(0.020) (0.043) (0.016) (0.033) (77.74) (133.53)

19-24 months after release -0.071*** -0.132*** 0.004 -0.014 255.53*** 303.50**(0.021) (0.039) (0.017) (0.032) (82.18) (138.38)

25-30 months after release -0.076*** -0.074* 0.007 -0.024 236.04*** 205.19(0.021) (0.043) (0.018) (0.034) (87.39) (152.65)

31-36 months after release -0.096*** -0.068 -0.001 0.010 393.04*** 219.33(0.020) (0.044) (0.019) (0.038) (86.35) (166.58)

R2 0.023 0.025 0.008 0.014 0.023 0.021N 1,748 2,388 1,748 2,388 1,748 2,388

Wald statistic (p-val) <0.001*** <0.001*** 0.998 0.801 <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

23Though it is customary, I do not use log earnings because a large proportion of the sample experiencelonger 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 zerowith one. The DD estimates do not differ qualitatively from those shown by table I.3 though the DDDestimates 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 pub-

lic 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 es-

timates 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 incar-

24In order to investigate the possibility of opposing effects within the composite measure of dependencyon other public transfers, I have estimated the model with a subdivision of this outcome into two generalcategories: 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 mar-ket programs; and second, mandatory programs required in order to be eligible for the receipt of benefits orpassive support without any requirements, such as sick leave, early retirement relating to lack of employabil-ity, etc. None of the benefits included in the second group are aimed at obtaining future employment on thelabor market. The first outcome category was unaffected by the reform, while there was a weak sign of anincrease in the second category as a consequence of the reform. However, this result was neither sufficientlyrobust 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 unem-

ployment and dependency on other public transfers). The results using this outcome did not change anyconclusions, 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



1-6 months after release -0.037* -0.104*** 0.005 0.043 87.49 149.93(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)

13-18 months after release -0.072*** -0.122*** 0.04 0.007 126.84 132.30(0.020) (0.041) (0.016) (0.033) (107.99) (137.20)

19-24 months after release -0.075*** -0.134*** 0.004 -0.014 255.53*** 307.99**(0.021) (0.039) (0.017) (0.033) (109.21) (144.60)

25-30 months after release -0.080*** -0.075* 0.007 -0.026 236.04*** 210.44(0.021) (0.042) (0.018) (0.036) (156.17) (154.61)

31-36 months after release -0.100*** -0.067 -0.001 0.009 393.04*** 223.60(0.020) (0.043) (0.019) (0.038) (260.28) (164.27)

R2 0.027 0.033 0.009 0.015 0.032 0.033N 1,748 2,388 1,748 2,388 1,748 2,388

Wald statistic (p-val) <0.001*** <0.001*** 0.999 0.775 <0.001*** 0.043**


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 incarcera-

tion 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.

25In the appendix.26In the appendix.27Table IA.4 shows balancing tests for this restricted sample.28I have also performed this robustness check with persons sentenced to imprisonment for a crime com-

mitted 2, 3, 5, 6, 7, 8, and 9 months prior to or after the implementation of the reform. The results can beobtained from the author on request.

29

Table I.5: Estimation Results, Reduced Sample



1-6 months after release -0.046 -0.146* 0.031 0.062 51.54 145.87(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 -0.128*** -0.190* 0.023 0.007 287.15 229.77(0.044) (0.105) (0.038) (0.077) (150.25) (287.04)

19-24 months after release -0.059 -0.181* 0.004 0.005 205.50 170.64(0.047) (0.102) (0.041) (0.081) (166.92) (312.15)

25-30 months after release -0.040 -0.015 0.013 -0.076 -17.75 66.98(0.050) (0.102) (0.043) (0.087) (187.67) (330.36)

31-36 months after release -0.034 -0.032 0.014 0.026 95.16 90.28(0.046) (0.099) (0.042) (0.089) (174.60) (349.71)

R2 0.031 0.043 0.013 0.021 0.043 0.041N 351 484 351 484 351 484

Wald statistic (p-val) 0.020** 0.047** 0.832 0.608 0.250 0.914


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

29Again, I have estimated the model using total dependency on public transfers. The results were notsignificantly different from those for unemployment. Therefore, they suggest that the rate of unemploymentdropped as a consequence of the reform, while there was no attrition from the labor market, as the reformdid 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 placebo-

reform 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 placebo-

reforms 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

30The sample size of each placebo-reform is approximately equal to the sample size of the main sampleconstructed around the actual reform. The individual placebo-control groups and placebo-treatment groupsare also approximately of equal size.

31I have also estimated the effects of the placebo-reform for the DD model. The results and overall patterndo not differ qualitatively form DDD results reported in figure I.4. The DD placebo results can be obtainedfrom 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

1

Le

ve

l of sig

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Timing of pseudo-reform

Earnings Unemployment

0.05

0.1

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 placebo-

reforms 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 unreason-

able 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 offend-

ers 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

32Produced by Flemming Balvig, Professor of Criminal Law, in cooperation with The Danish Bar andLaw 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:

πc + πa

πc

[

E (X | P = 1, D = 1)−πa

πc + πa

E (X | P = 1, D = 0)

]

(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, unem-

ployment 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 incarcera-

tion 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 ac-

cording 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

33The 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 self-

selection.

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 DD DDD

1-6 months after release 0.216 0.270(0.173) (0.341)

7-12 months after release 0.489*** 0.416(0.193) (0.368)


19-24 months after release 0.689*** 0.740*(0.222) (0.395)



R2 0.015 0.031N 1,748 2,388

Wald statistic (p-val) <0.001*** 0.158


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

Tab

leIA

.2:Estim

ationResultsFrom

Start

ofIncarceration

Periods

Full

emp.in

jail

Unem.asbefore

jail

Full

unem.in

jail

DD

DDD

DD

DDD

DD

DDD

1-6mon

thsafterincarcerationstart

-0.029

-0.097

*-0.032

***

-0.094

***

-0.001

-0.063

(0.018)

(0.039)

(0.017)

(0.039)

(0.019)

(0.043)

7-12

mon


-0.057

***

-0.138

***

-0.055

**-0.134

***

-0.051

***

-0.124

***

(0.021)

(0.041)

(0.021)

(0.041)

(0.021)

(0.042)

13-18mon


-0.050

***

-0.108

***

-0.048

***

-0.106

***

-0.049

***

-0.106

***

(0.021)

(0.041)

(0.021)

(0.041)

(0.021)

(0.411)

19-24mon


-0.074

***

-0.120

***

-0.075

***

-0.121

***

-0.075

***

-0.120

***

(0.021)

(0.040)

(0.021)

(0.039)

(0.021

)(0.039)

25-30mon


-0.065

***

-0.054

-0.065

***

-0.054

-0.065

***

-0.054

(0.021)

(0.042)

(0.021)

(0.042)

(0.021

)(0.042)

31-36mon


-0.097

***

-0.066

-0.098

***

-0.068

-0.098

***

-0.067

(0.020)

(0.043)

(0.020)

(0.043)

(0.020

)(0.043)

R2

0.016

0.021

0.022

0.025

0.064

0.056

N1,748

2,388

1,748

2,388

1,748

2,388

Waldstatistic(p-val)

<0.001*

**<0.001*

**<0.001*

**<0.001*

**<0.001*

**<0.001*

**

Significance

levels:

∗:p<10%

∗∗:p<5%

∗∗∗:p<1%

Note:

Tab

leshow

sDD

andDDD

regression

resultswheretime0is

thestartof

incarcerationinsteadof

releasefrom

jail.

Thetable

show

stheresultsforunem

ploymentas

outcom

eusingthreedifferentim

putation

sof

in-jailunem

ployment:

Fullem

ployment,

unem

ploymentrate

asbeforeincarceration,an

dfullunem

ployment.

Theblock-bootstrap

ped

stan

darderrors

arereportedin

parentheses

below

theestimates

44

Table IA.3: Estimation Results Discounted Earnings

Periods DD DDD


7-12 months after release 149.878** 167.508(75.598) (123.980)


19-24 months after release 253.323*** 299.236**(81.590) (143.677)



R2 0.023 0.026N 1,748 2,388

Wald statistic (p-val) <0.001*** 0.059*


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 Full sample Control Treatment Sign. diff.

Measured 12 months prior to incarcerationUnemployed 0.32 0.33 0.30

(0.45) (0.46) (0.44)Dependent on other public transfers 0.18 0.17 0.16

(0.35) (0.37) (0.33)Earnings (USD 2005) 1,532 1,427 1,481

(1,891) (1,964) (1,925)Age 28.99 29.27 28.71

(7.91) (7.97) (7.87)Married 0.21 0.25 0.18

(0.41) (0.43) (0.38)Cohabitant 0.29 0.32 0.27

(0.46) (0.45) (0.47)Have children 0.39 0.41 0.37

(0.49) (0.49) (0.48)Non-western immigrants or descendants 0.13 0.16 0.10 ∗

(0.34) (0.37) (0.30)No job-qualifying education 0.67 0.63 0.70

(0.47) (0.48) (0.46)Vocational or skilled 0.23 0.26 0.21

(0.42) (0.44) (0.41)Upper secondary or higher 0.10 0.11 0.09

(0.30) (0.31) (0.29)Measured at the start of incarcerationHave been convicted before 0.87 0.90 0.85

(0.33) (0.31) (0.35)Have been convicted of a violent crime before 0.52 0.56 0.48

(0.50) (0.50) (0.50)Have been convicted of a property crime before 0.68 0.67 0.69

(0.47) (0.46) (0.47)Months since 1st date of crime leading to an indictment 117 118 117

(84) (83) (85)Months since 1st date of crime leading to an conviction 106 106 106

(86) (85) (87)Months since 1st incarceration 52 50 55

(78) (75) (81)Number of previous convictions 4.96 4.95 4.937

(6.06) (6.01) (6.12)

N 351 172 179

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 samplelength to +35 days

Measured 12 months prior to incarcerationUnemployed 0.24 0.33Dependent on other public transfers 0.12 0.15Earnings (USD 2005) 1,406 1,473Age 24.89 28.13Married 0.00 0.23Cohabitant 0.42 0.28Have children 0.25 0.36Non-western immigrants or descendants 0.17 0.12No job-qualifying education 0.72 0.67Vocational or skilled 0.18 0.23Upper secondary or higher 0.10 0.10Measured at the start of incarcerationHave been convicted before 0.83 0.83Have been convicted of a violent crime before 0.05 0.48Have been convicted of a property crime before 0.56 0.67Months since 1st date of crime leading to an indictment 101 109Months since 1st date of crime leading to an conviction 83 98Months since 1st incarceration 25 46Number of previous convictions 2.90 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 ofproperty crimes (Penal Law), number of simple violent crimes (as in the paper) indexed to the number ofcrimes in each category in May 2002 for males aged between 18 and 45 at the time of the crime. Thevertical 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.

34See 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 inform-

ation 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 individual-

specific 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 vari-

ous 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 vari-

ables. 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 Full sample Control Treatment

Unemployment 0.37 0.36 0.39(0.47) (0.47) (0.47)

Depedendency of other public transfers 0.17 0.19 0.15(0.36) (0.38) (0.34)

Earnings 864 802 926(1,521) (1,454) (1,585)

Age 26.84 27.28 26.41(7.62) (7.67) (7.55)

Married 0.19 0.20 0.19(0.40) (0.40) (0.39)

Cohabitant 0.25 0.25 0.25(0.43) (0.43) (0.43)

Have children 0.28 0.30 0.26(0.45) (0.46) (0.44)

Non-western immigrants or descendants*** 0.20 0.17 0.24(0.40) (0.37) (0.43)

No job-qualifying education 0.73 0.73 0.73(0.45) (0.44) (0.45)

Vocational or skilled 0.15 0.15 0.16(0.36) (0.36) (0.37)

Upper secondary or higher 0.12 0.12 0.11(0.32) (0.32) (0.32)

N 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 BeNAHumboldt University, ISER, University of Essex, University of Sussex, KORA, CAM, University of St. Gal-len, Xiamen University, the joint University of Bergen & UCL workshop 2013, the workshop on “Economicsof Successful Children” at Aarhus University 2013, the University of Chicago’s Life Cycle and Inequalityworking group as well as participants at ESPE 2013, EALE 2013, ASSA 2014, the IZA YSW at GeorgetownUniversity 2014, and at the DGPE workshop are appreciated. Financial support from the Danish Councilfor Strategic Research (CSER, 09-070295) and CIRRAU (Simonsen) is gratefully acknowledged. The usualdisclaimer 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 educa-

tional 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

1They study urban schools and find that increasing the number of school days reduce arrests for propertycrimes but increases arrests for violent crimes. While the effect on property crime is thought to be dueto incapacitation, the effect on violent crime is thought to be a network effect (spending more time withcriminal 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 pre-

school 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

Ockert (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.

2Anderson 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.

3One note of caution is that crime reports to the police may differ according to whether youth are inschool or not. If criminal events taking place in school are treated differently than criminal events takingplace outside school, this would lead to similar findings. This issue is likely more relevant for violent crimethan 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 ad-

ministrative 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 Institutional settings and mechanisms

2.1 Educational Institutions and School Starting Age

During the period relevant for this study, Danish law stipulated that education was compuls-

ory 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 rela-

tionship 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 school-

ing 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

4The school starting regulations are not strictly enforced and exemptions are granted based on applicationsfrom the parents. Exemptions are granted by the local municipality if it is considered beneficial for the child’sdevelopment. School start can only be delayed by one year, and school is no longer compulsory from July 31in the calendar year of the child’s 17th birthday even if 9th grade has not been completed. School childrendo not pass or fail grades, but in collaboration with the parents, the school principal can decide that childrepeats a grade or jumps a grade again if this is considered beneficial for the childs development. For moredetails consult the Danish Law of public schools.

5It was also possible to complete a voluntary 70th grade before continuing on to a vocational or academicpath.

6A 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

7UNI-C (2009) documents this and describes background characteristics of children across school startingage.

8This pattern is clear from Figure A1 that shows the distributions of social and emotional difficulties atage 4 among punctual and late school starters, drawn from an auxiliary data source (the Danish LongitudinalSurvey of Children).

9Fredriksson and Ockert (2013) do find earnings gains for individuals with low-educated parents.10A 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


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,

11http://www.unicef.org/pon97/p56a.htm.12The 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.13See the Danish Service Act.

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 +X ′

iγ + εi (1)

where Y denotes the outcome, X observable characteristics,15 and ε unobservable char-

acteristics. 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 Ockert (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 pre-

scribed. We can therefore instrument SSA with a dummy for being born immediately after

14The reported victimisation rates reveal what proportion of a sample of 2000 individuals report that theythemselves or persons in their households had experienced one of ten types of conventional crimes (such asvehicle-related crime, theft of personal property and contact crime), see OECD (2009).

15X 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’ educationand 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 instru-

ments 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 mid-

1993 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.

16Using charges instead of convictions enables us to use three additional years of data because the timeinvolved in processing cases through courts and subsequent appeals is obviated. Conclusions are robust tousing 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

Girls BoysAge All Property Violence Other N All Property Violence Other N15 0.019 0.018 0.002 0.001 48,546 0.039 0.033 0.006 0.007 50,38316 0.032 0.029 0.003 0.003 48,546 0.081 0.059 0.014 0.029 50,38317 0.044 0.037 0.005 0.006 48,546 0.140 0.081 0.025 0.077 50,38318 0.054 0.043 0.007 0.010 48,546 0.189 0.101 0.036 0.119 50,38319 0.069 0.049 0.009 0.021 43,668 0.243 0.118 0.047 0.174 45,36820 0.083 0.053 0.010 0.034 39,037 0.290 0.131 0.057 0.222 40,60621 0.096 0.055 0.010 0.045 34,559 0.327 0.141 0.065 0.262 36,01222 0.106 0.056 0.011 0.057 30.209 0.358 0.147 0.070 0.295 31,40523 0.116 0.056 0.011 0.068 26,093 0.383 0.151 0.074 0.323 26,93724 0.124 0.057 0.012 0.075 22,125 0.402 0.154 0.076 0.345 22,78125 0.133 0.057 0.012 0.086 18,240 0.417 0.156 0.079 0.362 18,72326 0.138 0.057 0.012 0.092 14,630 0.429 0.156 0.081 0.375 14,94927 0.143 0.057 0.011 0.100 11,045 0.439 0.157 0.082 0.388 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 convic-

tions 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

17Due to space considerations, we have chosen only three broad categories of crimes. Different classifica-tions 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.

18As an additional check we report results from the first stage regression at various grade levels by use ofthese 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 in-

dividual 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. Im-

portantly, 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 inform-

ation 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 assuggested by Elder and Lubotsky (2009), our results will be biased towards zero.

19The APGAR score ranges from zero to 10 and summarizes the health of a newborn child based on fivesimple criteria: Appearance, Pulse, Grimace, Activity and Respiration.

20For 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 1981etc.

21The difference in birth weight is for example 16 grams, which corresponds to 0.03 point difference in IQaccording to Black et al. (2007). Figure IIA.4 shows the variation of birthweight on either side of the cutoff. Even though the (numerically small) difference is significantly different for boys and girls, there is nosystematic pattern across dates.

68

Table II.2: Balancing Tests: Regression of Instrument on Background Characteristics

Girls BoysF-statistic 0.53 0.70P-value 0.94 0.81N 48,546 50,383Distance to cut-off X XCovariates X X

Note: Table shows F-statistics and associated p-values from regressions of birth-month (January=1)on the full set of covariates (background characterist-ics presented in Table IIA.3 and cohort fixed effects)as well as distance to cut-off in days.

5 Results

5.1 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 F-

statistic easily passes the Staiger-Stock rule-of-thumb.With one endogenous variable and 1

instrument, F should be greater than 10,23

22Results are robust to including more flexible polynomials of the running variable.23As 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 firststage is literally unaffected by this approximation; for individuals born Dec 2000-Jan 2001, we can comparefirst stage as measured by being old-for-grade in preschool versus 2nd grade, while for individuals bornDec 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 theapproximation

69

Table II.3: First Stage Estimation Results: Children Born in December and January

Girls BoysJanuary=1 0.245∗∗∗ 0.244∗∗∗ 0.172∗∗∗ 0.171∗∗∗

Days to cut-off, December -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗

Days to cut-off, January 0.003∗∗∗ 0.003∗∗∗ 0.001∗∗∗ 0.001∗∗∗

Constant 0.714∗∗∗ 2.282∗∗∗ 0.872∗∗∗ 1.540∗∗∗

N 48,546 50,383Cohort Fixed Effects X X X XRemaining covariates X XF-value for January dummy 877.29 891.59 574.01 576.22

Note: Table shows results from linear regressions of indicators for starting schoolat 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 TableIIA.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 (con-

ditional 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 individu-

als 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

24This is not driven by the smaller sample for which we observe outcomes at all ages. The estimate profileis 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

Figure

II.4:Estim

ationResults:

CrimeAtor

BeforeAge

byTypes

ofCrime

((a))Girls,property

((b))

Girls,violence

((c))Girls,other

crim

e

((d))

Boys,

property

((e))Boy

s,violence

((f))Boys,

other

crim

e

Note:

Figuresshow

theestimatedeff

ects

ofbeingold-for-gradebased

on2S

LSregression

son

theprobab

ilityof

property,violent,an

dother

crim

eat

(left)

andat

orbefore(right)

agiven

age.

Cut-off

dummy(Jan

uary=1)

usedas

instrument.

Con

ditioningsetincludes

distance

tocu

t-off

,cohortfixed

effects,an

dbackgroundcharacteristics

(see

Tab

leIIA.3).

Dashed

lines

indicate95

%confiden

ceintervals.

74

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


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 mid-

twenties 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.

25Even when we align outcomes by grade levels, we see a negative significant effect of being old-for-gradeon 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 in-

strument 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 Girls BoysSample Compliers T-value Sample Compliers T-value

Immigrant 0.04 0.02 4.99∗∗∗ 0.04 0.02 3.91∗∗∗

Parents married/cohabiting 0.79 0.81 -2.72∗∗ 0.79 0.83 -3.45∗∗∗

Apgar score=9 0.18 0.17 1.39 0.19 0.17 1.25Apgar score=8 0.07 0.06 2.74∗∗ 0.07 0.08 -2,39∗

Apgar score lower 0.08 0.09 -0.12 0.10 0.08 1.78Birth weight, grams 3349.43 3414.11 -5.90∗∗∗ 3473.43 3589.40 -7.21∗∗∗

Gestational length, weeks 39.55 39.61 -1.59 39.47 39.62 -2.67∗∗

Mother:Months of schooling 137.41 139.08 -2.49∗ 137.75 142.92 -5.87∗∗∗

Completed HS or equivalent 0.29 0.29 0.08 0.30 0.34 -3.51∗∗∗

Unemployed 0.13 0.11 3.00∗∗ 0.13 0.10∗ 2,31∗

Out of the labour force 0.11 0.10 1.29 0.11 0.09 1.59Age at birth of first child 24.85 24.91 -0.76 24.92 25.18 -2.18∗

Father:Months of schooling 140.15 143.26 -3.85∗∗∗ 140.38 146,86 -5.71∗∗∗

Completed HS or equvalent 0.19 0.18 2.58∗∗ 0.20 0.23 -3.29∗∗∗

Unemployed 0.08 0.07 1,67 0.07 0.06 2.28∗

Out of the labour force 0.06 0.04 4.51∗∗∗ 0.06 0.04 3.26∗∗

Note: Table shows selected mean characteristics of the full sample and compliers (i.e. those who are inducedto 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 im-

portance 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 (Sat-

Sun). For girls, the effect during the weekdays is not statistically different from zero, while

79

Figure

II.7:Estim

ationResults:

CrimeAtor

BeforeAge

byTypes

ofCrime

((a))Girls,mother

<12

yos

((b))

Girls,mother≥12

yos

((c))Girls,father

employed

((d))

Girls,father

not

empl.

((e))Boy

s,mother

<12

yos

((f))Boys,

mother≥12

yos

((g))Boy

s,father

employed

((h))

Boy

s,father

not

empl.

Note:

Figuresshow

theestimated

effects


on2S

LS

regression

son

theprobab

ilityof

crim

eat

orbeforeagiven

age

bymothersed

ucation(≥

12yearsof

education(40%)v.<12

years

ofed

ucation

(60%

))an

dfathersem

ploymentstatus(employed(86%

)v.not

employed(14%

)).Cut-off

dummy(Jan

uary=1)

usedasinstrument.

Con


distance

tocu

t-off

,cohortfixed

effects,an

dbackgrou

nd

characteristics(see

Table

A3).

Dashed

lines

indicate95

%confiden

ceintervals.

80

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 Ockert

(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

26We impute average age of peers for observations with fewer than 10 other children enrolled at the schoolin grade 8.

27Compare the results presented in Table IIA.6 to those in Table IIA.8.28Danish grades are not affected (not shown).

81

Table II.5: Effects of School Starting Age on Other Outcomes

Variable Girls BoysOLS 2SLS 2SLS OLS 2SLS 2SLS

GradesMath -0.028∗ 0.502∗∗∗ 0.510∗∗∗ -0.052∗∗∗ 0.356∗ 0.295∗∗∗

(0.011) (0.101) (0.093) (0.014) (0.145) (0.135)Effort -0.116∗∗∗ 0.036 0.065 -0.093∗∗∗ 0.201 0.195

(0.011) (0.090) (0.088) (0.015) (0.150) (0.146)N 27,909 27,909 27,909 27,974 27,974 27,974

Years of schooling, age 27 -0.448 -0.048 -0.045 -0.335 0.234 0.165(0.050) (0.136) (0.124) (0.052) (0.147) (0.135)

N 11,045 11,046 11,047 11,273 11,274 11,275

College enrollmentMed School -0.007∗∗∗ 0.026∗ 0.026∗ -0.006∗∗∗ 0.019 0.019

(0.001) (0.011) (0.011) (0.001) (0.011) (0.011)Law School -0.007∗∗∗ -0.013 -0.013 -0.003∗∗∗ -0.006 -0.006

(0.002) (0.013) (0.013) (0.001) (0.012) (0.012)N 30,209 30,209 30,209 31,405 31,405 31,405Distance to cut-off X X X XCovariates X X X X

Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions of alternativeeducation outcomes. Cut-off dummy (January=1) used as instrument. Conditioning set includesdistance 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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Table IIA.1: Means of Selected Outcome Variables by Month of Birth

Criminal charge Girls Boys(0/1) at age December January Difference N December January Difference N15 0.021 0.017 0.003∗∗ 48,546 0.042 0.036 0.007∗∗∗ 50,38316 0.016 0.015 0.001 48,546 0.058 0.051 0.007∗∗∗ 50,38317 0.015 0.013 0.002∗ 48,546 0.093 0.081 0.012∗∗∗ 50,38318 0.014 0.013 0.001 48,546 0.095 0.084 0.010∗∗∗ 50,38319 0.021 0.020 0.001 43,668 0.114 0.102 0.012∗∗∗ 45,36820 0.021 0.022 -0.001 39,037 0.117 0.108 0.009∗∗ 40,60621 0.021 0.019 0.002 34,559 0.112 0.103 0.008∗∗ 36,01222 0.022 0.020 0.001 30,209 0.105 0.097 0.008 31,40523 0.020 0.019 0.001 26,093 0.101 0.097 0.005 26,93724 0.020 0.018 0.003 22,125 0.093 0.092 0.002 22,78125 0.023 0.018 0.005∗ 18,240 0.085 0.082 0.003 18,72326 0.019 0.016 0.002 14,630 0.081 0.077 0.004 14,94927 0.019 0.020 -0.001 11,045 0.080 0.071 0.009 11,273

Criminal charge Girls Boys(0/1) at or before age December January Difference N December January Difference N15 0.021 0.017 0.003∗∗∗ 48,546 0.042 0.036 0.007∗∗∗ 50,38316 0.035 0.030 0.004∗∗ 48,546 0.086 0.076 0.010∗∗∗ 50,38317 0.047 0.041 0.006∗∗∗ 48,546 0.147 0.133 0.014∗∗∗ 50,38318 0.057 0.051 0.006∗∗∗ 48,546 0.196 0.181 0.015∗∗∗ 50,38319 0.073 0.065 0.008∗∗∗ 43,668 0.252 0.234 0.018∗∗∗ 45,36820 0.086 0.081 0.005 39,037 0.298 0.282 0.017∗∗∗ 40,60621 0.098 0.093 0.005 34,559 0.336 0.318 0.018∗∗∗ 36,01222 0.109 0.104 0.005 30,209 0.368 0.348 0.020∗∗∗ 31,40523 0.116 0.115 0.001 26,093 0.391 0.374 0.018∗∗∗ 26,93724 0.125 0.123 0.003 22,125 0.410 0.395 0.016∗∗ 22,78125 0.136 0.130 0.006 18,240 0.423 0.410 0.013 18,72326 0.140 0.136 0.004 14,630 0.433 0.424 0.009 14,94927 0.142 0.144 - 0.001 11,045 0.446 0.433 0.013 11,273

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 Fraction beingdelayed/retained

Kindergarten 0.1361st grade 0.0142nd grade 0.0033rd grade 0.0044th grade 0.0035th grade 0.0036th grade 0.0037th grade 0.0028th grade 0.0039th grade 0.005

Note: Table shows fraction of childrenwho are retained / red-shirted at eachgrade level.Calculation based of grade level datafrom 2007 and onwards.

89

Table IIA.3: Summary Statistics of the Sample

Variable Girls BoysDecember January T-value December January T-value

Immigrant 0.043 0.037 0.006∗∗ 0.042 0.034 0.008∗∗∗

0.001 0.001 0.001 0.001Parents married/cohabiting 0.788 0.784 0.004 0.789 0.792 -0.003

0.003 0.003 0.003 0.003Apgar score=9 0.181 0.184 -0.002 0.187 0.184 0.004

0.002 0.002 0.002 0.002Apgar score=8 0.071 0.067 0.004 0.066 0.070 -0.004

0.002 0.002 0.002 0.002Apgar score lower 0.084 0.085 -0.001 0.097 0.094 0.003

0.002 0.002 0.002 0.002Birth weight. grams 3341 3358 -16.59∗∗ 3466 3481 -15.02∗∗

3.987 3.813 4.152 3.909Gestational length, weeks 39.564 39.543 0.021 39.482 39.464 0.019

0.012 0.011 0.012 0.012Father:Months of schooling 137.276 137.502 -0.226 136.986 138.480 -1.494∗∗∗

0.230 0.235 0.229 0.226Completed HS or equvalent 0.292 0.287 0.005 0.290 0.302 -0.013∗∗

0.003 0.003 0.003 0.003Unemployed 0.130 0.125 0.005 0.128 0.122 0.006∗

0.002 0.002 0.002 0.002Out of the labour force 0.104 0.111 -0.006∗ 0.105 0.105 0.000

0.002 0.002 0.002 0.002Age at birth of first child 24.819 24.886 -0.068 24.851 24.990 -0.139∗∗∗

0.027 0.027 0.026 0.026Father:Months of schooling 139.736 140.507 -0.771 139.544 141.215 -1.671∗∗∗

0.281 0.277 0.277 0.273Completed HS or equvalent 0.191 0.190 0.002 0.195 0.204 -0.009∗

0.003 0.003 0.002 0.003Unemployed 0.078 0.077 0.001 0.076 0.073 0.004

0.002 0.002 0.002 0.002Out of the labour force 0.065 0.062 0.003 0.064 0.061 0.003

0.002 0.002 0.064 0.001Observations 24,279 24,267 25,157 25,226

Note: Table shows summary statistics of the sample by month of birth and gender. Std. errors shown belowsample 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 Girls BoysJanuary=1 0.245∗∗∗ 0.245∗∗∗ 0.244∗∗∗ 0.246∗∗∗ 0.172∗∗∗ 0.171∗∗∗ 0.171∗∗∗ 0.171∗∗∗

(0.008) (0.008) (0.008) (0.008) (0.007) (0.007) (0.007) (0.007)Days to cut-off, December -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗ -0.005∗∗∗

(0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)Days to cut-off, January 0.003∗∗∗ 0.003∗∗∗ 0.003∗∗∗ 0.003∗∗∗ 0.001∗∗∗ 0.001∗∗∗ 0.001∗∗∗ 0.001∗∗∗

(0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000) (0.000)Apgar score=9 0.005 0.005 0.005 -0.001 -0.001 -0.003

(0.005) (0.005) (0.005) (0.005) (0.005) (0.005)Apgar score=8 0.014 0.012 0.012 0.003 0.001 -0.002

(0.008) (0.008) (0.008) (0.007) (0.007) (0.007)Apgar score lower than 8 0.015 0.011 0.013 0.006 0.004 0.004

(0.008) (0.008) (0.008) (0.006) (0.006) (0.006)Immigrant -0.033∗∗ -0.041∗∗∗ -0.067∗∗∗ -0.097∗∗∗ -0.070∗∗∗ -0.097∗∗∗

(0.011) (0.012) (0.012) (0.009) (0.011) (0.011)Birth weigth -0.000∗∗∗ -0.000∗∗∗ -0.000∗∗∗ -0.000∗∗∗ -0.000∗∗∗ -0.000∗∗∗

(0.000) (0.000) (0.000) (0.000) (0.000) (0.000)Gestation length -0.065∗∗∗ -0.070∗∗∗ -0.068∗∗∗ -0.035∗ -0.034∗ -0.031

(0.019) (0.019) (0.019) (0.017) (0.017) (0.017)Gestation length squared 0.001∗∗ 0.001∗∗ 0.001∗∗ 0.000 0.000 0.000

(0.000) (0.000) (0.000) (0.000) (0.000) (0.000)Mother’s months of schooling 0.001∗∗∗ 0.001∗∗∗ 0.001∗∗∗ 0.001∗∗∗

(0.000) (0.000) (0.000) (0.000)Mother’s months of schooling sq. -0.000∗∗∗ -0.000∗∗∗ -0.000∗∗∗ -0.000∗∗∗

(0.000) (0.000) (0.000) (0.000)Father’s months of schooling 0.001∗∗ 0.000∗ 0.001∗∗∗ 0.000∗∗

(0.000) (0.000) (0.000) (0.000)Father’s months of schooling sq. -0.000∗∗∗ -0.000∗∗ -0.000∗∗ -0.000∗

(0.000) (0.000) (0.000) (0.000)Mother has compl. high school -0.026∗∗∗ -0.022∗∗∗ -0.005 -0.002

(0.006) (0.006) (0.005) (0.005)Father has compl. high school -0.065∗∗∗ -0.060∗∗∗ -0.051∗∗∗ -0.048∗∗∗

(0.007) (0.007) (0.006) (0.006)Mother unemployed 0.020∗∗ 0.017∗∗ 0.007 0.005

(0.006) (0.006) (0.006) (0.006)Mother out of labour force 0.002 -0.003 -0.025∗∗∗ -0.029∗∗∗

(0.007) (0.007) (0.006) (0.006)Father unemployed 0.017∗ 0.020∗ 0.001 0.004

(0.008) (0.008) (0.007) (0.007)Father out of labour force 0.009 -0.002 0.009 -0.000

(0.009) (0.009) (0.008) (0.008)Mother’s age at first child 0.002∗∗∗ 0.000 0.004∗∗∗ 0.002∗∗∗

(0.001) (0.001) (0.001) (0.000)Parents are married 0.001 0.004 0.002 0.005

(0.005) (0.005) (0.005) (0.005)Cut-off 1981-1982 -0.143∗∗∗ -0.147∗∗∗

(0.010) (0.009)Cut-off 1982-1983 -0.132∗∗∗ -0.136∗∗∗

(0.010) (0.009)Cut-off 1983-1984 -0.135∗∗∗ -0.117∗∗∗

(0.010) (0.009)Cut-off 1984-1985 -0.145∗∗∗ -0.109∗∗∗

(0.010) (0.009)Cut-off 1985-1986 -0.117∗∗∗ -0.095∗∗∗

(0.010) (0.009)Cut-off 1986-1987 -0.088∗∗∗ -0.070∗∗∗

(0.010) (0.009)Cut-off 1987-1988 -0.045∗∗∗ -0.042∗∗∗

(0.010) (0.009)Cut-off 1988-1989 -0.029∗∗ -0.010

(0.010) (0.008)Cut-off 1989-1990 -0.032∗∗∗ -0.012

(0.010) (0.008)Cut-off 1990-1981 0.006 0.016∗

(0.009) (0.008)Cut-off 1992-1993 0.006 0.002

(0.009) (0.008)Constant 0.714∗∗∗ 2.294∗∗∗ 2.282∗∗∗ 2.372∗∗∗ 0.872∗∗∗ 1.707∗∗∗ 1.540∗∗∗ 1.590∗∗∗

(0.006) (0.369) (0.368) (0.365) (0.005) (0.321) (0.321) (0.318)N 48,546 48,546 48,546 48,546 50,383 50,383 50,383 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-offdummies (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

Tab

leIIA.5:First

Stage

Resultat

DifferentGradeLevels

Girls

Boys

Preschool

2ndgrad

e4thgrad

e8thgrad

ePreschool

2ndgrad

e4thgrad

e8thgrad

eBorn

Born

Born

Born

Decem

ber

2000

Decem

ber

1996

Decem

ber

2000

Decem

ber

1996

Jan

uary2001

Jan

uary1997

Jan

uary2001

Jan

uary1997

Jan

uary=1

0.249∗

∗∗

0.251∗

∗∗

0.231∗

∗∗

0.215∗

∗∗0.129∗

∗∗

0.134∗

∗∗

0.112∗

∗∗

0.109∗

∗∗

(0.024)

(0.024)

(0.023)

(0.023)

(0.017)

(0.018)

(0.018)

(0.018)

Daysto

cut-off

,Decem

ber

-0.005

∗∗∗

-0.005

∗∗∗

-0.005

∗∗∗

-0.005

∗∗∗

-0.004

∗∗∗

-0.004

∗∗∗

-0.004

∗∗∗

-0.003

∗∗∗

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

Daysto

cut-off

,Jan

uary

0.003∗

∗∗

0.003∗

∗∗

0.003∗

∗∗

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)

Con

stan

t0.809∗

∗∗

0.792∗

∗∗

0.795∗

∗∗

0.797∗

∗∗

0.941∗

∗∗

0.941∗

∗∗

0.923∗

∗∗

0.928∗

∗∗

(0.016)

(0.017)

(0.017)

(0.017)

(0.013)

(0.013)

(0.013)

(0.013)

N4,977

4,977

5,264

5,264

5,328

5,328

5,433

5,433

F-valueforJan

uarydummy

280.69

287.42

275.32

262.96

162.94

173.46

146.03

132.19

Note:

Tab

leshow

sresultsfrom

linearregression

sof

indicatorsforstartingschool

atag

e7.6instead

of6.6whileconditioningon

cut-off

dummies

(Jan

uary=1),distance

tocu

t-off,cohortfixed

effects

andbackgrou

ndcharacteristics(see

Tab

leA3).School

startingag

eis

measuredat

differentgrad

elevels

intheperiod20

07-2013

.p<0.05

:∗,p<0.01

:∗∗,p<0.00

1:∗∗∗.

92

Table IIA.6: Detailed Estimation Results: Crime At or Before Age

Criminal charge Girls Boys(0/1) at or before age OLS 2SLS 2SLS N OLS 2SLS 2SLS N15 -0.005∗∗∗ -0.009∗ -0.008∗ 48,546 -0.005∗ -0.025∗∗∗ -0.019∗∗ 50,383

(0.001) (0.003) (0.003) (0.002) (0.007) (0.006)16 -0.003 -0.011∗ -0.010∗ 48,546 -0.009∗∗∗ -0.035∗∗∗ -0.025∗∗ 50,383

(0.002) (0.004) (0.004) (0.003) (0.009) (0.009)17 -0.003 -0.016∗∗ -0.015∗∗ 48,546 -0.006 -0.051∗∗∗ -0.037∗∗ 50,383

(0.002) (0.005) (0.005) (0.004) (0.012) (0.012)18 -0.003 -0.017∗∗ -0.016∗∗ 48,546 -0.002 -0.054∗∗∗ -0.038∗∗ 50,383

(0.002) (0.006) (0.006) (0.004) (0.013) (0.013)19 -0.003 -0.020∗∗ -0.019∗∗ 43,668 0.001 -0.066∗∗∗ -0.045∗∗ 45,368

(0.002) (0.007) (0.007) (0.005) (0.015) (0.015)20 -0.001 -0.012 -0.011 39,037 0.000 -0.058∗∗∗ -0.036∗ 40,606

(0.003) (0.008) (0.007) (0.005) (0.016) (0.016)21 -0.004 -0.012 -0.011 34,559 0.004 -0.061∗∗∗ -0.039∗ 36,012

(0.003) (0.008) (0.008) (0.005) (0.017) (0.017)22 -0.005 -0.012 -0.011 30,209 0.004 -0.068∗∗∗ -0.043∗ 31,405

(0.004) (0.009) (0.009) (0.006) (0.019) (0.018)23 -0.002 -0.002 -0.000 26,093 0.008 -0.057∗∗ -0.035 26,937

(0.004) (0.010) (0.010) (0.006) (0.020) (0.019)24 -0.001 -0.006 -0.005 22,125 0.005 -0.049∗ -0.030 22,781

(0.004) (0.012) (0.011) (0.007) (0.021) (0.020)25 -0.002 -0.015 -0.013 18,240 0.003 -0.038 -0.018 18,723

(0.005) (0.013) (0.013) (0.008) (0.023) (0.022)26 -0.004 -0.011 -0.010 14,630 0.005 -0.026 -0.006 14,949

(0.006) (0.015) (0.014) (0.009) (0.025) (0.024)27 0.001 0.004 0.004 11,045 0.004 -0.036 -0.019 11,273

(0.007) (0.017) (0.017) (0.010) (0.028) (0.027)Distance to cut-off X X X XYearly cut-off FE X X X X X XCovariates X X X 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. Conditioning set includes distance to cut-off, cohort fixed effects, andbackground 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 Girls Boys(0/1) at age OLS 2SLS 2SLS N OLS 2SLS 2SLS N15 -0.005∗∗∗ -0.009∗ -0.008∗ 48,546 -0.005∗ -0.025∗∗∗ -0.019∗∗ 50,383

(0.001) (0.003) (0.003) (0.002) (0.007) (0.006)16 0.002 -0.003 -0.003 48,546 -0.007∗∗ -0.026∗∗∗ -0.019∗ 50,383

(0.001) (0.003) (0.003) (0.002) (0.008) (0.008)17 0.001 -0.006∗ -0.006∗ 48,546 0.001 -0.044∗∗∗ -0.036∗∗∗ 50,383

(0.001) (0.003) (0.003) (0.003) (0.010) (0.009)18 0.001 -0.002 -0.002 48,546 0.004 -0.039∗∗∗ -0.030∗∗ 50,383

(0.001) (0.003) (0.003) (0.003) (0.010) (0.010)19 0.001 -0.002 -0.002 43,668 0.002 -0.045∗∗∗ -0.033∗∗ 45,368

(0.001) (0.004) (0.004) (0.003) (0.011) (0.011)20 0.002 0.003 0.003 39,037 0.002 -0.031∗∗ -0.021 40,606

(0.002) (0.004) (0.004) (0.004) (0.011) (0.011)21 -0.001 -0.004 -0.004 34,559 0.011∗∗ -0.029∗ -0.019 36,012

(0.002) (0.004) (0.004) (0.004) (0.012) (0.011)22 0.001 -0.003 -0.002 30,209 0.003 -0.028∗ -0.018 31,405

(0.002) (0.004) (0.004) (0.004) (0.012) (0.012)23 0.002 -0.002 -0.002 26,093 0.006 -0.015 -0.005 26,937

(0.002) (0.005) (0.004) (0.004) (0.012) (0.012)24 -0.001 -0.007 -0.007 22,125 0.009∗ -0.005 0.003 22,781

(0.002) (0.005) (0.005) (0.004) (0.012) (0.012)25 -0.000 -0.012∗ -0.011∗ 18,240 0.005 -0.009 -0.001 18,723

(0.002) (0.005) (0.005) (0.004) (0.013) (0.013)26 -0.000 -0.006 -0.006 14,630 -0.002 -0.011 -0.003 14,494

(0.002) (0.006) (0.006) (0.005) (0.014) (0.013)27 -0.000 0.002 0.002 11,045 0.002 -0.026 -0.020 11,273

(0.003) (0.007) (0.007) (0.005) (0.015) (0.015)Distance to cut-off X X X XYearly cut-off FE X X X X X XCovariates X X X X

Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions of crime at or before agiven age. Cut-off dummy (January=1) used as instrument. Conditioning set includes distance to cut-off, cohortfixed 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 BeforeAge

Criminal charge Girls Boys(0/1) at or before age Old-for-grade Peer age N Old-for-grade Peer age N15 -0.008∗ 0.014 48,546 -0.019∗ 0.002 50,383

(0.003 (0.028) (0.006) (0.044)16 -0.010∗ -0.033 48,546 -0.025∗ -0.017 50,383

(0.004) (0.036) (0.009) (0.062)17 -0.015∗∗ -0.011 48,546 -0.037∗∗ -0.058 50,383

(0.005) (0.042) (0.012) (0.078)18 -0.016∗∗ -0.006 48,546 -0.038∗∗ 0.049 50,383

(0.006) (0.046) (0.013) (0.088)19 -0.018∗∗ -0.060 43,668 -0.046∗∗ 0.116 45,368

(0.007) (0.054) (0.015) (0.101)20 -0.010 -0.063 39,037 -0.037∗ 0.065 40,606

(0.008) (0.061) (0.016) (0.112)21 -0.009 -0.113 34,559 -0.041∗ 0.093 36,012

(0.00)8 (0.068) (0.017) (0.119)22 -0.010 -0.116 30,209 -0.044∗ 0.027 31,405

(0.009) (0.076) (0.018) (0.129)23 0.001 -0.075 26,093 -0.036 0.054 26,937

(0.010) (0.083) (0.019) (0.136)24 -0.002 -0.124 22,125 -0.030 0.022 22,781

(0.012) (0.094) (0.021) (0.146)25 -0.008 -0.230 18,240 -0.017 -0.058 18,723

(0.013) (0.102) (0.022) (0.159)26 -0.006 -0.152∗ 14,630 0.005 -0.321 14,949

(0.015) (0.113) (0.025) (0.177)27 0.005 -0.030 11,045 -0.009 -0.321 11,273

(0.018) (0.130) (0.028) (0.201)Distance to cut-off X XYearly cut-off FE X XCovariates X X X X

Note: Table shows the estimated effects of being old-for-grade based on 2SLS regressions on crime at or beforea given age. Cut-off dummy (January=1) used as instrument for own school starting decision, predicted schoolstarting age of peers if compliant with rules used as instrument for average peer age. In addition to average peerage, conditioning set includes distance to cut-off, cohort fixed effects, and background characteristics (see TableA3). p<0.05: ∗, p<0.01: ∗∗, p<0.001: ∗∗∗

95

Figure IIA.1: Age 4 Social and Emotional Difficulties Among Punctual and Late SchoolStarters

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

Figure

IIA.2:CrimeAtor

BeforeAge

((a))Girls,ag

e19

((b))

Girls,ag

e27

((c))Boy

s,ag

e19

((d))

Boy

s,ag

e27

Note:

Figuresshow

Crime-Age

Profiles:Thefraction

ofindividualswhohavebeenchargedwithacrim

eat

(left)

andat

orbefore(right)

agivenag

e.

Population

ofchildrenborn19

81-199

3

97

Figure

IIA.3:CrimeAtor

BeforeAge

((a))Girls,ag

e19

((b))

Girls,ag

e27

((c))Boy

s,age

19((d))

Boy

s,ag

e27

Note:

Figuresshow

scatterplots

ofcrim

eat

orbeforeagivenag

e(19an

d27

)bydateof

birth.Thesolidlineisalocalpolynom

ialsm

oothed

linean

d

thecorrespon

dingdashed

lines

indicate

95%

confiden

ceintervals.

98

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

Figure

IIA.6:Estim

ationResults:

CrimeAtor

BeforeAge

byWeekday/W

eekend

((a))Girls,weekday

((b))

Boys,

weekday

((c))Girls,weekend

((d))

Boy

s,weekend

Note:

Figuresshow

theestimated

effects


on2S

LSregression

son

theprobab

ilityof

crim

ebyweekdays(M

on-Fri)an

d

weeken

ds(Sat-Sun).

Cut-offdummy(Jan

uary=1)usedas

instrument.

Con


distance

tocu

t-off

,cohortfixed

effects,an

d

backgroundcharacteristics(see

Table

A3).

Dashed

lines

indicate95

%confiden

ceintervals.

101

Figure IIA.7: Estimation Results: Crime At or Before Age by Continuous School StartingAge

((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

Figure

IIA.8:Estim

ationResults:

CrimeAtor

BeforeAge,Extended

Ban

dwidth

((a))Girls,±

30days

((b))

Girls,±

60days

((c))Girls,±

90day

s

((d))

Boy

s,±

30days

((e))Boy

s,±

60days

((f))Boys,±

90day

s

Note:

Figuresshow

theestimated

effects


on2S

LSregression

son

theprobab

ilityof

crim

eat

orbeforeagivenag

eusing

varyingsample

ban

dwidths.

Cut-off

dummy(Jan

uary=1)

usedas

instrument.

Con


distance

tocu

t-off

,cohortfixed

effects,an

d

backgrou

ndcharacteristics

(see

Tab

leA3).Dashed

lines

indicate95

%confiden

ceintervals.

103

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. Becausethe covariance between the instrument (here defined as January=1) and the treatment (old-for-grade) ispositive σOfG,Z , as being born in January predicts a higher probability of being old-for-grade, the boundsare given as Bounds B∗ =

[βIVZ ,

σOfG(σOfG,Z−σZσOfG)σOfGσZ,y−σOfGσOfG,y

] if σOfG,Z > 0

[σOfG(σOfG,Z−σZσOfG)σOfGσZ,y−σOfGσOfG,y

, βIVZ ] if σOfG,Z < 0

Where Z denotes the instrument, y crime at or before a given age ,and OfG 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 substan-

tially 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 unob-

serveable 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 popu-

lation, 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 psy-

chiatric 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 psychi-

atric 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 indi-

viduals 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 admis-

sion 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 pa-

tients’ 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 strength-

ening 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.

1A 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

2We do not explicitly address the degree to which various treatment forms reduce core symptoms ofpsychiatric illnesses or improve the quality of life for patients, but only the derived effects on realisedoutcomes.

3Since the 1960s a comprehensive change has taken place in the psychiatric treatment systems in themajority of developed countries.The change is sometimes labelled the third revolution of psychiatry (Castelet 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 treatingthe 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 contactwith 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.

4See 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 re-

admission 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.

5See Frank & McGuire (2000) for a review of the literature on mental health economics.6One 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 betweentwo types of treatment instead of the full sample of patients seeking treatment.

7For an example see Creed et al. (1990) who find no differences between inpatient and day treatmentsusing a U.K. RCT with a sample size of 89 individuals.

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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 psychi-

atric 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 psychi-

atrists, the GP has three options: (1) refer the patient to a psychiatric practitioner (the

8GPs 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 prescribemost 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,

9In 2000, one third of all psychiatric patients received treatment from a specialist, with the last two-thirds 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).

10Both 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 localsocial services together with psychiatrists and funded and governed by the individual municipalities. Duringthe period in question, Denmark consisted of 279 municipalities and 13 counties. Hoff et al. (2012) providean overview of the Danish system compared to the English and the Dutch. With the exception of the fundingschemes, these two strands of treatment possibilities resemble those of many OECD countries, including theU.S. and the U.K.

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Table III.1: Average Treatment Length

Not admitted AdmittedTotal length of treatment as inpatient - 30.203

- (76.790)Outpatient treatment at psych. hospitals 0.502 -

(0.500) -Total length of treatment as outpatient 68.398 -

(152.048) -Observations 16928 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.

11Danish psychiatric facilities have been the focus of gradual budget cuts and capacity reductions duringthe past two decades, especially with respect to inpatient treatments (Bengtsson, 2011). However, theperiod between 1998 and 2001 is a relatively stable period without any major reforms and reductions onadult psychiatric treatment possibilities. Different conditions apply for child and geriatric patients relativeto the average adult population once in contact with a psychiatric care facility.

12We also discard individuals who are diagnosed with mental retardation, dementia, or disorders of earlypsychological development (because these patient groups suffer from chronic disorders and have little or nolabour 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 excludeindividuals who contact the few countryside treatment facilities that only treat 10-50 individuals per year.

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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 unem-

ployment 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 emo-

tional 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

13The random sample has been weighted by the age-distribution of our main sample for comparison.

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Table III.2: Descriptive Statistics for Sample

Full sample Not admitted Admitted Representative sampleMale 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 716411Note: 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 statisticsof a randomly selected sample of individuals aged between 18-45 in 1999-2001.

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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 con-

tacts, criminal convictions, self-harming behaviour, and labour market outcomes. We meas-

ure 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 psy-

chiatric 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 ad-

mission 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) hospitalisa-

tions 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:

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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

Admission Contact Crimes Overdose LesionNot adm. Adm. Not adm. Adm. Not adm. Adm. Not adm. Adm. Not adm. Adm.

3 months 0.017 0.030 0.088 0.220 0.226 0.497 0.010 0.019 0.001 0.002(0.145) (0.186) (0.283) (0.414) (0.418) (0.500) (0.101) (0.135) (0.034) (0.042)

6 months 0.035 0.059 0.123 0.284 0.281 0.572 0.016 0.030 0.002 0.003(0.219) (0.285) (0.329) (0.451) (0.450) (0.495) (0.127) (0.172) (0.047) (0.055)

9 months 0.055 0.086 0.143 0.317 0.313 0.602 0.020 0.041 0.003 0.005(0.291) (0.373) (0.350) (0.465) (0.464) (0.490) (0.140) (0.199) (0.054) (0.069)

12 months 0.072 0.110 0.153 0.346 0.333 0.623 0.024 0.049 0.004 0.006(0.355) (0.447) (0.360) (0.476) (0.471) (0.485) (0.154) (0.215) (0.059) (0.079)

15 months 0.088 0.135 0.162 0.366 0.351 0.638 0.028 0.054 0.005 0.007(0.400) (0.511) (0.368) (0.482) (0.477) (0.481) (0.165) (0.227) (0.067) (0.083)

18 months 0.103 0.158 0.169 0.382 0.365 0.649 0.031 0.060 0.005 0.008(0.450) (0.564) (0.375) (0.486) (0.482) (0.477) (0.174) (0.237) (0.073) (0.088)

21 months 0.117 0.180 0.176 0.398 0.381 0.660 0.035 0.064 0.006 0.009(0.496) (0.615) (0.380) (0.489) (0.486) (0.474) (0.184) (0.245) (0.077) (0.094)

24 months 0.132 0.203 0.181 0.408 0.393 0.668 0.038 0.067 0.007 0.010(0.541) (0.665) (0.385) (0.492) (0.488) (0.471) (0.190) (0.251) (0.082) (0.097)

27 months 0.147 0.228 0.187 0.419 0.403 0.675 0.040 0.072 0.007 0.011(0.592) (0.733) (0.390) (0.493) (0.490) (0.468) (0.196) (0.258) (0.085) (0.104)

30 months 0.160 0.251 0.192 0.427 0.413 0.683 0.043 0.077 0.008 0.012(0.634) (0.800) (0.394) (0.495) (0.492) (0.466) (0.202) (0.267) (0.089) (0.107)

33 months 0.172 0.276 0.196 0.433 0.421 0.688 0.045 0.082 0.009 0.013(0.671) (0.865) (0.397) (0.496) (0.494) (0.464) (0.208) (0.274) (0.093) (0.112)

36 months 0.186 0.301 0.200 0.440 0.429 0.693 0.048 0.087 0.009 0.013(0.717) (0.925) (0.400) (0.496) (0.495) (0.461) (0.213) (0.281) (0.096) (0.114)

Observations 16928 7349 16928 7349 16928 7349 16928 7349 16928 7349

Note: Table shows means and std. dev. of outcome variables for the sample dependent on treatment status. Time 0 is month of initialcontact. Crimes are aggregating count variables. Admission, Contact, Overdose and Lesion are absorbing state dummies. Standarddeviation in parentheses.

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Table III.4: Summary of Labor Market Outcomes

Empl. Unempl. Out of labor forceNot adm. Adm. Not adm. Adm. Not adm. Adm.

12 months 0.550 0.455 0.169 0.202 0.282 0.343(0.498) (0.498) (0.375) (0.402) (0.450) (0.475)

24 months 0.537 0.444 0.166 0.190 0.297 0.366(0.499) (0.497) (0.372) (0.393) (0.457) (0.482)

36 months 0.532 0.431 0.160 0.177 0.308 0.391(0.499) (0.495) (0.367) (0.382) (0.461) (0.488)

Observations 16928 7349 16928 7349 16928 7349Note: 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

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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:

Zlag(1week)i =

∑

−1d=−7 Contactshd

max(∑

−1d=−7 Contactshd,

∑

−2d=−8 Contactshd, ...,

∑

−359d=−365 Contactshd)

Zlag(2weeks)i =

∑

−8d=−14 Contactshd

max(∑

−1d=−7 Contactshd,

∑

−2d=−8 Contactshd, ...,

∑

−359d=−365 Contactshd)

(1)

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

14Importantly, we only count an individual once within a given week in order to avoid that e.g. highadmission thresholds affects the number of contacts as patients keep reappearing.

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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.

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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 endo-

geneity. 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 (2)

15If rejected patients turn up at other hospitals with more vacant beds and are admitted there, this couldresult in a misspecification of the treatment variable and result in attenuation bias. But as only 1.7% ofthe no-admission group contacts another hospital within the first week of their initial rejection, we do notconsider this to be a problem.

16Major cities also constitute the areas most likely to allow for selection between hospitals according tooccupancy rate.

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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]

= 1[µ1(X)− µ0(X) > U0 − U1 + UC ]

(4)

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 out-

comes 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 = π′

1X + π′

2Z − V (6)

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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 instru-

ment. 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:

βLATE2 = E[β2|π

′

1X + π′

2Z < V < π′

1X + π′

2Z∗], for 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, βLATE2 may incorporate

heterogeneous treatment effects across individuals with different levels of unobservable char-

acteristics, 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

17We estimate the first stage equation using the instrument linearly. The results are robust to usingalternative specifications that allow for non-linear relationships between the probability of admission andprevious weeks’ contact intensity. These results are presented in Figure IIIA.3 in the Appendix.

18Alternatives 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 inpatientadmission. Our treatment effects will identify the effect of inpatient admission upon initial contact relativeto an average of all of these individual alternatives. Identifying each individual alternative would requireat least one instrument per margin of treatment. Authors refer to Heckman & Urzua (2010) for a generaldiscussion of this issue and Kirkebøen et al. (2014) for an application (investigating field of study) whereall individual treatment margins are identified.

123

Effects (MTE) of admission (Bjorklund & Moffitt, 1987; Heckman & Vytlacil, 2005):

βMTE2 = E[β2|UD = u∗

D, X = X∗] (8)

where UD = FUD[V ] (see eq. (4)). βMTE

2 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.

19We estimate the first stage equation of the MTE by a probit. We report estimates of the parametricversion of the MTE, see Heckman et al. (2006).

20The MTE is a generalisation of treatment effects such as the LATE:

βLATE2 =

1

UD − UD∗

∫ UD∗

UD

βMTE2 dU

where UD is the random/latent variable for those who are affected by Z.

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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 socio-

economic 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

Inpatient adm. Inpatient adm. Inpatient adm.Average occupancy rate,deviation from hospital meanPrevious 1-7 days -0.154∗∗∗ -0.143∗∗∗ -0.142∗∗∗

(0.030) (0.030) (0.027)

Previous 8-14 days -0.103∗∗∗ -0.092∗∗ -0.089∗∗∗

(0.029) (0.028) (0.026)F-value 99.372 82.671 87.776Observations 24277 24277 24277SES and demograpic controls X XDiagnosis controls X

+p < .10;∗p < .05;∗∗p < .01; ∗∗∗p < .001Note: Table shows OLS regression results of inpatient admission (0/1) on the two instrumentalvariables; hospital specific contact intensity the two week prior to the individual’s initial con-tact. 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 priorpsych. 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 probab-

ility 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

21The variance of estimates is large. This could indicate the use of a weak instrument. However, the firststage 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 over-

representation 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.

22Note, however, that the 2SLS estimates for admittance and contacts are significantly different from eachother at the start of the period only (6 months).

127

Figure III.2: Effect on Probability of Subsequent Inpatient Admission by Months Since 1stContact

((a)) OLS estimates

((b)) 2SLS estimates

Note: Figure shows OLS and 2SLS regression results of inpatient admission (0/1) on subsequentre-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 ofinitial contact.SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothersyears 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 byMonths Since 1st Contact

((a)) OLS estimates


Note: Figure shows OLS and 2SLS regression results of inpatient admission (0/1) on subsequent contact topsych. 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 ofinitial contact.SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothersyears 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


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, mothersyears 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 ad-

mitted 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

23This reduction is not driven by incapacitation. The estimates do not differ qualitatively when we centeroutcomes around day of discharge.

131

Figure III.5: Effect on Subsequent Probability of Being Hospitalized for Self-harm by MonthsSince 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 everexperiencing 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, mothersyears 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 2SLS 2SLS 2SLSEmploymentFirst year since contact -0.054∗∗∗ -0.053 -0.112 -0.096

(0.007) (0.098) (0.097) (0.095)Second year since contact -0.049∗∗∗ -0.053 -0.143 -0.126

(0.007) (0.088) (0.088) (0.085)Third year since contact -0.053∗∗∗ -0.168∗ -0.253∗∗ -0.240∗∗

(0.007) (0.083) (0.085) (0.083)UnemploymentFirst year since contact 0.016∗∗ -0.069 -0.045 -0.053

(0.006) (0.069) (0.073) (0.072)Second year since contact 0.013∗ -0.020 0.009 0.003

(0.006) (0.066) (0.068) (0.068)Third year since contact 0.009+ 0.017 0.059 0.054

(0.005) (0.056) (0.060) (0.060)Out of Labor ForceFirst year since contact 0.038∗∗∗ 0.122 0.158∗ 0.149+

(0.007) (0.075) (0.080) (0.079)Second year since contact 0.036∗∗∗ 0.073 0.134 0.124

(0.007) (0.080) (0.086) (0.085)Third year since contact 0.044∗∗∗ 0.151∗ 0.194∗ 0.186∗

(0.007) (0.072) (0.076) (0.076)N 24277 24277 24277 24277SES and demograpic controls X X XDiagnosis controls X X

+p<.10;∗p<.05;∗∗p<.01;∗∗∗p<.001Note: Table shows 2SLS regression results of inpatient admission (0/1) on subsequent em-ployment (0/1), unemployment (0/1), and being out of the labor force (0/1). Standard errorsclustered 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 priorpsych. 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 ad-

mission.24 Psychiatric hospital records are a strong indicator for whether social services

provide individuals with disability pension, early retirement, or other forms of social assist-

ance 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

24Also, the changes from OLS to 2SLS appear counterintuitive if one has the likely selection bias of anaverage population in mind. Yet, as we have shown, our sample is not drawn from the average populationand very different selection mechanisms may play a role here. For example, stronger patients may be betterat manipulating institutions (see Moustsen et al. (2015) for a similar example from cancer-treatment).

25We also examine whether there exist heterogeneous effects across types of diagnoses, but find no signi-ficant or substantial differences. Results available on request.

134

Figure III.6: 2SLS Estimates of Effects of Inpatient Admission on Likelihood of SubsequentAdmission, 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 indicate95% confidence intervals and the dotted line indicate 90% confidence intervals. Time 0 is month of initialcontact. Standard errors clustered by hospital and month in parentheses. SES and demographic controlsinclude: Age at adm., mother’s age at birth, mothers years of schooling, father’ age at birth, father’s yearsof 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 ini-

tial 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 psychiat-

ric 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

Male FemaleEmploymentFirst year since contact 0.022 -0.231

(0.113) (0.141)Second year since contact -0.006 -0.256+

(0.114) (0.136)Third year since contact -0.044 -0.470∗∗∗

(0.112) (0.136)UnemploymentFirst year since contact -0.017 -0.093

(0.095) (0.107)Second year since contact -0.040 0.045

(0.103) (0.0900)Third year since contact 0.034 0.080

(0.083) (0.090)Out of Labor ForceFirst year since contact -0.004 0.324∗

(0.102) (0.130)Second year since contact 0.045 0.211

(0.117) (0.130)Third year since contact 0.010 0.390∗∗

(0.105) (0.132)

Observations 11246 13031SES and demographic controls X XDiagnosis controls X X

+p < .10;∗p < .05;∗∗p < .01; ∗∗∗p < .001Note: Table shows 2SLS regression results of inpatient admission(0/1) on subsequent employment (0/1), unemployment (0/1), andbeing 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’sage 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 CPHarea (dummy), other metropolitan area (dummy), year dummies.Diagnosis controls include: Dummies for each F. diagnosis cat-egory from ICD-10.

137

5.3 Marginal Treatment Effects

In the previous section we documented heterogeneous effects across observable characterist-

ics 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 treat-

ment 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 MTE = δ∆i/δp(Z,X) |UD=U∗

Dacross UD may be a composite of two differ-

ent 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, hospit-

alisations 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),

26We abstain from presenting results from MTEs for spousal labour market outcomes as estimates areinconclusive due to large variance. The results can be obtained from the authors.

27Or as an alternative formulation in the Roy-model framework, UD = U0 − U1 assuming no costs ofadmission (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 SubsequentAdmission, Contacts, and Number of Crimes

((a)) Admission

� � � � � � � ��

� � � � � � � � � �! �" # $ � % & � # $ � �! � % ' � ( �� ( �� ( �� ( �� ( �●

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((b)) Contact

) * + , -. � ��

/ � � % # �! �" # $ � % & � # $ � �! � % ' 0 � ( �� ( �� ( �� ( �� ( �� ( �●

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((c)) Crimes

) * + , -. � ��

1 2 � 3 4 & � 5 # & � � 4 � 0 � ( � �0 � ( � 60 � ( � �0 � ( � 60 � ( � �0 � ( � 6� ( � �●

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Note: Figures show estimated Marginal Treatment Effects of inpatient admission (0/1) on subsequentre-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 ownmunicipality (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 Probabilityof Being Hospitalized for Overdoses or Lesions During the Subseq. Three Years

((a)) Overdose

) * + , -. � ��

� � � � � � � � � � $ � �! � % ' 7 � $ � 8 4 & � � � 4 0 � ( � 60 � ( � �0 � ( � 6� ( � �� ( � 6●

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Note: Figures show estimated Marginal Treatment Effects of inpatient admission (0/1) on the risk of everbeing hospitalized the next three years for self-harm due to overdose (0/1), or lesion (0/1). Time 0 ismonth 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 ownmunicipality (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 Out-comes

((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 em-ployment (0/1), unemployment (0/1), and being out of the labor force (0/1). Time 0 is month of initialcontact. Covariates include: Gender (dummy), age at adm., mother’s age at birth, mothers years of school-ing, father’ age at birth, father’s years of schooling, mother has prior psych. history (dummy), admitted inown 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

Employment Unemployment Out of labor forceOLS 2SLS OLS 2SLS OLS 2SLS

First year since contact 0.030∗ 0.246+ -0.004 -0.195+ -0.026∗ -0.052(0.013) (0.146) (0.009) (0.106) (0.012) (0.113)

Second year since contact 0.008 0.221 -0.006 -0.161+ -0.002 -0.059(0.013) (0.145) (0.009) (0.092) (0.011) (0.119)

Third year since contact 0.004 0.266+ 0.009 -0.239∗ -0.013 -0.028(0.013) (0.156) (0.009) (0.107) (0.011) (0.119)

Observations 5763 5763 5763 5763 5763 5763

+p < .10;∗p < .05;∗∗p < .01; ∗ ∗ ∗p < .001Note: Table shows 2SLS regression results of inpatient admission (0/1) on his/herspouse’s subsequent employment (0/1), unemployment (0/1), and being out of thelabor force (0/1). Standard errors clustered by hospital and month in parentheses.SES and demographic controls include: Gender (dummy), age at adm., mother’s ageat 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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Table IIIA.1: Regression of GP and Specialists Visits on the Instruments

Model 1 Model 2 Model 3GP visits, year of admissionIV, day 1-7 -0.558 -0.507 -0.495

(0.681) (0.653) (0.652)

IV, day 8-14 -0.389 0.223 0.205(0.704) (0.672) (0.673)

GP visits, year prior to admissionIV, day 1-7 0.220 0.137 0.152

(0.593) (0.577) (0.580)

IV, day 8-14 -0.582 -0.146 -0.153(0.617) (0.600) (0.600)

Specialists visits, year of admissionIV, day 1-7 0.239 0.132 0.127

(0.214) (0.212) (0.213)

IV, day 8-14 0.333 0.259 0.259(0.219) (0.217) (0.218)

Specialists visits, year prior to admissionIV, day 1-7 0.122 0.033 0.030

(0.189) (0.188) (0.187)

IV, day 8-14 0.008 -0.058 -0.054(0.207) (0.204) (0.204)

SES controls X XDiagnosis controls XObservations 24,277 24,277 24,277

Note: Table shows OLS regression results of the two intrumental variables (hospitalspecific contact intensity the two week prior to the individual’s initial contact) onnumber of visits to general practioners and specialists the year of and the year priorto initial contact. Standard errors clustered by hospital and month in parentheses.SES and demographic controls include: Gender (dummy), age at adm., mother’s ageat 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

IV day 1-7 IV day 8-14Male -0.006∗ -0.003

(0.002) (0.002)Age at admission -0.000 -0.000

(0.000) (0.000)Mother’s age at birth 0.000 -0.000

(0.000) (0.000)Mother’s months of schooling 0.000∗ 0.000∗

(0.000) (0.000)Year 1999 -0.023 -0.026+

(0.015) (0.015)Year 2000 0.014 0.011

(0.015) (0.015)Mother has been admitted 0.001 0.000

(0.004) (0.004)Mother missing 0.002 0.000

(0.005) (0.005)Father’s months of schooling 0.000 0.000∗

(0.000) (0.000)Father missing 0.010∗ 0.009∗

(0.004) (0.004)Admitted in own municipality -0.002 -0.005

(0.005) (0.005)Admitted in Copenhagen 0.040∗∗∗ 0.043∗∗∗

(0.009) (0.009)Admitted in metropolitan area 0.036∗∗ 0.036∗∗

(0.012) (0.012)Disorder associated with substance use -0.001 -0.000

(0.005) (0.005)Psychosis, schizophrenia -0.000 -0.001

(0.006) (0.006)Nervous or stress-related 0.000 0.000

(0.005) (0.005)Personality disorder -0.006 -0.007

(0.005) (0.006)Affective/emotionel, pre-adult origin 0.009 0.014

(0.009) (0.009)Previous crime (0/1) -0.001 -0.004

(0.003) (0.003)Out of labor force in year -1 -0.005 -0.007∗

(0.003) (0.003)Unemployed in year -1 -0.003 -0.000

(0.004) (0.004)Observations 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 ini-tial contact) on gender (dummy), age at adm., mother’s age at birth, mothersyears of schooling, father’ age at birth, father’s years of schooling, motherhas prior psych. history (dummy), admitted in own municipality (dummy),greater CPH area (dummy), other metropolitan area (dummy), year dum-mies, and dummies for each F. diagnosis category form ICD-10. Standarderrors 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 PsychiatricHospital

OLS 2SLS 2SLS 2SLS3 months from 1st contact 0.115∗∗∗ 0.152∗ 0.160∗ 0.160∗

(0.005) (0.064) (0.066) (0.068)6 months from 1st contact 0.140∗∗∗ 0.134+ 0.162∗ 0.160∗

(0.005) (0.078) (0.077) (0.080)9 months from 1st contact 0.150∗∗∗ 0.129 0.158∗ 0.155+

(0.006) (0.081) (0.079) (0.082)12 months from 1st contact 0.167∗∗∗ 0.115 0.146+ 0.142+



(0.006) (0.078) (0.077) (0.078)21 months from 1st contact 0.188∗∗∗ 0.188∗ 0.222∗∗ 0.217∗∗


(0.006) (0.078) (0.079) (0.080)27 months from 1st contact 0.195∗∗∗ 0.176∗ 0.205∗ 0.199∗

(0.006) (0.078) (0.080) (0.080)30 months from 1st contact 0.196∗∗∗ 0.179∗ 0.210∗∗ 0.204∗

(0.006) (0.079) (0.081) (0.081)33 months from 1st contact 0.198∗∗∗ 0.172∗ 0.199∗ 0.193∗


(0.006) (0.078) (0.080) (0.079)Observations 24,277 24,277 24,277 24,277SES and demograpic controls X X XDiagnosis controls 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 0is month of initial contact. Standard errors clustered by hospital and monthin 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’syears of schooling, mother has prior psych. history (dummy), admitted in ownmunicipality (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

154

Table IIIA.4: Estimation Results on Likelihood of Subsequent Contact with PsychiatricHospitals

OLS 2SLS 2SLS 2SLS3 months from 1st contact 0.247∗∗∗ 0.079 0.093 0.096

(0.006) (0.091) (0.096) (0.097)6 months from 1st contact 0.261∗∗∗ 0.117 0.160 0.160





(0.007) (0.086) (0.090) (0.093)21 months from 1st contact 0.243∗∗∗ 0.124 0.157+ 0.152






(0.007) (0.088) (0.093) (0.094)Observations 24,277 24,277 24,277 24,277

Note: Table shows OLS and 2SLS regression results of inpatient admission(0/1) on subsequentcontact to psych. hospitals (0/1) corresponding to Fig-ure III.3. Time 0 is month of initial contact. Standard errors clustered byhospital 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’syears of schooling, mother has prior psych. history (dummy), admitted inown municipality (dummy), greater CPH area (dummy), other metropolitanarea (dummy), year dummies.Diagnosis controls include: Dummies for each F. diagnosis category fromICD-10.+p < .10;∗p < .05;∗∗p < .01; ∗∗∗p < .001

155

Table IIIA.5: Estimation Results on Subsequent Crimes

OLS 2SLS 2SLS 2SLS3 months from 1st contact 0.008∗∗∗ -0.034 -0.054+ -0.056+

(0.002) (0.026) (0.0285) (0.0291)6 months from 1st contact 0.023∗∗∗ -0.101+ -0.153∗ -0.156∗

(0.005) (0.061) (0.0675) (0.0690)9 months from 1st contact 0.036∗∗∗ -0.182+ -0.270∗ -0.277∗

(0.010) (0.110) (0.121) (0.124)12 months from 1st contact 0.055∗∗∗ -0.275 -0.405∗ -0.416∗




(0.034) (0.409) (0.449) (0.456)24 months from 1st contact 0.174∗∗∗ -0.678 -1.057+ -1.096+



(0.059) (0.706) (0.774) (0.789)33 months from 1st contact 0.323∗∗∗ -0.787 -1.437 -1.504

(0.069) (0.821) (0.899) (0.916)36 months from 1st contact 0.388∗∗∗ -0.781 -1.536 -1.615

(0.079) (0.943) (1.033) (1.051)Observations 24,277 24,277 24,277 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 initialcontact. 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’syears of schooling, Mother has prior psych. history (dummy), Admitted in ownmunicipality (dummy), Greater CPH area (dummy), Other metropolitan area(dummy), year dummies.Diagnosis controls include: Dummies for each F. diagnosis category form ICD-10.+p < .10;∗p < .05;∗∗p < .01; ∗∗∗p < .001

156

Table IIIA.6: Regional Robustness Checks

Without Copenhagen Without major citiesOLS 2SLS OLS 2SLS

Crime

3 months after first contact 0.008∗∗ −0.040 0.010∗∗∗ −0.034(0.003) (0.026) (0.003) (0.021)

6 months after first contact 0.013∗∗∗ −0.084∗ 0.014∗∗ −0.053(0.004) (0.040) (0.004) (0.033)

9 months after first contact 0.013∗ −0.096+ 0.012∗ −0.049(0.005) (0.056) (0.005) (0.046)

12 months after first contact 0.0123∗ −0.118+ 0.0132∗ −0.0559(0.006) (0.068) (0.006) (0.055)

15 months after first contact 0.016∗ −0.115 0.017∗ −0.059(0.007) (0.075) (0.007) (0.062)

18 months after first contact 0.020∗∗ −0.137 0.022∗∗ −0.088(0.007) (0.086) (0.008) (0.070)

21 months after first contact 0.024∗∗ −0.152+ 0.026∗∗ −0.090(0.008) (0.091) (0.009) (0.075)

24 months after first contact 0.028∗∗ −0.146 0.030∗∗ −0.086(0.009) (0.099) (0.010) (0.081)

27 months after first contact 0.032∗∗∗ −0.151 0.034∗∗ −0.089(0.010) (0.105) (0.011) (0.087)

30 months after first contact 0.040∗∗∗ −0.096 0.040∗∗∗ −0.054(0.011) (0.109) (0.012) (0.095)



Admissions

3 months after first contact 0.116∗∗∗ 0.171∗∗ 0.115∗∗∗ 0.124∗

(0.005) (0.066) (0.006) (0.053)6 months after first contact 0.143∗∗∗ 0.168∗ 0.137∗∗∗ 0.133∗


(0.006) (0.079) (0.007) (0.064)12 months after first contact 0.173∗∗∗ 0.148+ 0.167∗∗∗ 0.140∗



(0.006) (0.074) (0.007) (0.064)21 months after first contact 0.197∗∗∗ 0.212∗∗ 0.188∗∗∗ 0.180∗∗






(0.007) (0.074) (0.008) (0.065)Contacts

3 months after first contact 0.252∗∗∗ 0.121 0.251∗∗∗ 0.121(0.007) (0.097) (0.009) (0.074)

157

6 months after first contact 0.268∗∗∗ 0.160 0.263∗∗∗ 0.153∗

(0.007) (0.102) (0.008) (0.076)9 months after first contact 0.264∗∗∗ 0.148 0.260∗∗∗ 0.138+

(0.007) (0.098) (0.008) (0.072)12 months after first contact 0.264∗∗∗ 0.0993 0.259∗∗∗ 0.080









(0.008) (0.091) (0.009) (0.073)Employment

12 months after first contact −0.0525∗∗∗ −0.0834 −0.0517∗∗∗ −0.160∗

(0.008) (0.092) (0.009) (0.0726)24 months after first contact −0.0468∗∗∗ −0.130 −0.0496∗∗∗ −0.189∗∗

(0.008) (0.080) (0.009) (0.0658)36 months after first contact −0.0483∗∗∗ −0.238∗∗ −0.0526∗∗∗ −0.272∗∗∗

(0.008) (0.077) (0.009) (0.0669)Unemployment

12 months after first contact 0.015∗ −0.039 0.019∗∗ 0.050(0.006) (0.070) (0.007) (0.056)

24 months after first contact 0.012∗ 0.066 0.016∗ 0.111∗

(0.006) (0.065) (0.007) (0.053)36 months after first contact 0.007 0.056 0.007 0.109∗

(0.006) (0.056) (0.006) (0.048)Out of Labor Force

12 months after first contact 0.038∗∗∗ 0.123+ 0.033∗∗∗ 0.110+



(0.007) (0.070) (0.008) (0.060)

Observations 19595 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 errorsclustered 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

Tab

leIIIA

.7:Summarystatistics

bygender

andtreatm

entstatus

Not

Admitted,Fem

ale

Admitted,Fem

ale

Not

Admitted,Male

Admitted,Male

Immigrant

0.120

0.122

0.135

0.126

(0.325)

(0.327)

(0.342)

(0.332)

Age

atad

mission

30.401

31.778

31.394

31.959

(7.497)

(7.593)

(7.518)

(7.451)

Gross

incomein

year

-1179003.786

180252.508

213254.889

209616.192

(107239.963)

(103035.132)

(157252.309)

(141716.768)

Previouscrim

e(0/1)

0.123

0.159

0.435

0.479

(0.329)

(0.366)

(0.496)

(0.500)

Unem

ploymentdegreein

year

-10.168

0.187

0.192

0.196

(0.299)

(0.309)

(0.308)

(0.307)

Welfare

dep

endency

inyear

-10.386

0.353

0.300

0.284

(0.401)

(0.387)

(0.368)

(0.359)

Mother’smon

thsof

schooling

128.149

122.925

125.263

120.085

(34.394)

(33.387)

(34.406)

(33.558)

Father’smon

thsof

schooling

137.994

133.954

136.200

131.877

(34.794)

(34.734)

(35.076)

(35.292)

Mother’sageat

birth

26.275

26.249

26.132

26.138

(4.993)

(4.935)

(5.025)

(5.227)

Admittedin

ownmunicipality

0.170

0.156

0.161

0.158

(0.376)

(0.363)

(0.367)

(0.365)

Admittedin

Cop

enhagen

0.214

0.161

0.196

0.161

(0.410)

(0.368)

(0.397)

(0.367)

Admittedin

metropolitan

area

0.145

0.166

0.156

0.152

(0.352)

(0.372)

(0.363)

(0.359)

Disorder

associated

withsubstan

ceuse

0.050

0.107

0.228

0.298

(0.217)

(0.309)

(0.420)

(0.458)

Psychosis,schizop

hrenia

0.022

0.146

0.056

0.174

(0.148)

(0.353)

(0.230)

(0.379)

Affective

disorder

0.203

0.309

0.148

0.189

(0.402)

(0.462)

(0.355)

(0.392)

Nervousor

stress-related

0.571

0.340

0.413

0.276

(0.495)

(0.474)

(0.492)

(0.447)

Personalitydisorder

0.123

0.088

0.111

0.057

(0.328)

(0.284)

(0.314)

(0.232)

Affective/emotionel,pre-adultorigin

0.031

0.010

0.043

0.005

(0.174)

(0.100)

(0.204)

(0.073)

Observations

9763

3268

7165

4081

Note:

Tab

leshow

smeansandstd.dev.of

covariates

forthefullsample

divided

bytreatm

entstatusan

dgender.

159

Figure IIIA.1: Effect on Subsequent Crimes by Months Since 1st Contact for Outpatientsand 1st Discharge for Inpatients

Note: Figure shows 2SLS regression results of inpatient admission (0/1) on subsequent crimes where time 0is defined as hospital discharge instead of initial contact. The dashed lines indicate 95% confidence intervalsand the dotted line indicate 90% confidence intervals. Standard errors clustered by hospital and month inparentheses.SES and demographic controls include: Gender (dummy), age at adm., mother’s age at birth, mothers yearsof 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 oftreatment on two instruments (hospital specific contact intensity the two week prior to the individual’sinitial contact)and SES and demographic controls: Gender (dummy), age at adm., mother’s age at birth, mothers yearsof 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 dummiesand 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, admissionfor overdoses, and number of crimes re-estimated with a non-linear function in the first stage of the form:D = γ1z1 + γ2z2 + γ31[z1 > 0.4] + γ41[z2 > 0.4] + γ51[z1 > 0.4]z1 + γ61[z2 > 0.4]z2X

′ΠThe 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. SESand 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 ownmunicipality (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

�

�

�

��

��

�

�

�

�

��

� ��

� ��

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 geriat-

ric 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 popula-

tion. 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 set-

ting 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 construc-

ted 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

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