Essays in Education, Crime, and Job Displacement

Bennett, Patrick Doctoral Thesis Essays in Education, Crime, and Job Displacement PhD Series, No. 18.2016 Provided in Cooperation with: Copenhagen Business School (CBS) Suggested Citation: Bennett, Patrick (2016) : Essays in Education, Crime, and Job Displacement, PhD Series, No. 18.2016, ISBN 9788793483019, Copenhagen Business School (CBS), Frederiksberg, https://hdl.handle.net/10398/9308 This Version is available at: https://hdl.handle.net/10419/208972 Standard-Nutzungsbedingungen: Die Dokumente auf EconStor dürfen zu eigenen wissenschaftlichen Zwecken und zum Privatgebrauch gespeichert und kopiert werden. Sie dürfen die Dokumente nicht für öffentliche oder kommerzielle Zwecke vervielfältigen, öffentlich ausstellen, öffentlich zugänglich machen, vertreiben oder anderweitig nutzen. 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If the documents have been made available under an Open Content Licence (especially Creative Commons Licences), you may exercise further usage rights as specified in the indicated licence. https://creativecommons.org/licenses/by-nc-nd/3.0/ Patrick Bennett The PhD School of Economics and Management PhD Series 18.2016 PhD Series 18-2016ESSAYS IN EDUCATION, CRIME, AND JOB DISPLACEMENT COPENHAGEN BUSINESS SCHOOL SOLBJERG PLADS 3 DK-2000 FREDERIKSBERG DANMARK WWW.CBS.DK ISSN 0906-6934 Print ISBN: 978-87-93483-00-2 Online ISBN: 978-87-93483-01-9 ESSAYS IN EDUCATION, CRIME, AND JOB DISPLACEMENT Essays in Education, Crime, and Job Displacement Patrick Bennett Supervisors: Birthe Larsen and Lisbeth la Cour PhD School in Economics and Management Copenhagen Business School Patrick Bennett Essays in Education, Crime, and Job Displacement 1st edition 2016 PhD Series 18.2016 © Patrick Bennett ISSN 0906-6934 Print ISBN: 978-87-93483-00-2 Online ISBN:978-87-93483-01-9 “The Doctoral School of Economics and Management is an active national and international research environment at CBS for research degree students who deal with economics and management at business, industry and country level in a theoretical and empirical manner”. All rights reserved. No parts of this book may be reproduced or transmitted in any form or by any means, electronic or mechanical, including photocopying, recording, or by any information storage or retrieval system, without permission in writing from the publisher. Forward This Ph.D. thesis has been written over the course of my doctoral studies in the Department of Economics at the Copenhagen Business School. I am very grateful for the financial support provided by the Copenhagen Business School throughout my Ph.D. First and foremost, I wish to thank my two supervisors, Birthe Larsen and Lisbeth la Cour, for their numerous comments and suggestions, for our co-authorship, and more generally for always being so supportive and always being available. I wish to thank Amine Ouazad not only for our co-authorship but for providing so much guidance and insight throughout our relationship. During 2014, I was fortunate enough to visit the Swedish Institute for Social Research (SOFI), and I am grateful to Matthew Lindquist not only for the invitation but for all his support and to everyone else who provided feedback and insight during my stay at SOFI. I also wish to acknowledge the financial support from Otto Mønsteds Fond and Christian og Ottilia Brorsons Rejselegat which made my visit to SOFI possible. I am very grateful to Marcus Asplund for his detailed comments and work on the first chapter of my thesis. I also wish to thank all of those who have taught me throughout my academic career both in the UK and Denmark. I am very thankful for the thorough and invaluable comments I received during my Closing Seminar from Dario Pozzoli and Anna Piil Damm. Special thanks go to all of my colleagues at the Copenhagen Business School for the support at various seminars and workshops, but in particular Fane Groes for always helping with data questions, Moira Daly for always going the extra mile in helping me throughout my Ph.D., Jimmy Martínez-Correa for his support during the start of my Ph.D., and Dario Pozzoli for his encouragement throughout the last months of my Ph.D. I wish to also thank my Ph.D. colleagues not only for inspiring ideas and discussions but also for putting up with some of my less than desirable work habits—your presence will be missed. I also wish to thank the anonymous twins who revealed themselves at various stages in my relationships with them for providing anecdotal evidence on the twin lifestyle. Finally, I wish to thank mother for (quite correctly) teaching me to always print, my father for paving the way for Bennett graduates in Economics, and both of them for all that they have done. Thank you to my grandparents for always looking out for me and their constant support 3 throughout my academic career. A special thanks goes to all of my high school English teachers who, although they may never even see this, certainly deserve praise and appreciation for their tireless and underpaid educational efforts. Special thanks also go to Fabio Aricò for his words of encouragement, support, and assistance over the years, without which I wouldn’t be anywhere close to where I am today. Lastly, but certainly not least, I wish to thank my wife Anna for her endless support and for dealing with the countless late nights, weekends, and trips abroad required throughout my Ph.D. And to anyone who I mistakingly left out, please know I appreciate your efforts and please accept my sincere apologies for the omission. 4 Abstract With a limited budget and resources, governments must decide how to allocate funds across a variety of factors which benefit society such as education, crime deterrence, and public safety. Each increase in spending on one area comes with the knowledge that this money cannot be spent on social problems in another area. As such, externalities and unexpected spillover effects impact the costs and benefits of public spending to society and may have large and meaningful implications on how to most effectively allocate resources across a multitude of outcomes. For example, an increase in education corresponds to an increase in the opportunity cost of engaging in criminal activity, decreasing the probability an individual commits crime. Likewise, loss of employment decreases the opportunity cost of engaging in criminal activity, increasing the probability an individual commits crime. Discrimination towards immigrants can impact their employment prospects which, in turn, impacts their decision to further pursue education. Identifying how these individual level factors have an impact on society is key to informing and designing effective public policy. This Ph.D. thesis, entitled “Essays in Education, Crime, and Job Displacement”, analyzes the determinants and social implications of these three factors. While independent, each essay within this thesis examines the impact of factors such as education, in terms of reduced crime, job loss, in terms of increased crime, and discrimination, in terms of its impact on the educational attainment of immigrants, on society. The first essay of my thesis, “The Heterogeneous Effects of Education on Crime: Evidence from Danish Administrative Twin Data” examines whether education is equally effective in reducing crime for everyone. Education reduces crime, but this paper is the first to directly examine heterogeneous effects, in particular how the crime reducing capabilities of education depend on specific individuals and factors. I make use of twins contained in detailed Danish Register Data to control for characteristics, both observable and unobservable, which are common between twins. I focus on twin data as identification using twins provides many advantages—giving the freedom to explore the impact of many educational qualifications across the entire education distribution and directly estimating the effects of juvenile crime on educational attainment to examine reverse causality. I find that family factors are important, where education reduces crime for males of 5 low educated families, with less effects seen for individuals coming from highly educated families. Environmental factors are found to be less important—education lowers crime irrespective of the levels of crime in childhood neighborhoods. I find that the completion of high school lowers crime considerably while, contrary to expectations, the completion of vocational education is found to have no crime reducing effects. The role of juvenile crime is examined in great detail, revealing that taking into account participation in juvenile crime is important but that education reduces adult crime above and beyond what is explained through juvenile crime. My results imply that these specific “at risk” individuals obtain education which is less than socially optimal, as, in addition to the private benefits to education, the social benefits of education are large. The second essay, entitled “Job Displacement and Crime” investigates, together with Amine Ouazad, the individual level impacts of job loss on crime. While unemployment measured at an aggregate level causes crime, the extent to which a transition into unemployment increases crime is less clear, as previous literature has focused on measures of unemployment at the state or county level. We identify the impact of sudden and unexpected job loss on crime, using detailed police, employer, and employee data. Following Jacobson, LaLonde and Sullivan (1993), we examine high tenured workers with strong labor market ties to their firms. For these individuals, job loss occurring in a mass layoff event is likely sudden and unanticipated. We find that displaced individuals are significantly more likely to be convicted in the time following job loss, but importantly, not in the time before job loss. These effects are primarily seen for property crimes and are concentrated for individuals at the lower ends of the educational distribution. These effects are long lasting, particularly for individuals with less than high school education. Individuals educated to the university level or beyond are more resilient, in terms of criminality, to job loss. We examine a possible intergenerational effect where father’s job loss may impact the criminality of children, finding some evidence that sons are marginally more likely to commit crime in the short-run following father’s displacement. We see sizable, significant, and long lasting effects for individuals who live alone. Our results are robust to changing our mass-layoff criteria including increasing the number of employees who must lose their job to cause a mass-layoff event and altering how we define a mass-layoff event. We argue that neither employers nor employees fully internalize the social costs of job loss, which justifies an active role of policies which incentivize unemployed to transition back into formal employment or additional taxation of employers. The final essay of my thesis, “Negative Attitudes, Network and Education”, investigates, to6 gether with Lisbeth la Cour, Birthe Larsen, and Gisela Waisman, what factors can explain the educational gap that exists between natives and immigrants. We examine, both theoretically and empirically, the importance of two specific factors: negative attitudes towards immigrants and networking amongst immigrants. Theoretically, we formulate a Becker-style taste discrimination model within a search and wage bargaining setting where the educational decision of natives and immigrants is endogenous. We show that the education an immigrant obtains depends on negative attitudes, which directly influence their employment prospects. If all immigrants are equally affected by discrimination, immigrants obtain less education than natives. If only low skilled immigrants are affected by negative attitudes, immigrants obtain more education than natives to improve their employment prospects. We find that more immigration increases the fraction of educated immigrants via networking which also improves immigrant employment prospects. Empirically, we analyze the educational decision of young immigrants, specifically whether they decide to attend high school. We find evidence that negative attitudes against immigrants increase the likelihood male immigrants attend high school, supporting the case when discrimination is against only low skilled immigrants. We find evidence supporting our theoretical findings that networking amongst immigrants, in the form of a higher fraction of own nationality immigrants for females and a higher fraction of own nationality immigrants who are employed for males, increases the likelihood young immigrants attend high school. Due to the fact that immigrant’s can selectively locate, we examine how our results change taking into account unobservable factors which could drive these decisions. We show that, under reasonable assumptions regarding the role of unobservables, that while unobservables do explain a portion of our results, they are unable to completely explain the positive impact of negative attitudes on education we see for males. Our results are also robust to excluding those families who have recently relocated and are explained almost entirely by an impact on 1st generation immigrants. 7 14 Introduction This Ph.D. thesis is composed of three chapters and ends with a general conclusion for all three chapters. It should be noted that while all three chapters are independent research papers and can be read as such, they all address important topics within the field of Labor Economics. More specifically, all three chapters analyze the determinants and social implications of education, crime, and job displacement. The first chapter finds that education is not equally effective in lowering crime for everyone, and identifies specific individuals for whom we can expect education to have an impact on criminal activity. The second chapter finds that job displacement, sudden and unexpected job loss in a mass-layoff event, increases the probability of committing crime and that the magnitude and longevity of these effects depend on education, household factors, and post-displacement employment outcomes. The third chapter proposes two potential explanations of the educational gap that exists between immigrants and natives, negative attitudes towards immigrants and networking, finding that while networking amongst immigrants can reduce this gap, negative attitudes motivate immigrants to pursue further education and, as such, are unable to explain this gap in education. All three of these chapters are motivated by and build upon existing literature and make unique and novel contributions within their respective fields. Over the last decade, economists have established that education has a negative and significant impact on an individual’s propensity to commit crime. There are numerous studies establishing this fact (Lochner and Moretti 2004; Machin et al. 2011; Åslund et al. 2015; Hjalmarsson et al. 2015), which generally find that education has a negative and causal impact on crime. There are many reasons education is expected to lower crime, for example by increasing the opportunity cost of crime or by impacting individual factors such as instilling social values or increasing the patience of individuals. The motivation behind the first chapter is to recognize that while, overall, education reduces crime, that this may not be true for everyone and important heterogeneity in the crime reducing capabilities of education may exist below this overall effect. Similarly, the second chapter is motivated by the fact that unemployment and crime are related at an aggregate level (Raphael and Winter-Ebmer 2001; Gould et al. 2002; Öster and Agell 2007; Lin 2008; Fougère et al. 2009), but practically nothing 15 is known about the individual level relationship between becoming unemployed and engaging in crime. Job loss can impact crime by lowering the opportunity cost of crime but also by having a psychological impact on the individual, and there are many reasons to believe the individual level and aggregate impacts may differ, in terms of both types of crime and the longevity of the effects. Finally, the third chapter combines and expands on two strands of existing literature: one which analyzes the impacts of discrimination on employment and wages (Mailath et al. 2000; Lang et al. 2005; Charles and Guryan 2008; Waisman and Larsen 2015) but without the additional analysis of an individual’s educational decision and another which analyzes the importance of networking in securing employment (Calvó-Armengol and Jackson 2004; Andersson et al. 2009; Kramarz and Skans 2014). Negative attitudes may lead immigrants to obtain lower education, if immigrants are equally affected by discrimination, or may lead immigrant’s to obtain more education, if only low-skilled immigrants are affected by education, while networking will increases education. Within all of these strands of existing literature, a common underlying point of emphasis is the identification of a causal relationship between the explanatory variable and the outcome of interest. However, the methods used to estimate causal impacts differ across these fields. To examine the crime reducing effects of education, many studies have used changes in compulsory schooling laws; the first chapter of this thesis takes a different approach—controlling for characteristics which are common between twins. The previous literature on unemployment and crime has relied on exogenous changes at the state or county levels which impact unemployment but not crime; the second chapter relies on sudden and unexpected mass-layoffs at the individual level to generate exogenous changes in unemployment. The third chapter focuses on a sample of young immigrants for whom household location is plausibly exogenous to their educational decision and, additionally, provides evidence on the role of unobservable factors in explaining the findings. All three chapters make use of detailed administrative population data from Denmark. Danish Register Data, which is maintained and provided by Statistics Denmark, is a panel dataset compiled from various administrative sources which completely covers the entire Danish population. The detail and depth of this data is useful for assessing the heterogeneous impacts of education on crime, enables the linking of matched employer-employee data to police data to analyze the impacts of job displacement on crime, and the institutional structure of the educational system of Denmark enables the analysis of the impact of negative attitudes on a non-compulsory decision to attend further education. All three chapters would not be possible using other non-Register based data 16 sources where either information would not be detailed enough, data would simply not be available, or the timing of a crucial education decision would be either too early or too late. 17 Andersson, F., S. Burgess, and J. Lane (2009). Do as the neighbors do: The impact of social networks on immigrant employment. IZA Discussion Papers 4423, Institute for the Study of Labor (IZA). Åslund, O., H. Grönqvist, C. Hall, and J. Vlachos (2015). Education and criminal behavior: Insights from an expansion of upper secondary school. IZA Discussion Papers 9374, Institute for the Study of Labor (IZA). Calvó-Armengol, A. and M. O. Jackson (2004). The effects of social networks on employment and inequality. American Economic Review 94(3), 426–454. Charles, K. K. and J. Guryan (2008). Prejudice and wages: An empirical assessment of becker’s The Economics of Discrimination.Journal of Political Economy 116(5), 773–809. Fougère, D., F. Kramarz, and J. Pouget (2009). Youth unemployment and crime in france. Journal of the European Economic Association 7(5), 909–938. Gould, E. D., B. A. Weinberg, and D. B. Mustard (2002). Crime rates and local labor market opportunities in the united states: 1979–1997. Review of Economics and Statistics 84(1), 45–61. Hjalmarsson, R., H. Holmlund, and M. J. Lindquist (2015). The effect of education on criminal convictions and incarceration: Causal evidence from micro-data. The Economic Journal 125(587), 1290–1326. Kramarz, F. and O. N. Skans (2014). When strong ties are strong: Networks and youth labour market entry. The Review of Economic Studies. Lang, K., M. Manove, and W. T. Dickens (2005). Racial discrimination in labor markets with posted wage offers. American Economic Review 95(4), 1327–1340. Lin, M.-J. (2008). Does unemployment increase crime?: Evidence from u.s. data 1974-2000. Journal of Human Resources 43(2), 413–436. Lochner, L. and E. Moretti (2004). The effect of education on crime: Evidence from prison inmates, arrests, and self-reports. American Economic Review 94(1), 155–189. Machin, S., O. Marie, and S. Vujić (2011). The crime reducing effect of education. The Economic Journal 121(552), 463–484. Mailath, G. J., L. Samuelson, and A. Shaked (2000). Endogenous inequality in integrated labor markets with two-sided search. American Economic Review 90(1), 46–72. Öster, A. and J. Agell (2007). Crime and unemployment in turbulent times. Journal of the European Economic Association 5(4), 752–775. Raphael, S. and R. Winter-Ebmer (2001). Identifying the effect of unemployment on crime. Journal of Law and Economics 44(1), 259–283. Waisman, G. and B. Larsen (2015). Wages, amenities and negative attitudes. Mimeo. 18 Chapter 1 - The Heterogeneous Effects of Education on Crime: Evidence from Danish Administrative Twin Data 19 20 The Heterogeneous Effects of Education on Crime: Evidence from Danish Administrative Twin Data Patrick Bennett March 2016 Abstract Using administrative Danish Register Data to identify all twins aged 18-35 in 2000, this paper identifies heterogeneous effects of education on crime. Controlling for genetic and environmental factors, an additional year of education significantly lowers the probability of conviction for total, property, and violent crimes by 14%, 12%, and 19% for males. Estimation by parental education reveals family factors matter—education overwhelmingly lowers crime for children of low educated parents—while estimation by exposure to crime during childhood reveals environmental factors have less impact on the relationship between education and crime. Examining different educational programs reveals the completion of high school matters for crime reduction of males, while the completion of vocational training or university do not. These results are robust to correcting for the presence of dizygotic twins, directly estimating reverse causality between education and crime, and using data on incarcerations instead of convictions. JEL classification: I2, K42 Acknowledgments: The author wishes to thank Birthe Larsen, Lisbeth la Cour, Paolo Buonanno, Fane Groes, Moira Daly, Matthew Lindquist, Kevin Schnepel, Marcus Asplund, Dario Pozzoli, Anna Piil Damm as well as seminar participants at the Copenhagen Business School and the Swedish Institute for Social Research (SOFI) and participants of the Economics of Crime workshop at the University of Copenhagen, the 2014 SMYE, the 2014 CEN Workshop, the 2014 DGPE, and the 2015 RES Conference and Symposium of Junior Researchers. Copenhagen Business School, Department of Economics, Porcelænshaven 16A, 2000 Frederiksberg, Denmark. [email protected] 21 1 Introduction Education reduces crime—this fact has been established in a number of studies. This is true for both years of education as well as the completion of high school. This is also true for multiple crime types—total, property, and, in most instances, violent crimes. But is education equally effective in reducing crime for everyone? Given the vast differences in not only types of crime but also the motivating factors behind these crimes, there is good reason to believe education impacts the criminal behavior of specific types of individuals very differently. This paper analyzes heterogeneity in the crime reducing capabilities of education using Danish twin data, and makes three important contributions to the literature. First, heterogeneous effects are examined across family factors such as parental education as well as environmental factors such as growing up in neighborhoods with high and low levels of crime. Second, it evaluates the importance of specific educational qualifications and programs for the crime reducing effects of education. Third, it expands upon Webbink et al. (2013) by providing more generalizable results which use administrative twin panel data rather than self reported survey data, analyzing both male and female twin pairs, and examining detailed crime types in addition to investigating heterogeneity along other dimensions. Previous studies (Lochner and Moretti 2004; Machin et al. 2011; Meghir et al. 2012; Hjalmarsson et al. 2015) typically exploit changes in compulsory schooling laws to provide causal interpretations of the effects of education on crime. This paper takes a different approach—controlling for characteristics which are common between twins. As twins are genetically similar and are usually raised in the same environment as children, many unobservable factors which affect both education and crime are controlled for by comparing the outcomes of one twin to the other. Additionally, twin estimation is capable of estimating effects across the entire educational distribution of the population and not only for those at the lower end of the distribution. Using within twin fixed effects estimation, this paper confirms the existence of significant negative effects of years of education on the probability of conviction for male twins of total and violent crimes, with marginally significant effects seen for property crimes. An additional year of education lowers the probability a male twin was convicted of any crime committed from 2001-2006 by 14%, of a property crime by 12%, and of a violent crime by 19%. Involvement in juvenile crime significantly increases an individual’s probability of being convicted as an adult, but to less of an 22 extent than has been found previously (Webbink et al. 2013). Having confirmed education reduces an individual’s probability of conviction as an adult, the paper examines the presence of heterogeneous effects of education on crime. Family factors are found to be important—the effects of education on crime are large in magnitude for those from a low educated household and, with the exception of violent crimes, virtually non-existent for those with two highly educated parents. Environmental factors are found to be less important— education lowers crime irrespective of the levels of crime in the neighborhood twins are exposed to during childhood. Examining different educational qualifications reveals that the completion of high school is important in terms of crime reduction for males. However, contrary to expectations, the completion of vocational training geared directly towards professional employment has no effects on a male’s propensity to engage in crime. When analyzing every available crime type for male twins, education significantly decreases participation in firearms and alcohol related traffic offenses, with marginally significant effects found for sexual and other crimes. Isolating heterogeneous effects of education on crime which are causal in nature represents an empirical challenge. This relationship is complicated by the fact that education decisions are endogenous—more crime prone individuals are both less likely to pursue education and more likely to commit crime—and causality flows in both directions—participation in crime as a juvenile can directly affect the level of schooling an individual obtains. In addition to identifying causal effects of education on crime, there are many other advantages to using within twin estimation which enable the examination of heterogeneity in the effects of education on crime. Firstly, effects are identified over the entire population, not from those who comply with compulsory schooling reforms at the lower end of the educational distribution. Secondly, the analysis is not constrained to one specific educational change, giving the freedom to analyze the impact of multiple educational qualifications and time periods. Thirdly, estimation within twins enables the analysis of reverse causality between education and crime. Despite the prominent use of twin studies within Economics,1there are also limitations to using twin data. Specifically, while monozygotic (MZ) twins are virtually genetically identical, differences in unobservable factors which affect both education and, in this paper, crime participation are 1Twin studies have long been used in Economics, and particularly in the education literature, to estimate the returns to education (Ashenfelter and Krueger 1994; Ashenfelter and Rouse 1998; Isacsson 1999), the intergenerational transmission of education (Behrman and Rosenzweig 2002; Holmlund et al. 2011; Pronzato 2012; Lundborg et al. 2014), the impact of spousal education on earnings (Huang et al. 2009), and even in the portfolio choice literature (Calvet and Sodini 2014). 23 age ranges used in the final sample of twins described below. Taking these numbers as correct, eliminating different gendered twins from the estimation sample eliminates approximately half of the DZ twins from the entire twin sample. In addition to this, it is also necessary to eliminate twins for whom data is unobservable at the ages of 15 and 16 in order to observe juvenile criminality. This imposes two additional restrictions: (1) limiting the sample to twins who are, at a maximum, aged 15 in 1980 when the data begins and (2) eliminating those who are not in the data at the ages of 15 or 16. Imposing these restrictions eliminates 12,314 twins who are either older than 15 in 1980, who are not present in the data as a juvenile, or whose twin is not present in the data as a juvenile from the potential estimation sample that could be used. While not ideal, this restriction is necessary in order to control for, as in Webbink et al. (2013), whether a twin was convicted of any crime as a juvenile. It is worth noting that this restriction excludes any twin who is 36 or older in 2000, imposing an upper bound on the age of twins by construction. While this may be of concern, individuals aged 18-35 can be thought of as an age range where a large portion of offending takes place, and results which include all twins, produce similar (in terms of sign and significance), but unequivocally smaller effects of education on crime.10 This smaller magnitude of the effects of education on crime in the unrestricted sample is likely attributable to the use of an older sample, as young individuals are more likely to offend. As juvenile criminality is a strong predictor of adult criminality, controlling for juvenile criminality is likely to be quantitatively important. Specifically, controlling for juvenile crime history can be thought to capture unobservable characteristics that vary within twin pairs and determine adult criminality.11 Throughout this paper, juvenile crime is captured through the inclusion of two control variables: whether an individual was convicted of a crime while aged 15 and whether an individual was convicted of a crime while aged 16.12 Juvenile crime is analyzed separately by age to examine if the timing of juvenile crime matters for the effects of education on crime. Limiting the variable to crimes committed below the age of 17 increases the plausible exogeneity of this proxy variable, as younger persons are still restricted by compulsory schooling laws and are 10Results available upon request. 11In addition to being a proxy for unobservables, the inclusion of a juvenile crime dummy could also be interpreted as including a lag dependent variable, which in the use of within twin fixed effects estimation, would produce biased results. 12The age of criminal responsibility in Denmark is 15. Due to this, any crimes committed by individuals aged 14 and younger are not observable in the data. Age is recorded as the exact age when an individual is charged by the police with a crime. 30 legally unable to leave school. Because of this, juvenile crime committed within the compulsory schooling window are less likely to directly affect an individual’s educational attainment. While 15 year olds will still be restricted by these laws, some 16 year olds will have completed compulsory schooling during the age of 16. While using only 15 year olds would ensure students are still bound by compulsory schooling laws, including 16 year olds as well provides a more complete picture of juvenile delinquency. It should be noted that specifications excluding the juvenile crime at age 16 control and specifications including the control produce similar results. Because the extent to which a juvenile delinquency dummy can be considered truly exogenous in a regression of crime on education is perhaps uncertain, all baseline results are reported both with and without controls for juvenile crime history. 4.2 Crime and Education Definitions Given the panel nature of Danish Register Data, a very complete picture of an individual’s criminal history is observable. However, as with any administrative individual-level crime data, individuals are only classified as criminals if they are apprehended for the crime committed. Due to this, there could be measurement error in the crime data. In particular, if more skilled or clever criminals are both more educated and also better able to avoid detection, then the estimates of the effects of education on crime will be biased. As alternative measures of criminal activity, such as selfreported crime are unavailable, there is little that can be done to investigate this potential issue. However, as Danish Register Data is linked directly to police records, any individual either charged, convicted, or incarcerated in Denmark can be classified as a criminal. Using detailed crime codes, it is possible to identify types of offenses (property, violent, etc) as well as specific offenses (assault, motor vehicle theft, etc). The obvious concern with using detailed offenses is that to begin with, each offense does not contain many individual observations, a problem which is only compounded when estimating within twins. As such, broad offense categories, such as total, property, and violent crimes, are used. Total crimes correspond to the Danish classification of offenses are comprised of: sexual, violent, property, alcohol related traffic, narcotics, firearms, tax, unknown, and other crimes, as well as crimes against special legislation.13 A detailed discussion of crime types, as well as the offenses that make up property and violent crimes, can be found in Appendix A. Throughout this paper, crime is defined as a binary variable indicating if a twin has been 13This excludes traffic violations and citations, accidents, etc which are also recorded in police data. 31 convicted of a crime which was committed between 2001-2006,14 while education is measured as the highest education an individual has obtained in 2000. Using only the year 2000 enables the use of within twin fixed effects estimation, while using whether a twin was convicted in the 6 years following 2000 provides a more complete picture of offending than if a single year was used.15 A summary of Denmark during the time period of the analysis is provided in Appendix B. A major advantage of using Danish Register Data for twin estimation is that, unlike most twin datasets, data is not obtained through surveys of twins, but through administrative sources. One problem in using twin survey data is that it is subject to measurement error, caused primarily by twin recall errors. In addition, selective response amongst surveyed twins can introduce selection bias if twins who do not respond to the survey differ systematically from twins who do respond. As Danish Register Data is linked directly to administrative sources, within twin estimation conducted in this paper is free from measurement error caused by twin recall errors and selection problems which remain in twin survey data. However, as years of education is calculated based on achieved qualifications, this could introduce measurement error in education length if a twin takes either more or less years to achieve a given qualification. Due to this, education defined in terms of the qualification achieved is also analyzed in addition to years of education. 5 Summary Statistics Mean values and standard deviations for relevant determinants of an individual’s criminal propensity included in the analysis for the twin sample are summarized in Table 2. These values are separated by whether or not an individual was convicted of a crime committed from 2001-2006 in columns (1) and (2) respectively. Two striking differences appear when comparing these two columns, the differences in years of education and whether an individual was convicted of a crime as a juvenile. Those convicted of some crime, on the whole, receive 1.5 years less of education, and are 9 and 10 percentage points more likely to have been convicted of a crime at age 15 and 16 respectively. The gender difference in criminals, which has long been documented by economists and crimi14Specifically, whether an individual was convicted of a crime which was committed between January 1, 2001 to December 31, 2006. For a small fraction of crimes, the date of the offense is unobservable. For these crimes, the date of conviction is used instead. Estimation using the date of conviction or only those offenses with a date of offense produce similar results. 15While the results do fluctuate slightly between the chosen year, results are relatively stable across years, and are available upon request. 32 Table 2: Summary Statistics of Sample of Twins by Whether Charged with Crime or Not During 2001-2005 (1) (2) (3) (4) Variable Not Convicted of Crime Convicted of Crime Total (1)-(2) Committed 2001-2006 Committed 2001-2006 Years of Education 12.46 10.97 12.38 1.49** (2.18) (2.11) (2.20) [17.3] Male 0.48 0.86 0.51 -0.38** (0.50) (0.35) (0.50) [-19.2] Age 27.82 27.06 27.77 0.75** (4.99) (5.38) (5.02) [3.8] Juvenile Crime 15 0.01 0.10 0.02 -0.09** (0.11) (0.31) (0.13) [-17.9] Juvenile Crime 16 0.01 0.11 0.02 -0.10** (0.12) (0.32) (0.14) [-18.1] Parents Highly Educated†0.43 0.35 0.42 0.08** (0.49) (0.48) (0.49) [3.6] High Crime Municipality at 15 0.66 0.71 0.66 -0.05* (0.47) (0.46) (0.47) [-2.6] Number of Twins 11276 670 11946 Fraction of Twin Sample 94.39% 5.61% 100% Mean values for 2000 values. Standard deviations in parentheses, t statistics reported in brackets. **, *, and + correspond to significance at the 1% 5% and 10% levels respectively. †: sample sizes for Both Parents Highly Educated are 9,888, 548, and 10,436 respectively due to missing parental education information. nologists, is also visible in Table 2, with 86% of twins convicted during 2001-2006 being male. For twins whose parental education information is available, those convicted as an adult also have a lower fraction of parents who are both highly educated, a point which is investigated further in Section 8. The fraction of twins convicted of some crime in 2001-2006, 5.6% of the sample twin population, is also reported in the bottom of Table 2. Consistent with the descriptive evidence on the links between education and crime, Figure 1 displays the fraction of twins with certain years of education separated by whether a twin was convicted of a crime committed from 2001-2006 or not.16 Twins who are convicted of any crime are, on the whole, less educated than twins who are not convicted, with more than 60% of those convicted with a crime receiving 10 years or less of education. Conversely, there are less twins who are not convicted of a crime educated only 10 years or less, with a large fraction of twin pairs receiving 12 years or more of education. 16In order to comply with Statistics Denmark’s data confidentiality criteria, individuals with 17 or more years of education are not presented in Figure 1. 33 Figure 1: Percentage of Twins with Years of Education Separated by Criminality 34 Table 3 displays the distribution of crimes by type for twins convicted from 2001-2006 for both males and females combined. The majority of convictions are alcohol related traffic offenses followed by property crimes. The total number of convictions in Table 3 does not perfectly match the total number of twins convicted with a crime in Table 2 as there are some twins who are convicted of multiple types of crime during this time period. Table 3: Distribution of Crimes by Type (1) (2) Both Male and Female Twin Pairs Crime Type # Twins % Convicted Number Twins Convicted 670 Of Any Crime Sexual 17 1.9% Violent 129 14.3% Property 221 24.6% Other 65 7.2% Alcohol Related Traffic 225 25.0% Narcotics 103 11.4% Firearms 39 4.3% Special Legislation 101 11.2% Sum of All Types 900 100% Number of Twins 11946 Sum of all convictions is greater than the number of individuals convicted of any crime due to individuals being convicted of multiple crime types from 2001-2006. Percents in column (2) correspond to percentage of sum of all crime types (900) for a given crime. Twins are not separated by gender in order to comply with Statistics Denmark’s data confidentiality criteria. Table 4 displays within twin differences in years of education. In 2000, 55% of twin pairs have different education lengths, with the vast majority of twins having differences of 4 years or less in educational attainment. 6 Empirical Framework An advantage of using within twin estimation is it is possible to control for factors (both observable and unobservable) which both affect an individual’s probability to engage in crime and are constant between twins, including genetic, environmental, and familial factors. By estimating fixed effects 35 Table 4: Distribution of Education Differences by Twin Pair Differences in Years Frequency Percent Cumulative Percent 0 2675 44.78 44.78 1 1230 20.59 65.38 2 750 12.56 77.93 3 671 11.23 89.17 4 383 6.41 95.58 5 187 3.13 98.71 6 46 0.77 99.48 7+ years 31 0.52 100.00 Number of Twin Pairs 5973 100.00 within twin pair, variation in twin education levels enables the estimation of causal effects of education on crime. To obtain causal estimates, the following linear probability17 fixed effects regression is estimated: Cij =β(Sij) + φ1(J15 ij ) + φ2(J16 ij ) + γ(Aij) + αi+εij (1) Cij represents whether twin jin twin pair iwas convicted from 2001-2006 and is explained by: Sij, the years of schooling of twin jin twin pair i;J15 ij and J16 ij , control variables for whether twin jin twin pair iwas convicted of a crime as a juvenile at age 15 or 16; Aij, unobservable factors which vary across both twin pairs and twins; αi, unobservable factors which are identical to twins but vary across twin pairs; and εij, the (criminal) error term. To further explore the assumptions necessary for within twin fixed effects estimation to identify causal effects, the (criminal) error term, as in Bound and Solon (1999), can be expanded into two separate components: a component which is constant between twins and a component which is random, but only to twin jin twin pair i. εij =fi+uij (2) 17A linear probability model is used in order to facilitate the comparison of coefficients across specifications to see how the estimated effects change when examining the heterogeneity and robustness of the baseline results. Estimation using logit provide similar results, and are available upon request. 36 Additionally, an individual’s schooling can be explained by: Sij =δ1(Aij) + gi+wij (3) Within twin fixed effects estimation is able to account for fi, the portion of εij which is constant within twin pair. Thus, as with any twin study, the identifying assumption is that differences in education are driven by factors which do not also impact the outcome of interest, here crime participation. In other words, it is assumed that differences in schooling levels are caused by random factors (wij) which are unrelated to an individual’s propensity to engage in crime, cov(uij, wij)=0, and also cov(Aij, wij) = 0, so that schooling and crime are not correlated through Aij when estimating within twins. Related to this, it is required that Ai1=Ai2, otherwise differences in schooling are driven by differences in unobservable factors which vary between twins. In order for equation (1) to produce unbiased estimates, these assumptions must hold. If differences in factors that affect both education and crime participation drive variation in twin education levels,18 then within twin fixed effects estimates will be biased. An additional concern is the critique of Bound and Solon (1999) who, building upon the work of Griliches (1979), state that while MZ twins are nearly genetically identical, differences in unobservable factors19 which affect both education and, in this paper, crime decisions are determined by more than just genetic factors as twins experience different factors during their development. Twins are exposed to a variety of different environmental factors, particularly in school, and while genetically they may be similar, these environmental differences can contribute to unobservable differences which may be driving both crime and education decisions. This criticism is related to the assumption of the equality of unobservable factors between twins, Ai1=Ai2. If unobservable factors between twins are different, then within twin estimation will produce biased estimates. To further investigate this criticism, Aij can be broken down into two separate components: Aij =Gi+Eij +µij (4) where Giare unobservable factors which are the same between twins (genetic factors) and Eij are unobservable factors which can vary both within and across twin pairs (environmental factors). 18For example time discounting or risk aversion. 19The classic example is ability 37 Twins experiencing different environmental factors is equivalent to the case where Ei16=Ei2. In this case, unobservable factors (Aij), which affect both schooling and criminality are different and within twin estimation will produce biased results. While it is not straightforward to test the validity of assuming Ai1=Ai2, one important factor that can be exploited, as previously mentioned, is to exclude twins who were raised in separate households as children. In this case, the environmental factors between twins are vastly different, and this identifying assumption for within twin estimation in all likelihood does not hold, as Ei16=Ei2, and Ai16=Ai2. One additional concern is that early differences in health, potentially from the time of birth, could drive differences in twin education levels. In particular, competition for nutrients in utero could cause poor health outcomes of one twin and not another leading to differences in, for example, birth weight and these differences could potentially determine the within twin variation in education levels. Using Swedish data, Sandewall et al. (2014) empirically investigate these concerns over the validity of the identifying assumptions of twin studies, finding that the estimated effects of education on wages fall when including measures such as twin birth weight and IQ scores into standard twin earnings regressions. As such, the author’s question the validity of the identifying assumptions in twin studies. There is also a large literature, commonly using twins as an identification strategy, which analyzes the impact of infant health and birth weight on numerous adult outcomes such as employment, education, and mortality. This literature has produced mixed findings in that some papers find that differences in early health outcomes such as birth weight and Apgar infant health scores20 have no effects on the probability of twin’s attending high school at the age of 17 (Oreopoulos et al. 2008), estimate an effect of birth weight on education which is very small in magnitude (Royer 2009), or estimate an impact of twin birth weight on high school completion which is larger in magnitude (Black et al. 2007). While these studies tend to report some variation in the early health outcomes of twins, for example Oreopoulos et al. (2008) report differences in Apgar scores and birth weight, these differences are often not important enough to explain a large portion the differences in education between two twins. While the similarity of twins remains a concern here, Section 9.3 presents differences in GPA for a subset of twins for whom GPA information is available, as birth weight, IQ, or other early health measures are unavailable for the sample of twins used in this paper. 20Apgar scores measure newborn health over five criteria, where the scores range from 0-10. 38 A related concern could be that one twin is born with a congenital birth defect, which could also drive differences in twin educational levels. However, previous studies have reported these defects affecting either twin are very rare,21 and are unlikely to be of major concern. One final possibility is that behavioral disorders affecting one twin could drive differences in education levels. In the working paper version of Webbink et al. (2013) (Webbink et al. 2008), the authors find that controlling for juvenile crime has a much larger impact on the effects of education on crime than when controlling for conduct disorders. While concerns over behavioral disorders may remain, it seems likely that controlling for juvenile crime will be more quantitatively important in estimating the impact of education on crime. 7 Results 7.1 OLS Estimation on Population Compared with Existing Results Prior to examining the heterogeneous effects of education on crime, it is first worthwhile to establish whether the Danish population provides a good basis for comparing how the effects of education on crime depend on specific factors and individuals by comparing results for the general population to existing findings in the literature. If population results across countries are similar, it is suggestive that the heterogeneous effects found in Denmark are not due to something particular about Danish data. A natural point of comparison is Hjalmarsson et al. (2015), who use Swedish population data which is Register based and collected in a similar fashion. However, lacking a similar instrument, OLS results are the only results that can be compared. Wherever possible, this separate population data is constructed to ensure the comparability of the Danish data with the dataset used in Hjalmarsson et al. (2015). For example, the exact same birth cohorts (1943-1954) are used, and the definitions of crime and education are identical. The main difference results from the fact that Danish Register Data only begins in 1980, while the Swedish data can be linked back to 1960. As such, factors such as municipality of residence and educational attainment are recorded at the start of 1980 and not earlier, and crime data is only available from 1980-2007 instead of from 1973-2007 as in the Swedish data. OLS results on Denmark are presented in columns (1) and (2) of Table 5 and for Sweden in columns (3) and (4). Despite these minor differences in the years available, OLS results using 21For example, Black et al. (2007) report excluding only 2.1% of twin pairs from their sample where either twin has a birth defect. 39 of years of education on total and property crimes are both small in magnitude and insignificant, where these differences between low and highly educated families are significant for total crimes. For females, there appear to be no significant effects of education on adult crime for either low or highly educated families, although the estimated effect of education on adult crime is negative for low educated families, but far from significant. Appendix C analyzes the role of parental education in further detail, presenting results of the three parental education subgroups which comprise at least one parent with low education: those with both parents low educated, those with a low educated mother but high educated father, and those with a high educated mother but low educated father. However, due to the small number of twins in each of these groups, the results should be interpreted with some degree of caution. Taking this into account, Table A1 indicates some non-linearity in the effects of education on crime by parental education: male twins with two low educated parents experience the largest effects of education on total crime while those with one low educated parent, either mother or father, and one high educated parent experience less crime reducing effects of education. For female twins, as before, there appear to be no significant effects of education on crime. The results presented in Tables 10 and A1 lead to the conclusion that parental education matters for the crime reducing effects of education of their children, where for males with at least one low educated parent, there are large crime reducing capabilities of education, but for males of highly educated parents, there are little crime reducing benefits of education. The fact that no effects are seen for females of low educated families reinforces the previous finding that education can reduce crime predominantly only for males. Three separate, but interrelated, explanations of these findings seem plausible. Firstly, Table 10 could simply be capturing the intergenerational transmission of education. If individuals with highly educated parents obtain more education and there is less crime reduction caused by higher education than lower education, then the lack of any negative effect seen for highly educated parents is due to the higher educational attainment of their children. Secondly, education could act as an adjusting mechanism, in that an additional year of education in terms of crime reduction, is very important for children of a low educated family and not very important for children of a high educated family. If, for whatever reason, children of low educated parents are more disposed to commit crime, then an additional year of education would have greater crime reducing benefits for these children. A third explanation could be that parental education captures “good parenting”, and good parenting simultaneously leads to both more ed46 ucation and less crime. Lacking a way to disentangle these potential explanations, identifying the exact cause of these differential effects of education on crime across parental education is beyond the scope of the paper. However, given the supportive evidence of the last two mechanisms found in Meghir et al. (2012), it seems likely that parenting or social mobility are fundamental reasons for the heterogeneous effects across parental education. 8.2 Growing Up In High or Low Crime Neighborhood In addition to family factors, environmental factors could also have differential impacts on the effects of education on crime. Many studies examine the Moving to Opportunity (MTO) experiments, which randomly allocate moving vouchers to low income families, to analyze the effects of moving to a better neighborhood on both education and criminal outcomes. Sanbonmatsu et al. (2006) find that children of families who were offered moving vouchers performed no better in school, while Chetty et al. (2015) find that, in the longer run, children moving to a neighborhood with less poverty at young ages are more likely to attend college and have higher wages. Kling et al. (2005) look at the effects of moving to a lower poverty/crime area on crime, finding that both males and females are less likely to engage in crime in the short run, while for males, participation in property crime actually increases in the long run. Damm and Dustmann (2014) use an exogenous placement scheme of refugees to examine in the impact of living in a high crime neighborhood, finding the share of young individuals convicted in neighborhoods increases the likelihood of conviction for male refugees later in life. Growing up in a high crime area could also have a strong impact on the effects of education on crime. For instance, those residing in a high crime area could be more likely to engage in juvenile crime and/or less likely to pursue education. At the same time, those residing in higher crime areas could, all else equal, have larger returns to education than those residing in lower crime areas. As the sample of twins constructed all reside in the same household during childhood, and hence same municipality, both twins are exposed similarly to these environmental factors. Table 11 examines the impact of growing up in a high or low crime area on the effects of education on adult crime for a predetermined neighborhood.25 High crime neighborhoods are defined as a municipality where the youth conviction rate is higher than the youth conviction rate of the median municipality in that year. Youth conviction rate is defined, as in Damm and 25Across all twins, municipality of residence is measured in the year twins are age 15. Results are robust to alternative definitions of municipality. There are 275 municipalities in the time period analyzed in Denmark. 47 Dustmann (2014), as the fraction of individuals aged 15-25 convicted of a crime in a given year. As before, the estimation controls for juvenile crime, which is especially relevant in this subsection given the amplifying effects that growing up in a high crime neighborhood could have on an individual’s propensity to engage in juvenile crime. Table 11: Within Twin Fixed Effect Estimates of Sample of Same Gender Twins In Same Childhood Environments By Municipal Youth Conviction Rates (1) (2) (3) (4) (5) (6) Male Twins Female Twins Raised in a Municipality With Low Youth Conviction Rate Total Property Violent Total Property Violent Years of Education -0.0144∗∗ -0.0046 -0.0082∗∗ -0.0025 -0.0006 -0.0013 (0.0049) (0.0030) (0.0029) (0.0029) (0.0021) (0.0018) Number Individuals 2090 2090 2090 1966 1966 1966 Twin Pairs 1045 1045 1045 983 983 983 Raised in a Municipality With High Youth Conviction Rate Total Property Violent Total Property Violent Years of Education -0.0122∗∗ -0.0026 -0.0010 -0.0002 0.0001 -0.0002 (0.0039) (0.0024) (0.0020) (0.0016) (0.0011) (0.0005) Number Individuals 3948 3948 3948 3942 3942 3942 Twin Pairs 1974 1974 1974 1971 1971 1971 Standard errors clustered at twin level reported in parentheses. **, *, and + correspond to significance at the 1% 5% and 10% levels respectively. High juvenile conviction: residing in a municipality at age 15 where the youth conviction rate is higher than the rate of the median municipality in that year. Low juvenile conviction: residing in a municipality at age 15 where the young conviction rate is equal to or lower than the rate of the median municipality in that year. For males, the estimated effects of education on total crimes presented in Table 11 are relatively similar irrespective of growing up in a high or low crime municipality. While the effects, in percentage point terms, are greater for those raised in a low crime municipality, they are very similar to those raised in a high crime municipality. Education appears to only reduce violent crime for individual’s raised in low crime areas, with negative, but insignificant effects seen for those in a high crime area. For property crimes, negative but insignificant effects of education are seen for both groups. For females, the effects of education on crime are greater for those raised in a low crime municipality, but are never significant at conventional levels for either low or high crime neighborhoods. With the exception of violent crimes, environmental factors, measured as being raised in a high or low crime neighborhood, appear to lead to minimal differences in terms of the crime reducing capabilities of education. 48 8.3 Differential Margins of Education As discussed previously, one advantage of using within twin estimation to identify causal effects of education on crime is that, unlike a change in compulsory schooling laws, multiple margins of education can be investigated. Despite the many studies on the effects of education, little emphasis has been placed on how these effects differ across an individual’s specific program of education. One exception is Åslund et al. (2015), who find that an expansion of vocational upper secondary education from two to three years lowered property crimes in Sweden. Their findings support the role of incapacitation effects, with the crime reduction largely attributable to the introduction of the additional third year in vocational education. This supports the idea that both vocational and non-vocational education can be expected to reduce criminal propensity. In this section, qualifications are divided by vocational training and non-vocational education to correspond to the Danish education system. In Denmark during the time period examined, once students complete compulsory schooling of 9 years, they then can either progress directly to high school or attend an optional 10th grade and then proceed to high school. There are three different types of high school students can attend in Denmark: regular, business (Højere Handelseksamen), and technical (Højere Teknisk Eksamen) high school. In addition to this, students can attend vocational training directly after compulsory schooling, which is similar to apprenticeship programs and geared not towards attending higher education, but rather professional employment. For simplicity, education of 9 or 10 years is referred to as lower secondary education, such that individuals can either attend high school or vocational training following lower secondary education. Table 12 reports the effect of completion of three different types of education on crime: (i) completing any high school from lower secondary education, (ii) completing any university education from any high school, (iii) completing vocational training from lower secondary education. Results reported in Table 12 are constructed in such a way that the sample is restricted to twin pairs where both twins are in one of the two educational groups analyzed. For example, the results in the top row compare the criminal participation of one twin who has only completed lower secondary education to a twin who has completed any high school. While in principle the three types of high school could also be separately analyzed, it is necessary to combine all types of high school into one qualification in order to ensure there are an adequate number of twins in each educational group. It is worth noting that for some qualifications, the effects are being driven by a small number of twins who make up a small percentage of the population. 49 Table 12: Differential Margins of Education by Type of Education Program (1) (2) (3) (4) (5) (6) Male Twins Female Twins Regular (Non-Vocational) Education Completing HS from Lower Secondary Education Total Property Violent Total Property Violent Completing HS -0.0993∗∗ -0.0473∗-0.0253+0.0273+0.0266+0.0072 (0.0331) (0.0225) (0.0142) (0.0144) (0.0144) (0.0072) Number Individuals 1748 1748 1748 1820 1820 1820 Twin Pairs 874 874 874 910 910 910 Completing Any University from HS Total Property Violent Total Property Violent Completing Any Univ. -0.0107 -0.0089 -0.0178 0.0056 0.0056 0.0056 (0.0181) (0.0089) (0.0125) (0.0097) (0.0056) (0.0056) Number Individuals 1144 1144 1144 1608 1608 1608 Twin Pairs 572 572 572 804 804 804 Vocational Training Completing Vocational Training from Lower Secondary Education Total Property Violent Total Property Violent Completing Voc. Training -0.0263 0.0002 -0.0117 -0.0104 -0.0036 -0.0095+ (0.0190) (0.0104) (0.0106) (0.0084) (0.0032) (0.0055) Number Individuals 3462 3462 3462 2940 2940 2940 Twin Pairs 1731 1731 1731 1470 1470 1470 Standard errors clustered at twin level reported in parentheses. **, *, and + correspond to significance at the 1%, 5%, and 10% levels respectively. Not reported are controls for juvenile crime. 50 Previous studies on education and crime have found that while the completion of high school (or an equivalent level) produces large crime reducing effects for males, attending university has little to no impact on crime participation (Lochner and Moretti 2004). Consistent with these expectations, for male twins, results on regular (non-vocational) eduction in Table 12 reveal the completion of high school leads to a 9.9 percentage point reduction in the probability of conviction for any crime, while the completion of any university has no significant effects either positive or negative. For female twins, completion of high school actually leads to a 2.7 percentage point increase in total and property crimes, an effect which is significant at the 10% level. Conversely, results using vocational training, reported in the bottom panel of Table 12, display a different trend. For male twins, additional vocational training past the compulsory schooling level appears to have no crime reducing benefits. For female twins, vocational education lowers the probability of conviction for total and violent crimes, where the effect on total crimes is insignificant. The lack of any crime reducing effect of vocational training for males is striking, especially when compared to the strong crime reducing effects of completing high school seen for males. As the lengths of normal high school and vocational training programs are very similar, the differences seen in Table 12 are not due to incapacitation effects.26 These differential effects by type of education could be driven by underlying differences between the students of both types of education, underlying differences between the two types of education, or by underlying differences in employment prospects between the two education groups. If, for example, students who attend vocational training are more prone to commit crime than students who attend regular education, then it could take longer for education to negatively impact an individual’s propensity to engage in criminal behavior. If this were the case, this could also be reinforced through peer effects while in school. An alternative explanation could be that the teaching and educational methods differ across the two types of education. If this were the case, student’s criminal propensity could develop differently across the two educational programs. Another possible explanation is that the completion of high school increases an individual’s probability of employment, but not for vocational training. If this were the case, then the crime reducing effects of employment caused by greater education would affect the two groups of students differently. However, as many vocational training programs are directly geared towards professional 26If anything, some vocational training programs can take longer than normal high school. In this case, the incapacitation effects of being involved in education for longer would lead to greater crime reducing effects of vocational training compared to normal high school, and the effects shown in Table 12 would actually underestimate the effects of completing high school compared to vocational training. 51 employment, this seems a less plausible explanation. Whatever is driving the underlying differences in reduced criminality between these two types of education, the results displayed in Table 12 demonstrate the importance to crime reduction not only of an individual’s educational qualifications, but also of an individual’s educational program. 8.4 Detailed Crime Types Estimation using all available crime categories that comprise total crime for male same household twin pairs is reported in Table A2 in Appendix D. Results are directly comparable to even columns of Table 8, which include juvenile crime controls. For more uncommon crimes, the effects are being driven by a small amount of male twins who make up a small percentage of the population. Taking this into account, estimated effects of education are generally negative across crime types, but with fluctuating significance. The results of Table A2 reveal large crime reducing effects of education on traffic related alcohol crimes, where a ceteris paribus year increase in education lowers the probability of conviction by 0.7 percentage points (20%). Large negative effects are also seen for firearms and sexual crimes, where a ceteris paribus year increase in education leads to a 0.2 percentage point (32%) and 0.1 percentage point (44%) reduction in the probability of conviction respectively, where the effect for sexual crimes is significant at the 10% level. Education also negatively affects participation in other crimes for male twins, an effect which is significant at the 10% level.27 Table A2 reveals that, for males, education can not only reduce participation in violent and total crimes, but in most other crime types as well. 9 Robustness Checks Having detailed heterogeneous effects by parental education and across educational program, the results below not only investigate the robustness of the main specification but also investigate the validity of the identifying assumptions required for within twin fixed effects. 9.1 Using Incarceration as a Dependent Variable Table 13 uses, as a dependent variable, whether an individual has spent time in jail resulting from an offense committed from 2001-2006. Results in the columns are divided by gender and not crime 27The three most common crimes in the definition of other crimes are false accusations, the sale of drugs (those that are not covered by the law on narcotics), and crimes against public authority. 52 type, where column (1) shows results for only male twin pairs and column (2) shows results for only female twin pairs. While being convicted of a crime corresponds to criminal activity, individuals who are ultimately incarcerated usually commit more severe crimes, and as incarceration is costly to society, it is worthwhile examining both convictions and incarcerations. As such, incarceration data is used to not only determine whether the negative effects seen using conviction data are robust to an alternative measure of criminal activity but also whether education can effectively reduce incarcerations. If the effects of education on crime are robust to changes in the crime measure used, this supports the argument that education truly reduces an individual’s propensity to engage in crime. Table 13: Within Twin Fixed Effect Estimates of Sample of Same Gender Twins In Same Childhood Environments using Incarceration (1) (2) Male Twins Female Twins Incarcerated Incarcerated Years of Education -0.0035∗-0.0001 (0.0014) (0.0006) Juvenile Crime 15 0.0517+0.0000 (0.0272) (0.0001) Juvenile Crime 16 0.0203 -0.0001 (0.0195) (0.0004) Number Individuals 6038 5908 Twin Pairs 3019 2954 Standard errors reported in parentheses. **, *, and + correspond to significance at the 1%, 5%, and 10% levels respectively. As before, years of education significantly lowers the probability of being incarcerated for male twin pairs, but not for female twin pairs. For male twin pairs, a ceteris paribus year of education lowers the probability of incarceration by 0.4 percentage points (22%). For female twin pairs, education appears to have no significant negative effects on the probability of incarceration. As with estimation using convictions, having been convicted of a crime committed as a juvenile increases the probability of incarceration, by roughly 2-5 percentage points depending on the age an individual engaged in juvenile crime, but there still remain significant negative effects of education on incarceration. The results in Table 13 lead to the conclusion that education has a larger, in terms of percentage of mean reduction, impact on an individual’s probability of incarceration than 53 on their probability of conviction, a finding which is also seen in other papers using Scandinavian data (Hjalmarsson et al. 2015). This is indicative that education not only decreases an individual’s probability of committing crime, but also has additional effects on reducing the severity of crimes committed, as these crimes usually correspond to jail sentences. 9.2 Accounting for role of DZ Twins in Estimation Following Holmlund et al. (2008), under certain assumptions and exploiting knowledge of the fraction of same gender DZ twins out of all same gender twins in the population (θ), the potential bias introduced by the presence of DZ twins in the estimation sample can be corrected for, even if zygosity of the individual twins is unknown. Making use of non-twin siblings (with both the same mother and father) to approximate the effect for DZ twins and under certain assumptions, the same gendered twin estimate, a composite of both MZ and DZ twins, can be decomposed into an average of the effect for MZ twins and the effect of DZ twins. This requires assuming that the education and crime equation, equation (1), is the same for same gender DZ twins and non-twin siblings, that DZ twins and non-twin siblings are treated the same, and there is no measurement error in schooling.28 In order to make these similarity assumptions more believable and, again, following Holmlund et al. (2008), only same gendered siblings who are born close to each other, defined here as within 2.5 years, are used.29 Some suggestive evidence of the extent to which these sibling populations are similar is presented in Björklund and Jäntti (2012), who examine sibling correlations for years of education, earnings, IQ, and non-cognitive skills. The authors explore a wide variety of siblings, including twin siblings, and show that DZ twins and closely spaced siblings (which they define as those with less than 4 years of age difference) have similar sibling correlations in education. While the DZ correlations are more imprecise, they also show that the sibling correlations for closely spaced siblings are more similar to DZ twins compared to non-closely spaced siblings (those with 4 or more years of age differences). As siblings with age differences of exactly 2.5 years are used in this paper, the similarity of same gender DZ twins and closely spaced siblings is, presumably, even more believable. 28As the quality of Register data is regarded as high, particularly with education, it seems realistic to assume measurement error in schooling is unproblematic. 29Closely spaced siblings are those born within exactly 912 days of each other. Results are robust to altering this somewhat arbitrary cutoff. 54 Under the above assumptions, the MZ twin estimate is calculated as: ˆ βMZ =1 θˆ βMZDZ −ˆ βCS where ˆ βMZDZ is the estimate for both same gendered MZ and DZ twins which has been estimated previously and ˆ βCS is the estimate for close siblings which represents the estimate for same gendered DZ twins had zygosity been observable. θis taken as 0.509 from Skytthe et al. (2011), who report among twins born from 1968-1982, 2,788 are MZ and 2,887 are same gender DZ. Standard errors are estimated as in Conley et al. (2006); Conley and Strully (2012), and require the additional assumption that the covariance between the same gender twin estimates and the close sibling estimates is zero, cov(βMZDZ, βCS)=0. This is a fairly strong assumption, which is equivalent to assuming that the error terms for same gendered twins and closely spaced siblings are unrelated.30 While this assumption is necessary in order to calculate any standard errors, the standard errors resulting from this method should be interpreted with some degree of caution. Results presented in Table 14 show that if it were possible to identify zygosity, the estimated effects of education on crime would be of a similar magnitude for MZ twins alone than in the same gender twin sample. For males, the effects of education on total convictions for all same gendered, same household males and for those with low parental education remain negative, sizable, and statistically significant. For estimation using incarceration as a dependent variable, while the estimated effects of education on crime become insignificant, the imputed MZ coefficient shows an effect which is similar in terms of magnitude, only less precisely estimated. Table 14 suggests that if zygosity were observable, a MZ twin sample would produce estimated effects of education on crime in a similar range as the effects from the same gendered twin sample used throughout the paper. 9.3 Examining Differences in GPA As discussed in Section 6, underlying differences in the ability levels of twins will violate the identifying assumptions required for within twin estimation. Sandewall et al. (2014) investigate the possibility of this using IQ scores and birth weight. While both IQ scores and birth weight are unavailable for the sample of twins used in this paper, for a subsample of twins, average GPA 30To the extent there could be positive covariance between same gendered twins and closely spaced siblings estimates, if these are biased in the same direction, this would lead to standard errors which are too large. For a further discussion of this method and its shortcomings, see Conley et al. (2006). 55 reduced criminality but perhaps something particular in the use of conviction data. Similar effects of education on crime are found when excluding twins with large differences in education, limiting concerns that the findings are driven by a few potentially outlying twins. Direct estimation of the reverse causality between education and crime reveals that while juvenile crime does lead to lower educational attainment as a youth, the effects are much smaller than has previously been found, and are not large enough to explain the entire relationship seen between education and adult crime. While on the whole, the estimated effects of education on crime using Danish twin data are in line with previous research, this paper improves on existing studies, which predominantly examine changes in compulsory schooling laws, by estimating heterogeneous effects of education on crime which are representative of the entire population while, at the same time, netting out inherent common factors between twins which is crucial to identifying causal effects of education on crime. One obvious concern is that the twins analyzed are unique and not representative of the general population. However, OLS results for twins are comparable not only to the non-twin sibling population, but also to the entire non-twin Danish population as well.34 This is indicative that the effects of education on crime found are representative at least of the Danish population. From a policy perspective, the findings of this paper reveal not only the overall importance of education in terms of crime reduction, particularly for the completion of high school, but also the importance of family background in the crime reducing capabilities of education. For children of low educated parents, it appears to be extremely beneficial to motivate additional schooling as for these individuals, levels of education obtained can be less than is socially optimal. The high crime reduction from children of low educated families also highlights the importance of the intergenerational transmission of education, as while individuals from low educated families experience large crime reduction from additional education, they may be more likely follow in the educational footsteps of their parents and fail to benefit from the crime reducing capabilities of education. This may be of concern even in Nordic countries, where most intergenerational estimates find that an additional year of parental education increases the education of their children by around 0.1 years (Holmlund et al. 2011). Encouraging individuals from low educated families to remain in education, as well as to avoid engaging in juvenile crime, could offer an effective way to not only reduce longer term educational inequality but also reduce criminality on the whole. The 34Results available on request. 62 heterogeneous effects outlined reveal the importance of accounting for differences across individuals when estimating the crime reducing capabilities of education, and further research is required to identify precise mechanisms behind these differences. References Aizer, A. and J. J. Doyle (2015). Juvenile incarceration, human capital, and future crime: Evidence from randomly assigned judges. The Quarterly Journal of Economics 130(2), 759–803. Amin, V. (2011). 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Koning, S. Vujic, and N. Martin (2008). Why are criminals less educated than non-criminals? evidence from a cohort of young australian twins. CPB Discussion Paper 114, CPB Netherlands Bureau for Economic Policy Analysis. Webbink, D., P. Koning, S. Vujić, and N. G. Martin (2013). Why are criminals less educated than non-criminals? evidence from a cohort of young australian twins. Journal of Law, Economics, and Organization 29(1), 115–144. 65 Appendices A Data Sources and Explanation Danish Register Data is composed of various databases through administrative sources, which are interlinked by a consistent and unique personal identifier number. This enables Danish residents to be tracked over time and the various separate databases. There are separate databases for employment data, individual data, family data, education data, income data, and crime data. The crime data used throughout the paper is conviction data which is combined with data on charges to make use of the exact date the offense was committed on. In Denmark, crimes against penal code are: sexual crimes (comprised of incest, rape, heterosexual offenses, homosexual offenses, public indecency, and prostitution), property crimes (comprised of forgery, check forgery, arson, various degrees of burglary, theft from vehicles, theft of various vehicles, shoplifting, larceny, embezzlement, fraud, blackmail, robbery, handling stolen goods, tax evasion, malicious damage to property, and offenses against property), violent crimes (comprised of violent against public authorities, disturbance of public order, homicide, attempted homicide, varying degrees of assault, intentional bodily harm, offenses against life, and threats), as well as some offenses which are categorized as unknown and other. There are special laws against offenses such as narcotics, firearms, and tax crimes. 66 B Denmark from 2000-2006 While the time period from 2000-2006 is not a perfectly stable, it is relatively stable both in terms of unemployment and crime. There are no large or sudden increases or decreases during the period for the crime data, and while unemployment does fluctuate from 2002-2004, by 2006, the unemployment rate returns to its 2001 level. Results using other years, while not perfectly identical, give similar coefficients. First two figures are author’s own calculation, aggregating individual level data to the national level, while last figure uses labor force survey data available from http://statistikbanken.dk. Figure A1: Total Reported Crimes from 1997-2008 500000 520000 540000 560000 580000 600000 Total Number of Reported Crimes 1997 1998 1999 2000 2001 2002 2003 2004 2005 2006 2007 2008 Year Total Number of Reported Crimes from 1997-2008 Source: Author’s calculation using data provided by Statistics Denmark. 67 Figure A2: Total Charged Crimes from 1997-2008 140000 150000 160000 170000 180000 Total Number of Criminal Charges 1997 1998 1999 2000 2001 2002 2003 2004 2005 2006 2007 2008 Year Total Number of Charges from 1997-2008 Source: Author’s calculation using data provided by Statistics Denmark. 68 Figure A3: Quarterly Unemployment Rate from Labour Force Survey from 1997-2008 34567 Unemplyoment Rate 1997q1 1998q1 1999q1 2000q1 2001q1 2002q1 2003q1 2004q1 2005q1 2006q1 2007q1 2008q1 2009q1 Year Seasonally Adjusted Quarterly ILO Unemployment Rate Source: http://statistikbanken.dk, “AKU123: Seasonaly adjusted labour force status in percentage by employment status”. 69 C Within Twin Estimates by Detailed Parental Education Table A1: Within Twin Fixed Effect Estimates of Sample of Same Gender Twins In Same Childhood Environments By Educational Attainment of Parents (1) (2) (3) (4) (5) (6) Male Twins Female Twins Both Parents Low Educated Total Property Violent Total Property Violent Years of Education -0.0243∗∗ -0.0022 -0.0041 -0.0039 -0.0021 -0.0030 (0.0063) (0.0041) (0.0032) (0.0034) (0.0021) (0.0022) Number Individuals 1322 1322 1322 1304 1304 1304 Twin Pairs 661 661 661 652 652 652 Low Educated Mother, High Educated Father Total Property Violent Total Property Violent Years of Education -0.0149∗-0.0049 -0.0005 -0.0015 -0.0031 0.0000 (0.0065) (0.0034) (0.0025) (0.0040) (0.0038) (.) Number Individuals 1188 1188 1188 1072 1072 1072 Twin Pairs 594 594 594 536 536 536 High Educated Mother, Low Educated Father Total Property Violent Total Property Violent Years of Education -0.0216∗-0.0090 -0.0118∗0.0000 -0.0000 -0.0000 (0.0083) (0.0056) (0.0058) (.) (0.0000) (0.0000) Number Individuals 570 570 570 548 548 548 Twin Pairs 285 285 285 274 274 274 Standard errors clustered at twin level reported in parentheses. **, *, and + correspond to significance at the 1%, 5%, and 10% levels respectively. Not reported are controls for juvenile crime. 70 D Detailed Crime Types Results for all available crime categories are reported in Table A2. 71 1 Introduction In the last decade, Europe has experienced a “reversal of misfortunes”: as crime rates have reached historic lows in the U.S., Europe on the contrary currently experiences historically high crime rates (Buonanno et al. 2011). Crime, arrests, and convictions generate large social costs, and the determinants of crime have been the focus of existing literature (Benson & Zimmerman 2010, Freeman 1999). Descriptive statistics suggest that in the United States, the peak of crime of the early 1990s approximately matches to the peak of the U.S. unemployment rate in 1994, and a positive relationship between unemployment and crime also exists for Denmark. Gould et al. (2002) uses trade instruments to estimate that wage trends explain more than 50% of the variation in property crime in the U.S. over their sample period (1979–1997), and that the decline in the unemployment rate of non-college-educated men after 1993 contributed to the decline in crime rates. Lin (2008) uses union membership rates and a state’s industrial structure to estimate that a one percentage point increase in the unemployment rate leads to a 4 percent increase in property crime. Prior literature has indeed uncovered convincing causal estimates of the impact of unemployment on crime in a number of countries including Sweden (Öster & Agell 2007) and France (Fougère et al. 2009). However, prior literature relies on state or municipality level data. In particular, it is hard to pinpoint exactly what individual-level mechanism generates the stateor municipality-level relationship between unemployment and crime rates. This paper estimates the impact of mass layoffs on the individual probability of committing a criminal offense in Denmark. Focusing on Denmark allows us to use a detailed employer-employeeunemployment matched individual-level data set with crime information taken from police records. The data set includes information on convictions, broken down by crime type—property crime, violent crime, etc—as well as individual earnings, weeks of unemployment, age, marital status, family information, and the area of residence of the individual. We focus on displaced workers, i.e. male individuals that have been in employment for at least 3 years in the same firm and move into unemployment when the firm experiences a mass layoff event, i.e. loses a substantial fraction of its employees compared to peak employment in a five year window prior to the time period of analysis. If events that drive the firm’s business cycle are arguably independent of the individual dynamics of the employee’s criminal offenses, focusing on displaced workers during mass layoff 78 events is likely leading to more causal estimates of the impact of job loss on the probability to commit crime. This paper finds statistically and economically significant impacts of displacement on the probability of an offense leading to a conviction for total and property crimes. We find that although displaced workers are no more likely to commit crime at any point prior to displacement, displaced workers are substantially more likely to commit crime after displacement. Results are robust to the inclusion of individual fixed effects, controls for family factors, and municipality fixed effects. Results are also robust to alternative definitions for mass layoffs: either (i) changing the threshold (30 or 40%) decline in firm size below which a firm is labeled as experiencing a mass layoff, (ii) using mean firm employment as the reference point for the firm-size decline instead of peak employment (Jacobson et al. 1993), or (iii) identifying mass layoffs as large deviations from a firm-specific trend in employment, estimated using prior firm size changes in 1985-1989. Results are also robust to focusing on larger-sized firms, for which a given percentage decline in size is less likely to be driven by temporary changes in firm size. We examine a variety of individual and family factors to assess the potential mechanisms behind why displacement leads to increases in crime. We assess whether there exists an intergenerational impact of father’s job displacement on the criminality of their children. We see a small impact of father’s displacement on son’s criminality in the short-run which is, at best, marginally different from the criminality of sons of non-displaced fathers. We find effects of displacement on crime are concentrated for individuals with low education—those with less than high school education and, to a lesser extent, those with vocational training education. Those displaced with education to the university level or higher are no more likely to be convicted than non-displaced individuals following displacement. We show that those living without another adult, either those unmarried or living in a single adult household, are more likely to engage in crime than displaced workers who are living with another adult, while displaced individuals are likely to engage in crime irrespective of age or whether they have children. Displaced workers experience substantial short-run and permanent earnings losses and spend longer in unemployment after the displacement event. While earnings losses and unemployment spells may explain part of the impact of displacement on crime, results suggest that our estimates are an effect of displacement on crime over and above what is explained by earnings losses but that time spent in unemployment can explain substantially more of the impact of displacement on crime. Given the generous unemployment system in Denmark 79 which may in part mitigate the role of earnings losses, this points to the fact that idleness may, at the very least, explain a portion of the impact of job displacement on crime. This paper makes contributions to two different literatures. First, the paper provides individuallevel estimates of the impact of job losses on crime using detailed employer-employee data. Previous literature (Gould et al. 2002, Öster & Agell 2007, Fougère et al. 2009) used regional-level data (such as county-level or state-level data) to estimate such impacts. Although the literature uses credible instrumental variable estimates, individual-level evidence of a mechanism relating unemployment and crime remains to be established. In particular, no U.S. data set matches individuals with their employers and includes crime data. Focusing on Denmark allows such analysis. Focusing on individual level data for Denmark provides estimates of a different relevance as compared to U.S. aggregate estimates. Individual-level estimates document the individual-level mechanism that may explain the aggregate level results: in particular a discrepancy between individual-level estimates and area-level estimates suggests either that regional level estimates are confounded or that there are social interactions in crime within states or municipalities: as unemployment rises, both individual incentives and social incentives to commit crime increase (Glaeser et al. 1996), and area-level estimates may be larger than individual level estimates. On the other hand, Denmark differs from the U.S. in significant respects. First, unemployment benefits and social benefits are significantly more generous in Denmark than in the U.S. Second, this paper focuses on the impact of job displacement on offenses leading to a conviction. Per capita incarceration rates are significantly lower in Denmark than in the U.S., and given the vast institutional differences in crime between the two countries, results presented in this paper are arguably a lower bound compared to what would be expected if similar data were available in the U.S. The paper also makes a contribution to the literature on the wider impacts of job displacement, which has documented the impact of job displacement on earnings (Jacobson et al. 1993, Couch & Placzek 2010), health (Eliason & Storrie 2009, Sullivan & von Wachter 2009, Browning & Heinesen 2012, Black et al. 2012), and mobility (Huttunen et al. 2015). Jacobson et al. (1993) documented the short-run and long-run earnings losses of displaced workers using U.S. Social Security data. Sullivan & von Wachter (2009) present evidence that job displacement leads to higher mortality rates. In this paper, we present results defining displacement in a similar way as in Jacobson et al. (1993) and Sullivan & von Wachter (2009), but we also use declines relative to a firm-specific trend in employment to identify large and sudden changes in firm size. 80 Results should be useful to policymakers: by establishing a link between individual-level displacement and crime, a job separation is likely to impact other parties than the firm and the employee. Job displacement may thus lead to increased policing costs, and overall negative welfare externalities for the municipality. In Blanchard & Tirole (2008) framework, neither employers nor workers may fully internalize the social cost of the job separations, which justifies either additional taxation of employers and/or active labor market policies that incentivize or help unemployed individuals to go back to formal employment. The paper proceeds as follows. Section 2 presents the rich Danish employer-employee data set. Section 3 presents the identification challenges and the paper’s identification strategy. Section 4 describes our empirical findings for convictions by crime types. Section 5 examines the possibility of intergenerational impacts of displacement on children’s probability of engaging in crime. Section 6 provides estimates of the impact of displacement by education, while Section 7 examines heterogeneity within our baseline results and identifies which individuals are more likely to be affected by displacement in terms of increased criminality. Section 8 presents results controlling for potential confounding characteristics and estimates what share of the effect of displacement on crime is mediated by the effect of displacement on earnings and unemployment, while Section 9 tests whether results are robust to alternative definitions for mass layoff and displacement. Section 10 concludes. 2 Data Set To analyze the impact of job displacement on crime, we utilize detailed employer and employee data contained in Danish Register Data made available by Statistics Denmark. Danish Register Data is a database of every individual residing in Denmark from 1980-present which is collected from various governmental and administrative sources. We follow individuals over time and across different data sources via an anonymous personal identification number derived from the central personal register (CPR, Det Centrale Personregister), and are able to match individuals to their employer using a unique firm identification number. We focus solely on males as males are overwhelmingly those who commit crime. We construct an individual level panel of every male residing in Denmark from 1985-2000 by combining five different data registers. First, the Population Registers include demographic factors such as age, gender, municipality 81 of residence, and immigrant and marital status. Second, the Danish Student Register contains education data such as an individual’s exact educational qualification and educational institution as well as information of any ongoing schooling. Third, the employer-employee data comes from the Integrated Database for Labor Market Research (IDA, Integrerede Database for Arbejdsmarkedsforskning) and contains information on an individual’s employment as well as the universe of firms in Denmark in a given year. The employee data set provides information such as an individual’s employment status (recorded at the end of November), the number of weeks in the year an individual was unemployed, information on part time or full time status, salary earned in the job , and a workplace (plant) identification number as well as a firm identification number. The employer data contains variables such as the number of employees in a workplace and the number of workplaces in a firm. We use this information to construct a firm level dataset. We consider only an individual’s primary job, according to a criteria set by Statistics Denmark which follows the definitions of the International Labour Organization (ILO).1All of the employee and employer data contained in IDA is observed annually, as in the French (Abowd et al. 1999) and Pennsylvania (Sullivan & von Wachter 2009) employer-employee data sets. Fourth, welfare and unemployment insurance payments received are observed at weekly frequency in the Central Register of Labour Market Statistics (CRAM, Det Centrale Register for Arbejdsmarkedsstatistik). This paper’s data set thus includes annual measures of an individual’s unemployment status by pointing out in which week of the year the individual goes from receiving no benefits to receiving some form of benefits.2As we match individuals to their firm, we know exactly when employees transition in and out of employment with that specific firm. Finally, crime data comes directly from the Central Police Register, and is available for charges (individuals charged by the police with a crime), convictions, as well as incarcerations. After a crime is reported, if the police suspect someone of committing this crime, this individual is formally charged with the crime. The criminal record then includes the date of the offense and the date charges were filed. After this, we observe whether and when the individual was tried for the crime, and the trial’s conviction outcome. The outcome can be either incarceration, a suspended sentence, a fine, a settlement, no charge/warning, or another, less frequent decision 1See www.dst.dk/kvalitetsdeklaration/848 for an explanation. 2In what follows, we use the terms receiving unemployment benefits and weeks of unemployment interchangeably. This could be problematic in that we would misclassify someone as non-displaced if they were displaced, but did not claim any benefits. Past studies have found this to be an unimportant factor, and this is particularly the case for us, as the high tenure individuals we identify are all eligible to receive social assistance or unemployment insurance (if they are a member) following job loss. 82 (for example a youth program or military punishment). While all of these are possible conviction outcomes, the overwhelming majority of convictions in Denmark result in either probation, a fine, or incarceration. In the estimation that follows we examine all types of convictions. A unique police case number links the criminal offense across the crime registers and the personal identification number links crimes to the specific offender’s in all other registers. The crime register also records the precise day charges were filed, convictions recorded, and incarceration started, which can then be compared to the week unemployment benefits started and the individual’s employment spell ended. Across all three crime databases, we also observe a detailed crime code, corresponding to the Danish classification system of offenses. Crimes are comprised of: sexual, violent, property, alcohol related traffic, narcotics, firearms, tax, unknown, and other crimes, as well as crimes against special legislation.3Within these large categories, the specific kind of offense is also recorded, i.e. burglary within property crimes, assault within violent crimes. Table 1 provides summary statistics for the individual level panel of males born from 1945-1960 residing in Denmark from 1985-2000 for our five different data sources. 3 Empirical Strategy A number of identification challenges make the identification of the effect of the loss of employment on crime difficult. In particular, individuals typically do not leave their firm for exogenous reasons. Individuals may choose to leave the labor force altogether, or choose to leave their current job and start an unemployment spell to look for a better match. Employers may also choose to separate from employees who are more likely to commit crime. If individuals leave their firm because of opportunities in the informal sector, OLS results will suggest a positive correlation between changes in employment status and the probability of crime. Such correlation will not likely reflect a causal relationship between employment loss and crime; indeed, current unobservables would drive both the probability of job loss and the probability of committing crime. The literature has identified a firm-level cause of job losses that should be arguably independent of the worker’s individual dynamics. In this paper, we focus on high-tenure workers whose firm experiences a mass layoff event, as in Jacobson et al. (1993). We focus on individuals born from 1945-1960 that are continuously employed in full-time work (30 hours a week or more) in the same firm who have at least 3 years of tenure in 1989. We also 3Excluding offenses such as traffic fines and accidents, which are also recorded in the police data. 83 Table 1: Impact of Displacement on Crime (1) (2) (3) Variable Mean SD Observations Annual Wage (2000 DKK) 238170 169906 8830448 Weeks Fully Unemployed 2.88 9.06 8830448 Firm size 4124.46 9860.5 7494777 Weeks on social assistance 27.1 17.05 150083 Weeks on UI benefits 16.77 15.02 1271574 Age 39.23 6.56 8830448 Birth Year 1952.27 4.67 8830448 Less than high school 27.23% 0.4452 8830448 High School 4.20% 0.2006 8830448 Vocational 44.33% 0.4968 8830448 University or beyond 22.75% 0.4192 8830448 Missing education 1.49% 0.121 8830448 Household income (2000 DKK) 484396 451135 8830448 Wage as fraction of HH Income 50.47% 29.97 8830448 Household size 2.89 1.35 8830448 Adults in Household 1.89 0.62 8830448 Number of children 1.05 1.14 8830448 Probability of charge 2.27% 14.89% 8830448 Number of charges 1.66 3.34 200391 Probability of conviction 1.91% 13.69% 8830448 Probability of conviction - Property 0.65% 8.06% 8830448 Probability of conviction - Violent 0.13% 3.67% 8830448 Probability of conviction - DUI 0.67% 8.14% 8830448 Number of convictions 2.26 5.89 168517 Probability of conviction to Prison 26.29% 44.02% 168517 Length of prison sentence (days) 2341.89 5844.60 44304 Sample: Danish males born from 1945-1960 who are continuously in Denmark from 1985-2000. Means and standard deviations from relevant variables from five different data sources are reported. 84 exclude individuals whose firm has fewer than 10 employees immediately prior to the displacement period in 1989 in order to exclude the possibility that small changes in the number of employees constitute a mass layoff event. In addition, we exclude any individual who is enrolled in education during the pre-displacement period, a first or second generation immigrant as residency may be tied to employment, or employed in a firm in 1989 which is publicly owned by the state or municipality as the definition of what a firm is for these employees is less obvious. Finally, we restrict our sample to those who are observable throughout our sample period from 1985-2000.4 Individuals identified by our sample construction with high-tenure are more likely to have accumulated firm-specific human capital, more likely to be enjoying a more favorable employeremployee specific match, and are thus more likely to face relatively worse outside options as compared to low-tenure workers. Such workers are also less likely to leave a firm during a mass layoff event.5The restrictions we put on the sample of workers ensure that those individuals we classify as displaced are high tenured workers with strong ties to their firms, for whom displacement is likely to be sudden and unexpected. In our detailed employer-employee dataset, an individual loses employment between year tand year t−1if the individual was in employment with their 1989 firm in year t−1and has at least one week of unemployment in year t.6In the data weeks of unemployment are identified such that a positive number of weeks of unemployment indicates that the worker either lost his employment or has transitioned back into employment with an unemployment spell in between positions. This paper’s data set excludes individuals that leave the workforce as (i) a majority of employees receive either unemployment benefits or social assistance and are counted as unemployed and thus (ii) individuals not in employment in year t are individuals that most likely separated from their firm voluntarily. A firm experiences a mass layoff event in year tif the firm experiences a decline in employment greater than 30% from that firm’s peak of employment from 1985-1989 (before the displacement period).7According to our definition of displacement, an individual is displaced only if they transition from employment into unemployment in a firm who experiences a mass layoff event, where displacement occurs somewhere between year t−1and t. 4Individuals can exist in the data in one year but not the following year either by emigrating from Denmark or through death. This sample restriction excludes a very small portion of individuals and relaxing this restriction does not alter our results. 5By focusing on high-tenure individuals, we are likely to get an underestimate of the impact of job losses on crime given the negative correlation between the probability of committing crime and job tenure. 6Appendix A presents a detailed discussion of the unemployment system in Denmark as well as the level and type of benefits available during unemployment. 7We also consider two alternative definitions of mass-layoff events in Section 9. 85 An individual is then displaced if he loses employment (following the above definition) from their 1989 employing firm during a firm-level mass layoff event, and we write Displacedit = 1. The sample focuses on mass layoffs that occur in the five years after our pre-displacement period such that an individual can be first displaced in 1990 and last displaced in 1994. We follow workers, both displaced and non-displaced, unconditionally in the post-displacement period from 1990-2000, such that our non-displaced sample is composed of individuals who remain in employment (either with the same firm or another firm), individuals who transition into unemployment in a non-mass layoff firm, individuals who transition into non-employment, and individuals who transition from full-time work into part-time work. This ensures we compare the criminal outcomes of high tenure displaced workers to the high tenure workers identified in our sample construction who are not displaced not only in the short run but also in the long run. Table A1 in Appendix B shows the structure of our final sample as well as the number of displaced individuals in each year of our displacement period, and the number of crimes committed in our final estimation sample. Within a firm that experiences a 30% or greater reduction in employment, individuals who lose employment may be specific individuals in observable and unobservable dimensions. Specifically, a firm and a set of employees may agree on voluntary layoffs. If such voluntary or selective layoffs affect workers that are more likely to commit crime, results correlating displacement events with criminal outcomes will be upward biased. Workers who are less productive, or whose nominal wage is high compared to the firm’s outside options, may be more likely to experience job separations. This is where the availability of a longitudinal dataset of individuals with wage and crime in every time period, with individual identifiers, allows us to control for an individual-specific fixed effect. For instance, childhood experiences, dimensions of educational achievement that are not controlled for, will be absorbed by the worker fixed effect. Individuals may also experience negative productivity shocks right before the firm’s mass layoff event, and thus be more likely to lose employment during that firm’s mass layoff event. For instance, the loss of a relative (Bennedsen et al. 2006), changes in marital status (Korenman & Neumark 1991), and other time-varying shocks have been shown to affect either worker pay or worker productivity. Such unobservable time-varying life events in the period from 1990-1994, that are correlated with worker productivity or pay and also with the propensity to commit crime, may confound the estimates of the impact of displacement on crime. To test for such possibility, we observe the criminal outcomes of individuals in all years prior to displacement and all years 86 after displacement. If displacement is truly exogenous to the individual’s prior unobservables – including propensity to commit crime – we should not observe that displaced individuals display a more crime-prone history before displacement than other workers. Another identification issue is that causality could flow from crime to job displacement if, for example, an individual is convicted of or incarcerated for a crime, an employer may separate from the worker as a result. Indeed, the timing of both the displacement event and criminal activity are crucial for our results to be interpreted as the effects of job displacement on crime. A criminal event – left-hand side of the regressions – is an offense that leads to a conviction. Because the dataset includes the date of the offense and a unique identifier for the charges that is linked to the judicial outcome and the sentencing, we trace each conviction back to the date of the corresponding offense.8In that way the data focuses only on severe offenses, i.e. with convictions, but avoids the problem of reverse causality that would occur if we defined a criminal event using the conviction date.9For instance, an individual could commit a crime prior to displacement, but, due to lags between when the offense is committed and being charged and convicted, may not ultimately be convicted until after displacement. Table A2 in Appendix C presents the typical time between when an offense is committed, is charged, is convicted, and is incarcerated for the overall population from 1985-2000 as well as our displaced sample. The lag between when the crime is committed and when an individual is finally convicted can be quite substantial. In this paper, Convictionit = 1 when an offense committed in year tresults in a conviction. Focusing on the offense date alleviates concerns that the conviction itself may be a driver of employment loss, as this would reveal itself in the dummies prior to displacement. Noting Convictionit such a criminal event (offense leading to a conviction), we estimate the full dynamics of criminal events preand post-displacement event. As such the main specification of this paper considers the regression of criminal events Crimei,t on the full set of dummy variables. The propensity to commit crime is modeled by the following equation: Convictionit =αi+ k=K X k=0 δk(Disp. in t −k) | {z } post-displacement + k=1 X k=K δ−k(Disp. in t +k) | {z } pre-displacement +τt+xitβ+εit (1) 8For a small percentage of crimes, date of offense is unobservable. For these crimes, date of conviction is used. Results are robust to dropping these crimes. 9While convictions corresponds to established guilt of a crime, estimation using charges instead of convictions produces relatively similar results which, if anything, are slightly larger in magnitude. 87 Table 3: Impact of Job Displacement on Crime (1) (2) (3) (4) Sons and Daughters Sons Total Property Total Property Year +7 0.0025 0.0032 0.0029 0.0040* (0.0026) (0.0022) (0.0024) (0.0021) Year +6 -0.0001 0.0004 -0.0010 0.0000 (0.0024) (0.0020) (0.0021) (0.0018) Year +5 -0.0007 -0.0009 -0.0023 -0.0025 (0.0024) (0.0019) (0.0021) (0.0016) Year +4 -0.0010 -0.0012 0.0001 -0.0005 (0.0022) (0.0018) (0.0021) (0.0016) Year +3 0.0025 0.0019 0.0019 0.0020 (0.0024) (0.0020) (0.0022) (0.0018) Year +2 0.0016 0.0003 0.0022 0.0009 (0.0025) (0.0020) (0.0023) (0.0018) Year +1 0.0042* 0.0025 0.0046** 0.0032* (0.0024) (0.0020) (0.0023) (0.0019) Displacement year 0.0020 0.0014 0.0014 0.0006 (0.0023) (0.0019) (0.0021) (0.0017) Year -1 Reference R20.191 0.168 0.200 0.178 Observations 1638016 1638016 Individuals 102376 102376 Crime is defined an offense leading to a conviction for children born from 1961 onwards who in 1989 reside in the same household as their father. Columns (1)-(2) use this measure of crime for both sons and daughters, columns (3)-(4) use this measure only for sons. Not reported are pre-displacement variables. Standard errors are clustered at the individual level. ***, **, and * correspond to significance at the 1%, 5%, and 10% levels respectively. 94 sory to grade 9.14 After compulsory education, individuals may decide to continue to high school (either directly after compulsory education or via an optional 10th grade) which is geared towards attending university, vocational training which is geared towards professional employment, or terminate education. Given the importance of educational attainment in determining an individual’s criminal propensity (Lochner & Moretti 2004, Machin et al. 2011, Hjalmarsson et al. 2015), all else equal, we would expect to see larger effects of displacement on crime for those with less education. Table 4 reveals that individuals with less than high school education experience sizable, significant, and long lasting effects of displacement on the probability of conviction for property crimes. Those displaced with vocational training education experience significant increases in crime compared to non-displaced individuals, but not as strong as the effects seen for those displaced with less than high school education. For individuals with university education, the estimated effects fluctuate between positive and negative, but never significantly different from zero. 7 Which Individuals Are Most Affected? In addition to education, we can examine what other factors (if any) predict whether displacement has an impact on crime. Table 5 investigates which types of individuals are most affected by the impact of job displacement on property crimes. While overall, we see large and long lasting effects of job displacement on property crimes, these effects, both in their magnitude and longevity, are likely to differ by family and socioeconomic factors. As with an individual’s education, we separate our estimation sample for predetermined levels of four potentially relevant variables in their 1989 values: age, whether displaced individuals have children, marital status, and single adult family. Ages are examined across two birth cohorts within our displaced sample, those born from 1945-1950 and those born from 1951-1960. The effects of age on offending are established to peak at late teens and early 20s, and declining over time. Thus it could be expected that the younger birth cohort may have larger effects of displacement on crime. Those who have any children in 1989 could be more responsible and less likely to offend in order to avoid the possibility of being apprehended and losing time spent with their children. On the other hand, it could be that those with children have a greater need for income in order to maintain their levels of expenditure prior to displacement, increasing the probability of committing crime. Those married and living with at least one other adult in 1989 are, similar to those with children, potentially less likely to offend to avoid the 14Recently a grade 0 became compulsory as well. 95 Table 4: Impact of Job Displacement on Crime by Educational Attainment (1) (2) (3) Less than High School Vocational Education University or Beyond Property Year +7 0.0051* 0.0042** 0.0026 (0.0029) (0.0020) (0.0032) Year +6 0.0057* 0.0017 0.0020 (0.0030) (0.0014) (0.0030) Year +5 0.0018 -0.0003 0.0020 (0.0022) (0.0009) (0.0030) Year +4 0.0051* 0.0044** 0.0075 (0.0029) (0.0019) (0.0049) Year +3 0.0036 0.0001 0.0047 (0.0028) (0.0011) (0.0040) Year +2 0.0057* -0.0000 0.0018 (0.0032) (0.0011) (0.0021) Year +1 0.0070** 0.0035* -0.0009 (0.0035) (0.0018) (0.0007) Displacement year 0.0097** 0.0019 -0.0008 (0.0039) (0.0015) (0.0007) Year -1 Reference R20.078 0.087 0.081 Observations 377024 896672 292256 Individuals 23564 56042 18266 Samples are defined taking an individual’s educational qualification in the pre-displacement period in 1989. Property crime is defined as committing a property offense which leads to a conviction. Not reported are pre-displacement variables. ***, **, and * correspond to significance at the 1%, 5%, and 10% levels respectively. 96 possibility of losing time spent with their spouse or fellow household members. Additionally, there is also the possibility both for those married and those living with another adult that income could be pooled over the household, and the impacts of job displacement on personal income could be less meaningful to financial stability. Estimation using whether a displaced individual lives with another adult takes into account the possibility that two individuals could be living together, but not be married. The impact of job displacement on property crime is presented in Table 5 by displaced individual’s age, whether they have children, whether they are married, and whether they live with other adults in columns (1)-(4) respectively. Within the separate birth cohorts, the estimated effects of job displacement on property crimes are positive and relatively similar irrespective of the displaced individual’s birth cohort. This suggests that displacement is such a negative and sizable shock to an employee that it is sufficient to push someone on the margin of committing crime to engaging in crime irrespective of their age. Examining the importance of having children reveals that job displacement impacts crime for both those with and without children in 1989. While it could be argued that having children of a young age, as opposed to children of any age, is what matters, the post-displacement effects on property crime are unchanged if children are defined not of any age, but those below the age of 18. The lack of differences by whether displaced individuals have children suggests that family factors may not necessarily predict the existence of effects of job displacement on crime. Where the estimated effects of displacement on crime differ is whether a displaced individual is married or living with another adult in 1989. There is a strong impact of job displacement on the crime participation of unmarried and those living with no other adults and while some effects are seen for those married or those living with at least one other adult, both the shortand long-run impacts of displacement on crime are much smaller in magnitude and, in most instances, not significantly different from zero. Job displacement appears to have meaningful and large impacts on crime, both in the shortand long-run, for individuals who are residing in a single adult household, suggesting the earnings potential of the household plays a role in mitigating the effects of job displacement on crime. 97 Table 5: Impact of Job Displacement on Crime for Relevant Samples (1) (2) (3) (4) (5) (6) (7) (8) Ages Children Married Adult in HH 1945-50 1951-60 Children No Children Married Unmarried Single Adult 2+ Adults Property Property Property Property Year +7 0.0024 0.0058** 0.0030* 0.0064** 0.0018 0.0075*** 0.0105** 0.0022 (0.0018) (0.0023) (0.0016) (0.0030) (0.0015) (0.0029) (0.0042) (0.0014) Year +6 0.0032* 0.0018 0.0024 0.0026 0.0014 0.0041* 0.0090** 0.0004 (0.0019) (0.0016) (0.0015) (0.0021) (0.0014) (0.0022) (0.0037) (0.0011) Year +5 0.0004 0.0009 -0.0003 0.0025 -0.0005 0.0023 0.0031 -0.0001 (0.0013) (0.0014) (0.0010) (0.0021) (0.0009) (0.0019) (0.0025) (0.0010) Year +4 0.0050** 0.0061*** 0.0042** 0.0083*** 0.0028* 0.0095*** 0.0100** 0.0042** (0.0022) (0.0023) (0.0017) (0.0032) (0.0016) (0.0030) (0.0040) (0.0016) Year +3 0.0013 0.0014 0.0009 0.0023 -0.0002 0.0037 0.0027 0.0009 (0.0016) (0.0016) (0.0013) (0.0021) (0.0011) (0.0022) (0.0025) (0.0012) Year +2 0.0005 0.0039* 0.0018 0.0031 0.0008 0.0043* 0.0038 0.0017 (0.0014) (0.0021) (0.0015) (0.0023) (0.0014) (0.0023) (0.0029) (0.0014) Year +1 0.0046** 0.0026 0.0033* 0.0041* 0.0014 0.0067** 0.0094** 0.0017 (0.0022) (0.0018) (0.0017) (0.0025) (0.0014) (0.0028) (0.0040) (0.0014) Displacement year 0.0027 0.0048** 0.0030* 0.0053** 0.0010 0.0076*** 0.0097** 0.0019 (0.0019) (0.0022) (0.0017) (0.0027) (0.0014) (0.0029) (0.0040) (0.0014) Year -1 Reference R20.091 0.087 0.091 0.084 0.083 0.094 0.093 0.087 Observations 720704 917312 1213872 424144 1105248 532768 269840 1368176 Individuals 45044 57332 75867 26509 69078 33298 16865 85511 Sample are defined over ages, the presence of children, marital status, and residing with another adult. For columns (3)-(8) these are measured using their values in the pre-displacement period in 1989. Property crime is defined as committing a property offense which leads to a conviction. Not reported are pre-displacement variables. Standard errors are clustered at the individual level. ***, **, and * correspond to significance at the 1%, 5%, and 10% levels respectively. 98 8 Controlling for Confounder Characteristics Figure A3 replicates the findings of Jacobson et al. (1993), i.e. estimates the impact of job displacement on annual earnings and on the number of weeks of unemployment. Jacobson et al.’s (1993) finding is that displaced workers will experience permanent earnings losses and long-term impacts on weeks of unemployment. Figure A3 presents results of the estimation of their specification on our Danish data. In particular the specification includes an individual fixed effect, year dummies, and the full set of preand post-displacement year-level dummies. Figure A3a is for annual salary in Danish Kroner, while Figure A3b is for weeks of unemployment. Figure A3a is similar to JLS’s finding that displaced workers experience permanent long-term earnings losses. In this paper’s analysis, the permanent loss 7 years after displacement is about 50,000 DKK, or 7,500 USD per year in 2015 dollars. Given the magnitude of such impacts of displacement on long-term earnings in the formal sector, opportunities in the informal sector—burglary, thefts, pilfering—may be become relatively more attractive; and thus the impact of displacement on earnings may explain the impact of displacement on crime. Tables 6 present estimates of the impact of displacement on offenses leading to a conviction for property crimes, controlling for a variety of family, geographic, and employment factors which were previously unaccounted for. The first column presents results including municipality fixed effects, while the next two columns present estimates conditional on whether a displaced individual has children and marital status in the current year. For example, as we do see an impact of job displacement on family dissolution, it is possible that job displacement impacts crime only, or partially, through its negative impacts on family structure. Likewise it could be that specific municipal factors could also affect an individual’s probability of engaging in crime and accounting for these may be important. However, the results of the three columns are virtually unchanged for property crimes, leading to the conclusion that neither family factors nor time-invariant municipality factors have much impact on the increase in crime due to displacement. The last two columns of Tables 6 present estimates of the impact of displacement on offenses leading to a conviction for property crimes, conditional on the individual’s unemployment weeks in the current year (column 4) and conditional on the individual’s annual salary in the current year (column 5). Given that lower earnings lead to increased probability of criminal offenses, and that there is a negative correlation between displacement and earnings, we should expect 99 Table 6: Controlling for Confounder Controls - Property (1) (2) (3) (4) (5) Municipality Effects Children Dummy Married Dummy Weeks Unemployed Annual Salary Property Crime Year +7 0.0042*** 0.0042*** 0.0042*** 0.0040*** 0.0040*** (0.0015) (0.0015) (0.0015) (0.0015) (0.0015) Year +6 0.0025** 0.0025** 0.0025** 0.0022* 0.0022* (0.0012) (0.0012) (0.0012) (0.0012) (0.0012) Year +5 0.0007 0.0006 0.0006 0.0002 0.0004 (0.0010) (0.0010) (0.0010) (0.0010) (0.0010) Year +4 0.0056*** 0.0056*** 0.0056*** 0.0049*** 0.0053*** (0.0016) (0.0016) (0.0016) (0.0016) (0.0016) Year +3 0.0014 0.0014 0.0013 0.0005 0.0010 (0.0011) (0.0011) (0.0011) (0.0011) (0.0011) Year +2 0.0022* 0.0022* 0.0022* 0.0008 0.0018 (0.0012) (0.0012) (0.0012) (0.0012) (0.0012) Year +1 0.0036** 0.0036** 0.0036** 0.0014 0.0030** (0.0014) (0.0014) (0.0014) (0.0014) (0.0014) Displacement year 0.0038*** 0.0038*** 0.0038*** 0.0021 0.0034** (0.0014) (0.0014) (0.0014) (0.0015) (0.0014) Year -1 Reference Control -0.0003* -0.0004*** 0.0001*** -0.00056*** (0.0002) (0.0001) (0.0000) (0.0000) Municipality FEs Yes No No No No R20.089 0.089 0.089 0.089 0.089 Observations 1638016 1638016 1638016 1638016 1638016 Individuals 102376 102376 102376 102376 102376 Control corresponds to the estimate of the variable listed in the column heading. Annual salary is reported per 100,000DKK. Property crime is defined as committing a property offense which leads to a conviction. Not reported are pre-displacement variables. Standard errors are clustered at the individual level. ***, **, and * correspond to significance at the 1%, 5%, and 10% levels respectively. that the coefficient conditional on earnings will be smaller in magnitude. Contrary to this, the results controlling for earnings are relatively similar, although less precisely estimated, to the baseline results, despite the negative and significant effect of wages. Given that the generous unemployment benefits are available in Denmark, these benefits may diminish the role of lost salary in explaining the effects of job displacement on crime, as individuals still receive a base level of income. However, when controlling for weeks spent in unemployment, the effect of displacement on property crimes is reduced, where all post-displacement coefficients decline in magnitude. The positive and significant effect of weeks of unemployment as well as its impact on the effects of displacement on crime indicate that inactivity, more so than individual earnings losses, may play some role in the links between job displacement and crime. 100 9 Robustness of Baseline Findings The paper’s baseline results present estimates of the impact of job displacement on crime assuming that firms’ mass layoff events occur when the firm’s size is lower than 30% of its peak employment, measured between 1985 and 1989 in the pre-displacement period (Jacobson et al. 1993). We examine the robustness of our baseline findings re-estimating our displacement effects considering displaced workers from larger firms, an alternative threshold for a mass layoff event, and two alternative definitions for mass layoff events. 9.1 Changes in Firm-Size Threshold The paper’s baseline estimates of Table 2 present results considering firms with 10 or more employees. Firms in Denmark are of a typically smaller size than firms in the United States, and the threshold of 10 corresponds to firms in 72nd percentile of the distribution of firm size in 1989.15 However, one may argue that with only 10 workers, a mass layoff event may be caused by a temporary changes in firm size. We thus test the robustness of our results to restricting the data set to firms with 20 or more employees (87th percentile), 25 or more employees (90th), and 50 or more employees (95th) in 1989. Results are presented in columns (2)-(4) of Table 7 and overall show very similar effects of displacement on conviction. However, it is worth noting that marginally larger effects are seen for the samples with larger firms. One potential shortcoming in using displacement as an identification strategy is that while an individual’s job loss is unanticipated, their fellow co-workers in their potential network may also experience a similar employment shock. It could be, in the case of very large firms, that these mass layoff events will be sufficiently large to alter an individual’s potential network, in which case some of the effects we attribute to job displacement on crime could also be due to the effects of a change in one’s network on crime. However, given that these effects are only marginally larger in these robustness specifications, are well within the confidence intervals of the baseline findings, and that (in regressions unreported) excluding individuals in firms in the top 1 percentile of firm size in 1989 produces very similar results to the baseline estimation, this issue seems minor, but is worth taking into consideration. 15Excluding those firms which are a self-employed individual. 101 Table 7: Robustness (1) (2) (3) (4) (5) Baseline Estimation 20+ Employees 25+ Employees 50+ Employees 40% JLS Threshold Property Crime Year +7 0.0042*** 0.0049*** 0.0054*** 0.0061*** 0.0025* (0.0015) (0.0017) (0.0019) (0.0022) (0.0014) Year +6 0.0025** 0.0025* 0.0028** 0.0023 0.0023* (0.0012) (0.0013) (0.0014) (0.0015) (0.0014) Year +5 0.0007 -0.0001 0.0001 -0.0001 0.0012 (0.0010) (0.0009) (0.0010) (0.0011) (0.0012) Year +4 0.0056*** 0.0067*** 0.0068*** 0.0070*** 0.0048*** (0.0016) (0.0018) (0.0019) (0.0022) (0.0017) Year +3 0.0014 0.0017 0.0019 0.0023 0.0005 (0.0011) (0.0013) (0.0014) (0.0016) (0.0011) Year +2 0.0022* 0.0031** 0.0035** 0.0033* 0.0012 (0.0012) (0.0015) (0.0016) (0.0018) (0.0013) Year +1 0.0036** 0.0040** 0.0044** 0.0038** 0.0036** (0.0014) (0.0016) (0.0017) (0.0019) (0.0016) Displacement year 0.0038*** 0.0046*** 0.0046*** 0.0046** 0.0042** (0.0014) (0.0017) (0.0017) (0.0020) (0.0017) Year -1 Reference Year -2 -0.0001 0.0002 0.0003 0.0007 0.0001 (0.0008) (0.0009) (0.0010) (0.0012) (0.0009) Year -3 0.0001 0.0004 0.0006 0.0004 0.0004 (0.0008) (0.0009) (0.0010) (0.0011) (0.0009) Year -4 0.0002 0.0005 0.0006 0.0005 0.0005 (0.0008) (0.0009) (0.0009) (0.0011) (0.0009) Year -5 -0.0005 -0.0008 -0.0007 -0.0007 -0.0005 (0.0006) (0.0006) (0.0006) (0.0007) (0.0006) R20.089 0.090 0.089 0.087 0.089 Observations 1638016 1472016 1407120 1201344 1638016 Individuals 102376 92001 87945 75084 102376 Column (1) corresponds to baseline estimation for property crime. Property crime is defined as committing a property offense which leads to a conviction. Columns (2)-(4) alter the number of employees in 1989 restriction, column (5) increases the criteria for a mass-layoff event. Standard errors are clustered at the individual level. ***, **, and * correspond to significance at the 1%, 5%, and 10% levels respectively. 102 9.2 Increasing JLS Criteria Column (5) of Table 7 examines defining mass layoff events as a year when firm size is 40% lower than its peak from 1985-1989 compared to the baseline of reduction of 30%. Using a threshold of 40% should lead to less frequent mass layoff events and thus to more conservative estimates of the impact of displacement on crime.16 The estimated effects of displacement on property crime using the 40% threshold are similar in magnitude to the baseline estimation, with slightly less statistical significance in the long-run effects of job displacement on crime. 9.3 Alternative Definitions for Firm-Level Mass Layoff Additionally, Figure 1 examines two alternative definitions of the reference point used to define mass layoff: a year in which firm size is 30% below the firm’s average employment in 1985-89 rather than its peak employment and a year in which firm size is 30% below a predicted firm-specific trend in employment. Such a firm-specific trend in employment is constructed as follows. First, for each firm, a linear regression of firm size on years since 1985 is run, for years between 1985 and 1989: FirmSizejt =Constantj+Slopej(Y ear −1985)t, where j indexes firms. When the firm has increasing size, we set Slopej= 0 and use its average employment to keep only genuine declines in employment, such that the firm-specific trend is only used for firms with declining employment. Such linear trend is then used to predict firm size after 1989. By using this firm-specific trend, we exclude the possibility that a firm whose employment is in slow decline throughout the entire sample period could eventually be classified as a firm with a mass layoff event, if gradual declines in employment persisted over multiple years. Within such a framework, the firm experiences a mass layoff event if its size in year tfor t= 1990, ..., 1994 is 30% lower than its predicted size according to this linear extrapolation. These two alternative definitions should lead to more conservative estimates of job displacement on crime as using average levels of employment to calculate a mass layoff will understate mass layoff events for firms with increasing employment trends who then experience a sudden decline in employment during the displacement period. Despite this, Figure 1 shows that for all definitions of firm-level mass layoff events, the effects of job displacement on property crimes are positive and long lasting. While these results are overall similar to the results of the baseline estimation, these alternative definitions produce effects of displacement on property crimes which are smaller 16Indeed the total number of displaced individuals decreases by slightly more than 800 individuals. 103 Table A1: Structure of the Panel Dataset Year 1985 1986 1987 1988 1989 1990 1991 1992 1993 1994 1995 1996 1997 1998 1999 2000 Pre-Displacement Period Post-Displacement Period Displacement Years Observations Final panel 102,376 102,376 Displacement 0 0 0 0 0 647 710 623 660 321 0 0 0 0 0 0 Crime Property 122 95 78 86 89 114 155 216 226 216 189 136 157 154 135 86 Violent 39 26 26 30 24 36 28 25 40 43 34 35 30 27 27 23 Total 713 687 674 609 663 723 693 794 767 730 623 575 600 612 591 427 Reported are the final number of individuals in each year of the data, the sums of displacement for the displacement years, and the sums of crimes in each year for the estimation sample over the preand post-displacement periods. 110 C Time Between Charges, Convictions, and Incarcerations 111 Table A2: Timing of Judicial Process for Overall Sample and Displaced Sample Time from Offense to Charges (days) Time from Charges to Conviction (days) Time from Conviction to Prison (days) Mean Median P25 P75 Charges Mean Median P25 P75 Convictions Mean Median P25 P75 Prison Terms Sample: all of Denmark with at least one charge over sample period Total Crimes 78.1 1 0 44 2759322 136 94 43 180 1172128 170.6 124 47 229 213246 (42.5%) (18.2%) Sample: displaced individuals with at least one charge over sample period Total Crimes 81 0 0 18 922 129.9 89.6 52 151.4 646 203.2 166 106 236.8 117 (70.1%) (18.1%) Top panel reports the time between charges, convictions, and incarcerations for all individuals charged by the police from 1985-2000. Bottom panel reports the same times for individuals who are displaced at any point from 1990-1994 from 1985-2000. For confidentiality reasons, the 25th percentile, the median, and the 75th percentile are calculated using the average observations of the 5 individuals surrounding each statistic. 112 D Graphical Representation of Baseline Estimates Figure A1: Impact of Job Displacement on Probability of an Offense Leading to a Conviction (a) Total Crimes -0.002 -0.001 0 0.001 0.002 0.003 0.004 0.005 0.006 76543210-1-2-3-4-5 Displacement Effect Years Since Displacement (b) Property Crimes -0.002 -0.001 0 0.001 0.002 0.003 0.004 0.005 0.006 76543210-1-2-3-4-5 Displacement Effect Years Since Displacement Plots correspond to baseline estimates in Table 2 for total and property crimes. 113 E Detailed Property Crimes Figure A2: Detailed Property Crimes Committed by Displaced Individuals Post-Displacement Theft Fraud Other Forgery Vandalism Illegal Handling of Goods Auto Theft Percentages correspond to the fraction of specific offenses within the property crimes committed by displaced individuals following displacement. “Other” corresponds to arson, burglary, extortion, and embezzlement and is aggregated in order to comply with Statistics Denmark’s data confidentiality policies. 114 115 F The Impact of Job Displacement on Earnings Losses and Unemployment Figure A3: Impact of Job Displacement on Employment Outcomes (a) Impact of Displacement on Annual Salary -140000 -120000 -100000 -80000 -60000 -40000 -20000 0 20000 40000 76543210-1-2-3-4-5 Annual Salary (DKK) Years Since Displacement (b) Impact of Displacement on Weeks Unemployed -2 0 2 4 6 8 10 12 14 16 18 76543210-1-2-3-4-5 Weeks Unemployed Years Since Displacement Plotted are coefficients from estimation of preand post-displacement dummies on weeks unemployed and annual salary respectively. 116 Chapter 3 - Negative Attitudes, Network and Education 117 118 Negative Attitudes, Network and Education Patrick Bennett∗ , Lisbeth la Cour∗ , Birthe Larsen∗ , Gisela Waisman† March 2016 Abstract This paper assesses, both theoretically and empirically, the potential explanations behind the educational gap between young natives and immigrants using two measures, negative attitudes towards immigrants and networking. The paper considers the impact of negative attitudes and networking and that these parameters may influence high and uneducated workers as well as immigrants and natives differently, creating different incentives to acquire education for the two ethnic groups. Theoretically, this paper concludes that if all immigrants are equally affected by discrimination, immigrants obtain less education than natives while if only low-educated immigrants are affected by negative attitudes, immigrants obtain more education than natives to improve their employment prospects. Using rich Danish administrative data, this paper finds evidence consistent with this second case, that greater negative attitudes have a positive impact on male immigrants decision to acquire education and that networking can also increase immigrant education. We want to thank participants at the Search and Matching conference in Edinburgh 2014, the Workshop on Gender and Ethnic Differences in Market Outcomes, Aix-en-Provence 2014, the Copenhagen Education Network Seminar December 2014, School of Economics, Singapore Management University 2015. the RES conference 2015 in Manchester, the EEA conference 2015 in Mannheim, the WEAI conference in Singapore 2016, and Bochum University 2015, Kevin Lang, John Kennes, Pietro Garibaldi, Linas Tarasonis, Dario Pozzoli, and Anna Piil Damm. Finally, we want to thank Simon Backlund for excellent research assistance. ∗Department of Economics, Copenhagen Business School. †Regeringskansliet, Stockholm. 119 and the firm may be dissolved more often than matches for natives and also may differ for highand low-educated workers. This implies that, for given networking, the expected profitability of a firm employing natives may be different than the expected profitability of employing a highand/or low-educated immigrant. With identical firms, using equations (1)-(3) and Kuhn-Tucker conditions, we obtain the nontrivial solution in the steady state determining labour market tightness, θm i, i =N, I,m =h, l: kym q(θm N)=ym−wm N ρ+sN−λm Nq(θm N),kym q(θm I)=ym−wm I ρ+sN(1 + am)−λm Iq(θm I).(4) The partial equilibrium results are the following: more severe negative attitudes, a higher am, will tend to reduce labour market tightness and more networking, a higher λm i, will raise labour market tightness for the firm hiring the specific type, for either immigrants or natives. 2.3 The Worker Let Um ibe the value of being an unemployed worker and Em i, m =h, l, i =N, I be the value of being an employed worker. The values are determined by ρUm i=f(θm i)(Em i−Um i)−Γ(m)c(ei), i =N, I, m =h, l, (5) ρEm I=wm I+sm I(Um I−Em I)−Γ(m)c(ei), m =h, l (6) ρEm N=wm N+sN(Um N−Em N)−Γ(m)c(ei), m =h, l. (7) We assume that workers have different abilities, ei, and therefore different costs of obtaining education, c(ei). The variable eiis uniformly distributed, ei∈[0,1] where educational costs are decreasing in ability at a decreasing rate, c0(ei)<0, c00 (ei)>0. In order to guarantee a nontrivial solution where some, but not all, individuals choose to acquire education, the individual with the highest ability faces a very low cost of education, c(1) = 0, and the individual with the lowest ability level face very high costs of education, i.e. limei→0c(ei) = ∞.Γ(m), m =h, l, is an indicator function, taking the value zero if the worker does not acquire education and one, if the worker acquires education. Hence, Γ(h)=1and Γ(l)=0.5 5We assume that the educational cost is a cost to acquire and maintain education or skills. This is a simplifying 126 2.4 Wages We assume that wages are determined by Nash bargaining and that the bargaining power is a half, so that Xm i=Em i−Um i, i =N, I, m =h, l, where from equation (4) we have that Xm i= kym/(q(θm i)) = (ym−wm i)/(ρ+si−λm iq(θm i)). We assume that the hiring cost parameter, k, is equal across firms, but that productivity and therefore actual hiring costs are higher for firms employing educated workers. This gives that kym=Xm iq(θm i)and thereby Xm i=ym−wm i+λm ikym (ρ+sm i), m =h, l. (8) Subtracting equation (5) from equation (6) or (7) and then using Xm i=Em i−Um iand (8) give the wage equations wm N= 0.5·ym(1 + (λm N+θm N)k),(9) wm I= 0.5·ym(1 + (λm I+θm I)k).(10) We note that wages are increasing in labour market tightness, networking and productivity. Substituting for wages into the equation determining labour market tightness, we obtain the equations for labour market tightness (8) as a function of parameter values and independently of productivity as hiring costs are a function of productivity: k(ρ+sm I)2 = (1 −θm Ik+λm Ik)q(θm I),(11) k(ρ+sN)2 = (1 −θm Nk+λm Nk)q(θm N).(12) We note the following. Regarding relative separation rates we have that, if the separation rate of both high and low productivity immigrants is greater than the separation rate of natives sm I> sN, then the left hand side of (11) is larger than the left hand side of (12) tending to reduce labour market tightness for firms employing immigrants and thereby the transition rate for immigrants. Considering networking, labour market tightness is increasing in labour networking: dθm i/(dλm i) = kq(θm i)/Dm i>0, i =N, I, m =h, l, where Dm i=−((1 −θm ik+λm ik)q0(θm i)−θm ikq(θm i)) >0. If networking is higher for immigrants than natives, λm I> λm N, this tends to increase θm Irelatively assumption and is not important for the results. The assumption enables us to use a model without having workers continuously being born and dying. Such a model would deliver similar qualitative expressions. 127 to θm N. However, if sm I> sNthis tends to increase θm Nrelatively to θm I. Therefore, if there the separation rate is greater for immigrants than for natives, sm I> sN, and networking for natives is greater than or equal to networking for immigrants, λm I≤λm N, then the labour market tightness for natives is higher than labour market tightness for immigrants, θm I< θm N. If networking among immigrants is greater than networking among natives, λm I> λm N, and sm I> sNthen the relative size of labour market tightness is ambiguous. For the rest of the theoretical analysis we assume that educated and uneducated workers face the same networking effect, hence λh i=λl i=λi, i =N, I. With this assumption we obtain that labour market tightness is the same for high and low-educated natives, θh N=θl N=θNwhereas we have two scenarios for immigrants. In the first case, negative attitudes is present for both high and low productivity workers and hence sh I=sl I=sIresulting in θh I=θl I=θI. In the second case, negative attitudes exist for educated workers only and hence sN=sh I< sl Iresulting in θh I> θl I. This assumption allows us to consider the impact of a change in attitudes and immigration on labour market tightness, education and unemployment, without making any assumptions about the relative importance of networking for educated or uneducated workers. We will in Section 6 below discuss how the results are modified in the case of heterogeneous networking effects. We have the following result. Result: In case 1, where negative attitudes are present in both the high and low productivity sector, ah=al>0, and networking of natives is larger than or equal to networking of immigrants, λN≥λIthen labour market tightness for natives is higher than labour market tightness for immigrants, θN> θI, and natives’ wages are thus higher than immigrants’ wages, wm N> wm I. In case 2, when negative attitudes are present in the low productivity sector only, al> ah= 0, and networking of natives is larger than or equal to networking of immigrants, λN≥λI, then: (i) for low productivity workers, labour market tightness for natives is higher than labour market tightness facing immigrants, θl N> θl I, and low productivity natives’ wages are thus higher than low productivity immigrants’ wages, wl N> wl I, and (ii) for high productivity workers, labour market tightness and wages of natives and immigrants are equal, θh N=θh Iand wh N=wh I. When networking of natives is less than networking of immigrants, λN< λI, then the relative sizes of labour market tightness, θm Nand θm I,and wages, wm Nand wm I,for natives and immigrants are indeterminate. Note that given the assumption above that λI=tI and λN=t(1 −I), where 0<t<1we 128 have that λN> λIas long as I < 0.5, which is the most realistic case. In case the networking function takes another form, namely if it is increasing in the number of the worker’s own ethnicity but at a decreasing rate, for example, λI=tI1/2and λN=t(1 −I)1/2,we will still have that λN> λIas long as I < 0.5, but the impact of an additional labour force participant is larger for immigrants than natives as long as immigrants are the minority. 2.5 Education When individuals decide on whether to educate or not, they compare the value of acquiring education to the value of remaining uneducated. That is, at each point in time, as an unemployed worker, they compare the value of being unemployed as a educated worker to the value of being unemployed as an uneducated worker. Workers with high educational costs find it too costly to obtain education, whereas high ability workers and low educational costs individuals find it more than worthwhile to do so. The marginal worker has the ability level, ˆei, i =N, I, which makes the worker just indifferent between acquiring education or remaining uneducated. For simplicity, we assume that natives and immigrants are identical with respect to the distribution of educational costs. We write the condition determining the educational costs of the marginal worker as ρUh i(ˆei) = ρUl i, i =N, I. (13) The higher ˆeiis, the higher is the ability level of the marginal worker acquiring education. Hence, fewer workers acquire education, and a smaller fraction of the workers will be educated. Use equations (5)-(7) and (13), the bargaining condition together with the free entry condition, to obtain the following simplified condition in the first case where ah=alfor immigrants and a= 0 for natives: yh−ylθik=c(ˆei), i =N, I. (14) Equation (14) gives ˆei, i =N, I as a function of the endogenous labour market tightness variables, θi, i =N, I. The higher the productivity difference is, the higher are wage differences, and then the more people will acquire higher education. For equal networking rate, labour market tightness facing natives is higher than labour market tightness facing immigrants, which results in that natives acquire more education than immigrants, that is, ˆeI>ˆeN. In the second case, the result changes for immigrants whereas the natives’ educational decision 129 is still given by equation (14), i.e. when ah= 0 and al>0then we obtain: yhθh I−ylθl Ik=c( ˆeI).(15) In this case, with equal networking rate for all workers, we now obtain that ˆeN>ˆeIas low productivity immigrants are worse of than natives in terms of a lower transition rate into a job, θl I< θl Nand lower wages and high productivity immigrants have the same wages and employment probability as natives, θh I=θh N. Hence, due to that the uneducated immigrants are relative worse of than natives, immigrants in this case experience stronger incentives for acquiring education that natives. This is summarised in the following result. Result: In case 1, where negative attitudes are present in both the high and low productivity sector, ah=al>0, and networking of natives is equal to networking of immigrants, λN=λI, natives acquire more education than immigrants, that is, ˆeI>ˆeN. In case 2, where negative attitudes are present in the low productivity sector only, al> ah= 0, and networking of natives is equal to networking of immigrants, λN=λI, then immigrants acquire more education than natives ˆeI<ˆeN. Notice here the significance of the networking assumption. In section 6 below we discuss the impact of including heterogeneity and we discussed the nonproportionality of the networking function above. 2.6 Unemployment In equilibrium, inflows are equal to outflows. The equilibrium flows characterising the labour market for workers are then, f(θm i)µm i=sm inm i, i =N, I, m =h, l, and nh i+µh i= (1 −ˆei)i, i = N, I, nl i+µl i= ˆeii, i =N, I, where employment is nm i, i =N, I, m =h, l and unemployment is µm i, i =N, I, m =h, l. The labour force is normalised to one, N+I= 1, giving the following expression for natives’ unemployment rates: um N, m =h, l:uh N=ul N=uN=sN/(f(θN) + sN), as θh N=θl N. In the first case, we have the separation rate for high and low productivity immigrants is equal, sh I=sl I, and hence labour market tightness is equal, θh i=θl i, then unemployment rates are the following: uh i=ul i=ui=si f(θi) + si , i =N, I. (16) 130 Unemployment rates for educated workers are equal to unemployment rates of uneducated workers. This results stems from the assumption that hiring costs are proportional to productivity. In the second case, where the separation rate of low productivity immigrants is higher than that of high productivity immigrants, sh I< sl Ias ah= 0 and al>0, then sl I=sN(1 + al)> sh I=sN and thereforefθl I< f θh I=f(θN)which results in the following unemployment rates uN=uh I< ul I=sI fθl I+sI , i =N, I. (17) The result is the following. Result: In case 1, where negative attitudes are present in both the high and low productivity sector, ah=al>0, and networking of natives is larger than or equal to networking of immigrants, λN≥λI, the unemployment rate of natives is smaller than the unemployment rate of immigrants, uN< uI. In case 2, where negative attitudes are present in the low productivity sector only, al> ah= 0, and networking of natives is larger than or equal to networking of immigrants, λN≥λI, then the unemployment rate of low productivity immigrants is larger than that of high productivity immigrants and the unemployment rate of high productivity immigrants is greater than or equal to that of natives, ul I> uh I≥uN. When λN< λIthen the relative sizes of the unemployment rates facing natives and immigrants, uNand uIare indeterminate. 3 Negative Attitudes In this section, we examine what happens to labour market tightness, wages, education and unemployment when immigrants face more severe negative attitudes. For simplicity, we consider the case where λN=λI. The impact on labour market tightness, wages and unemployment as well as education will differ dependent on whether negative attitudes towards immigrants exists in both sectors or in the low productivity sector only. We have the following proposition. Proposition: In case 1 where negative attitudes are present for both high and low productivity workers, ah=al>0, then when negative attitudes increase, immigrants’ wages fall and their unemployment rates increase. Education of immigrants is also reduced. 131 In case 2, when only low productivity workers face negative attitudes, al> ah= 0, then wages for low productivity immigrants fall and their unemployment rate increases, whereas high productivity immigrants are not affected, increasing education for immigrants. There is no impact on natives. Proof: see Appendix A. In the first case, where ah=al=a, an increase in negative attitudes increases the separation of immigrants and therefore makes it less profitable to open a vacancy. The reduction in labour market tightness for immigrants reduces their bargaining power and thereby their wages. Immigrants’ transition rate falls which together with their higher separation rate increases their unemployment rate. Concerning educational choice, the impact depends on the impact on employment perspectives for high productivity workers relatively to the impact on low productivity workers. The reduced employment perspectives, through lower employment chances and lower wages, affect both high productivity and low productivity workers. However, due to higher productivity, the reduction in wages is going to be larger for high productivity workers than for low productivity workers and therefore the incentives to acquire education fall. The result is that fewer immigrants acquire education. As negative attitudes have no impact on the separation rate of natives, they are not affected. For the second case, that is, where al> ah= 0, an increase in negative attitudes only increases the separation of low productivity workers and only for the low productivity firms hiring immigrants, there is a reduction in the profitability of opening a vacancy. The resulting reduced labour market tightness for low productivity firms hiring immigrants increases uneducated immigrants’ unemployment rate. High productivity immigrants are not affected as their separation rate is not affected. When we turn to educational choice, the result changes compared to in case 1. The employment perspectives for high productivity workers are not affected and as the employment perspectives of low productivity workers worsens, and the incentives to acquire education increase. In this case, we therefore obtain the opposite result compared to in case 1, namely that more immigrants acquire education. Again, as negative attitudes have no impact on the separation rate of natives, they are not affected. As a caveat, notice, that we could allow for the possibility that negative attitudes affect the value of being unemployed also directly, and not only indirectly through wages and employment chances. In this case, the impact on unemployment will not be affected, but if, in case 1, negative 132 attitudes directly diminish the value of being unemployment equally for uneducated and educated workers, then there is no impact on education. In case 2, the direct impact will also, as the indirect through employment and wages, tend to increase education. 4 Immigration In this section, we examine the impact on labour market tightness, wages, education and unemployment from more immigration. Notice that λI=tI and λN=tN =t(1 −I). The impact on labour market tightness, wages and unemployment as well as education will differ dependent on whether negative attitudes towards immigrants exists in both sectors or in the low productivity sector only. We have the following proposition. Proposition: When the fraction of immigrants increases, the unemployment rate of immigrants falls and their wages increase. The improved labour market prospects of immigrants raise their level of education in both case 1 and case 2 and the opposite holds for natives. Proof: see Appendix A. More immigrants will induce the fraction of immigrants to increase, improving networking and thus labour market tightness for firms hiring immigrants and therefore immigrants’ transition rate. Similarly, networking among natives fall, and thereby labour market tightness for natives falls. As networking both directly and indirectly has a positive impact on immigrants’ wages, their wages increase whereas natives’ wages fall. Furthermore, the increase in immigrant’s transition rate reduces their unemployment rate and the corresponding reduction in natives’ transition rate raise their unemployment rate. Finally, concerning education for immigrants, improved labour market conditions due to more networking are better for high productivity workers than low productivity workers, wherefore education increases. As an illustration, consider the situation where a= 0 and hence sI=sNand initially N=I. In this case, labour market tightness facing immigrants is equal to labour market tightness facing natives. The fraction of educated immigrants and natives are also identical, ˆeI= ˆeNand thereby c0(ˆeI) = c0(ˆeN). The increase in educated natives is therefore equal to the fall in the fraction of educated immigrants. However, a more realistic setup is where N > I so that θN> θIand thus ˆeI>ˆeN(the fraction of natives acquiring skills is higher than the fraction of immigrants acquiring skills). In this case, c(ˆeI)< c (ˆeN),and |c0(ˆeI)|> c0(ˆeN),the impact through the lower 133 educational costs will increase the impact on education. However, substituting from equation (11) and (12) we obtain that the positive impact of networking is smaller for immigrants than the negative impact from networking for the natives, |dθI/dI|< dθN/dI. Hence, given N > I initially, the impact from an increase in the number of immigrants on their educational level may be smaller or larger than the negative impact on the educational level facing natives. 5 Immigration and Negative Attitudes In this section we expand the model by allowing for the possibility that a higher fraction of immigrants aggravates negative attitudes, giving for case 1, sh I=sl I=sN(1 + a(I)) and for case 2, sh I=sNand sl I=sN(1 + a(I)). The idea is that more immigrants around increases the possibility of a multi-ethnic society, which for some people is a negative development. As results now in general becomes ambiguous we consider the special case where the matching function takes the form Xm I=pvm Ium Iand that a0(I)=1. The impact on natives is identical to the impacts above. Proposition: Natives are affected as above. For immigrants we have the following. In the first case, differentiating equations (11), including the matching function, Xm I=pvm Ium Iwith respect to Iwhere now a(I)we obtain dθI dI pa(I)=−k(sNa0(I)√θI−t) (k(ρ+sm I)/√θI+k).Substituting for the solution for labour market tightness we obtain the condition for a0(I) = 1 that dθI dI pa(I)Q0⇔zRI, where z=sN(2ρtk+sN(1−2tk))−t2k s2 Ntk .This implies that for case 1 we obtain dwm I dI pa(I)Q0and dˆeI dI pa(I)R 0⇔zRI,and that dum I dI pa(I)>0for z≥I. In the second case, we obtain where dal/dI = 1 that dθl I dI pal(I)=−ksN√θl I−t k(ρ+sl I)/√θl I+kand dθh I dI pal(I)=tk k(ρ+sl I)/√θl I+k>0.For wages we have dwl I dI pal(I)Q 0zRI , dwh I dI pal(I)>0,and education increases, dˆeI dI pal(I)<0and unemployment increases if dul I dI pa(I)>0for z≥I, and duh I dI pa(I)<0. The impact of immigration on labour market performance for immigrants now becomes ambiguous. The reason is that more immigration improves networking and thereby employment chances and wages, but at the same time, negative attitudes may become more severe which reduce labour market tightness again. In the first case, where ah=al=a(I)>0, the positive impact through networking on labour market tightness is more important than the negative impact through increased negative attitudes if the fraction of immigrants is sufficiently high. The condition for a positive sign for labour market tightness is dependent on the separation rate and the networking 134 effect, so that in this case, the separation rate has to be low, low s, relatively to the networking effect, high t. In the second case, ah= 0, al=a(I)>0,high productivity workers are not affected and low productivity workers are effected as in case 1, implying that education unambiguously increases, as the relative gain of acquiring education increases. 6 Heterogeneous Networking Effects In this section we allow the networking effects to differ for uneducated and educated workers as well as for natives and immigrants.6First, we consider the case where sm I> sN, m =h, l, which results in the left hand side of (11) being larger than the left hand side of (12) and therefore tends to reduce labour market tightness for firms employing immigrants and thereby the transition rate for immigrants. Therefore, when immigrants face more networking than natives, λm I> λm N,we cannot determine the relative size of θm Iand θm Nas this networking effect would tend to increase labour market tightness for immigrants relative to natives. For the rest of this section we therefore consider the case where networking for immigrants is lower than networking for natives, λm N> λm I, m =h, l. Regarding education, we now need to consider the more general equation, allowing labour market tightness to differ both for educated and uneducated natives as well as immigrants : yhθh i−ylθl ik=c(ˆei), i =N, I. (18) To begin with, we assume that networking is the same for educated and uneducated immigrants and consider first the case where λh N> λl N. In this case, educated natives are more efficient using the network and we obtain that θh N> θl N> θh I=θl I=θI,resulting in higher wages for educated native workers than uneducated native workers, (see equation (9)), who then in turn, as before, receive higher wages than immigrants (see equation (9) relative to (10) inserting for labour market tightness and networking). Furthermore, considering education, using equation (18) we obtain that a higher fraction of natives than immigrants acquire education, ˆeI>ˆeN, as yhθh I−ylθl I< yhθh N−ylθl Nif and only if ylθl N−θl I< yhθh N−θh Ias there is a larger gain involved for natives than immigrants acquiring education. If instead, uneducated native workers are better at networking than educated natives workers, 6As we do not allow networking effects to depend on the number of each educational type (as then labour market tightness would be a function of ˆei, i =N, I ) then this corresponds to assuming that tmis different for the two different educational types. 135 Figure 2: Municipal Fractions of Immigrants Residing in Municipality analysis, the last two concerns is partially addressed by the robustness check excluding those who have recently moved. However, this does not completely solve the unobservables problem, as the decision of staying and locating initially is also endogenous. As such, we investigate the importance of unobservables and examine the sensitivity of our results to the omitted variable bias problem using a procedure developed in Oster (2015) which tests the proportional importance of unobservables in relation to observables. In the macro-econometric analysis below, we address these concerns by exploiting the panel nature of our data and using a municipal fixed effects specification. We employ data from 1999 in order to account for any unobservable time-invariant factors at the municipal level which affect our measure of high school attendance. Additionally, a dynamic panel data specification allows us to comment on the theoretical predictions of Sections 3 and 4, which examine changes in the values of negative attitudes and immigrants. 7.3 Macro-econometric Model and Analysis Table 1 presents descriptive statistics of the municipal data. While the total number of municipalities in Denmark during the time period is 275, we drop 27 municipalities as there were no 16 year old immigrants residing in them in either 2002 or 1999.10 This leaves us with 248 municipalities 10The municipalities we drop are: Hvalsø, Fuglebjerg, Gørlev, Høng, Holeby, Højreby, Ravnsborg, Rudbjerg, Egebjerg, Haarby, Langeskov, Marstal, Sydlangeland, Tommerup, Tranekær, Aarup, Gram, Blåvandshug, Hinnerup, Nørhald, Samsø, Fjends, Sallingsund, Læsø, Sejlflod, Sindal, Åbybro. 142 for our regressions. From Table 1, it is seen that the average share of 16 year old immigrants in high school is about 45.8% while it is larger for natives, 74%. Table 1: Summary Statistics at the Municipal Level (1) (2) (3) (4) (5) Mean Median Std Dev Min Max Immigrants Aged 16 in Any HS (%) 45.8% 50.0% 27.0 0.0% 100% Natives Aged 16 in Any HS (%) 74.0% 74.2% 5.9 54.9% 88.2% Votes Both Parties (%) 13.2% 13.0% 2.3 7.1% 21.0% Network for Immigrants (% of immigrants) 5.0% 3.9% 3.3 2.0% 25.2% ‘Network’ for Natives (% of natives) 95.0% 96.1% 3.3 74.8% 98.0% Western Immigrants Employed (%) 95.0% 95.5% 3.2 81.8% 100.0% Non Western Immigrants Employed (%) 89.1% 90.9% 9.0 27.3% 100.0% Natives Employed (%) 96.5% 96.8% 1.3 90.4% 98.5% Gross Income Per Capita/100000 1.732 1.677 0.195 1.448 2.771 Population Density/1000 0.285 0.073 0.846 0.021 10.413 LF Short Tertiary Education (%) 40.1% 40.2% 3.4 27.1% 50.3% LF Medium Tertiary Education (%) 10.7% 10.2% 2.8 6.3% 24.2% LF Long Tertiary Education (%) 3.2% 2.3% 2.9 0.7% 20.4% Observations 248 Our negative attitudes measure has an average value of 13.2%. The first network measure for immigrants (fraction of immigrants) is on average 5% and the two elements of the second network measure for immigrants (fraction of employed immigrants from Western and non-Western countries respectively) are on average 95% and 89.1%. It is not surprising that the employment ratio for Western immigrants is larger than for non-Western immigrants. The average (of average) gross income level per capita is 173200 DKK and the average population density is 285 people per square kilometre. Population density is included to account for the degree of urbanisation of a municipality. The average share of the population with a short, medium and long education are respectively 40.1%, 10.7% and 3.2%. When comparing the mean values and the median values of all variables we see that in some cases – especially for variables involving immigrants – the distributions are a bit skewed. As stated above, we want to disregard mobility taken by the individual due to different labour market conditions or attitudes. We therefore estimate the high school decision at the municipal 143 level using a fixed effects model: (1 −ˆert) = β0+β1art +β2λrt +X η βrtηControlsrtη +γt+cr+εr,(19) r= 1, ..., 266 t= 1999,2002. The left hand side variable, (1 −ˆert), is either the fraction of young 16 years old immigrants attending high school in year t(our main group of interest) or, for control purposes, the same fraction for natives in municipality r. Ideally, we would expect both the attitude and the network variables to be significant for immigrants while being insignificant for natives. We examine whether negative attitudes, art, and networking, λrt, have any impact on the fraction of young immigrants (16 year olds) attending high school. For networking, we consider two potential measures for λrt to assess whether the quantity of individuals or the quality of individuals matters: (1) the fraction of immigrants residing in a municipality (quantity) and (2) the fraction of immigrants residing in a municipality who are employed (quality). The inclusion of both year fixed effects (γt) and municipality fixed effects (cr) control for differences in the fraction of 16 year olds attending high school over time and for municipality specific time-invariant characteristics. As additional control variables, we include gross income per capita in the municipality, population density, and the percentage of the labour force (LF) with short, medium and long tertiary education. Table 2 presents estimation results of equation 19, where columns (1) and (2) use the fraction of natives/immigrants as a networking measure for natives and immigrants respectively, while columns (3) and (4) use the fraction of natives/immigrants employed for natives and immigrants respectively. Across all specifications, we find no significant effects of negative attitudes on the school choice for either immigrants or natives. For immigrants, these effects are positive, but never significant, while for natives, these effects are close to zero. This is contrary to the expectations of our theoretical model, which predicts a negative impact of negative attitudes on immigrant education in case 1 and a positive impact in case 2. For networking, the first measure indicates a negative and (marginally) significant effect for immigrants and natives, while using the fractions employed, arguably a better network in relation to our theoretical model, shows a marginally significant positive effect for immigrants and no effect for natives. The overall weak effects found may be due to the fixed effect estimation which uses variation within municipalities. However, as the fixed effect approach is necessary to best handle the potential endogeneity problem, the results 144 at the macro level fail to provide much insight into the predictions of our theoretical model. Table 2: High School Participation for Immigrants and Natives at the Municipal Level (1) (2) (3) (4) Frac Native Frac Imm Frac Native Frac Imm Enrolled HS Enrolled HS Enrolled HS Enrolled HS % Votes Both Parties -0.10 0.88 -0.10 0.74 (0.22) (0.87) (0.22) (0.87) % Native -2.44** (1.20) % Immigrants -14.42* (7.33) % Natives Employed -0.03 (0.65) % Western Imm Employed 0.57 (0.93) % Non Western Imm Employed 0.40* (0.23) Controls? Yes Yes Yes Yes R20.234 0.076 0.195 0.082 N 248 248 248 248 Robust standard errors are reported in parentheses. Negative attitudes are measured as the share of votes for the Fremskridtspartiet or Dansk Folkeparti. Not reported are controls for gross income per capita, population density, and the fraction of the labour force with short, medium, and long tertiary education. Vocational education is included in the short tertiary category. Medium education also includes bachelor degrees. An intercept is included in the model but not reported in the table. * p<0.10, ** p<0.05, *** p<0.01. The natural next step is therefore to further examine the possibility of a positive networking effect for immigrants when using the fraction of immigrants employed and the positive, but insignificant, effect of negative attitudes using micro data. Moving to the individual level enables many individual and family level factors to be taken into account which cannot be at the municipal level. We are also able to more precisely measure an individual’s potential network using information about their home country. Hence in the next subsection we model the educational choice of the individual young immigrants, and again natives for comparison, based on information about negative attitudes and networking possibilities in their municipality. 7.4 Micro-Econometric Model and Results Using individual level data on 16 year old individuals living in Denmark in 2002, Table 3 presents summary statistics of all relevant variables included in the estimation. As before we see that immigrants on average attend high school less than natives. Our negative attitudes measure has a similar average value as the macro section, 12.8%. 145 Table 3: Summary Statistics at the Individual Level (1) Votes Both Parties (%) 12.74% (2.41) Munc. Unemployment Rate (%) 5.21% (1.50) Munc. Population Density/1000 0.7098 (1.5072) Munc. Gross Income Per Cap/100000 1.7592 (0.20569) Native (%) 93.99% (23.77) 1st Generation Immigrant (%) 3.82% (19.18) 2nd Generation Immigrant (%) 2.19% (14.63) Natives Aged 16 in Any HS (%) 74.24% (0.00) Imm./Desc. Aged 16 in Any HS (%) 52.65% (0.00) Male (%) 51.06% (49.99) Mother’s Education 12.55 (2.92) Father’s Education 12.33 (3.04) Parents Married (%) 68.53% (0.46) Father Employed (%) 84.85% (35.86) Mother Employed (%) 82.99% (37.57) Household Income/100000 6.2022 (5.0702) High School in Municipality (%) 72.41% (44.7) Observations 53256 Mean values shown for 16 year old individuals residing in Denmark in 2002 unless otherwise indicated. Standard deviations in parentheses. We estimate the following equation separately for natives and immigrants: 146 (1 −ˆei) = β0+β1ar+β2λr+β3P arentEdup+ X µ βrµMuncControlsrµ +X η βiηHHControlsiη +Origini+εi,(20) where (1 −ˆei)is the educational decision of individual irepresented by a dummy variable if an individual is attending any high school or not, which is determined by: ar, negative attitudes captured by the fraction of votes for both Fremskridtspartiet and Dansk Folkeparti in municipality r;λr, potential networking of same nationality individuals residing the same municipality r;ParentEdup, the years of education of parent pwhere p=mother, father;MuncControlsr, municipal factors such as population density and the fraction of immigrants/natives unemployed which may affect an individuals education decision; HHControlsi, additional household controls such as parental employment status in December of the previous year, total household income, and parental marital status; Origini, origin country dummies that capture educational differences across specific immigrant home countries; and εi, residual unobservables which are clustered at the municipality level. As in the macro-econometric estimation, we use separate measures of networking in order to assess whether the quantity or quality of an individual’s potential network matters where for the former, networking is measured by the fraction of own nationality individuals residing in the same municipality rwhere for the latter, networking is measured by both the fraction of own nationality individuals residing same municipality rwho have (at least) a high school education and the fraction who are employed. As before, in order to identify the effects for immigrants, we separately estimate equations (20) for natives and for immigrants. In the micro section, we also consider the high school choice of both 1st and 2nd generation immigrants in one measure. We do so in order to explore how the effects of negative attitudes on education depend on an individual’s gender, as sample sizes when combining the two groups are sufficiently large.11 Tables 4 and 5 present results for males and females. Columns (1) and (2) present results for natives and immigrants respectively using only the municipal fraction of own nationality individuals as a measure of networking. Columns (3) and (4) use the detailed networking measures of educated and employed own nationality individuals. 11Section 8.3 provides a comparison of the high school choice of 1st and 2nd generation immigrants. 147 Table 4: High School Participation for Male 16 Year Olds by Immigrant Status (1) (2) (3) (4) Native - Any Immigrant - Any Native - Any Immigrant - Any HS Ongoing HS Ongoing HS Ongoing HS Ongoing % Votes Both Parties 0.063 1.483*** -0.028 1.275** (0.178) (0.568) (0.156) (0.551) Frac. of Own Nat. Educated -0.104 0.141 (0.093) (0.150) Frac. of Own Nat. Employed 0.087 0.468*** (0.179) (0.167) Frac of Own Nat. 0.092 -1.115 (0.150) (0.724) Mother’s Education 0.014*** 0.010*** 0.014*** 0.010*** (0.001) (0.003) (0.001) (0.003) Father’s Education 0.016*** 0.006* 0.016*** 0.006* (0.001) (0.003) (0.001) (0.003) Parents Married 0.064*** 0.113*** 0.064*** 0.113*** (0.007) (0.034) (0.007) (0.033) Father Employed 0.053*** 0.081*** 0.053*** 0.074*** (0.009) (0.028) (0.009) (0.028) Mother Employed 0.102*** 0.082*** 0.102*** 0.068** (0.009) (0.025) (0.009) (0.026) Household Income/100000 0.003** 0.014** 0.003** 0.012* (0.001) (0.006) (0.001) (0.006) % Natives Unemployed -0.304 -0.252 (0.277) (0.396) % Western Imm Unemployed -0.136 -0.050 (0.636) (0.625) % Non Western Imm Unemployed -0.032 0.094 (0.217) (0.211) Population Density/1000 -0.004 0.009* -0.004 0.007 (0.004) (0.006) (0.003) (0.005) High School in Municipality 0.016* 0.063 0.017** 0.036 (0.008) (0.039) (0.008) (0.038) Origin Country Dummies? No Yes No Yes R20.064 0.186 0.064 0.192 N 25526 1669 25526 1669 Standard errors reported in parentheses clustered at municipality level. Any HS Ongoing corresponds to either enrollment in regular high school, business high school, or vocational training programs (apprenticeships). * p<0.10, ** p<0.05, *** p<0.01. 148 Table 5: High School Participation for Female 16 Year Olds by Immigrant Status (1) (2) (3) (4) Native - Any Immigrant - Any Native - Any Immigrant - Any HS Ongoing HS Ongoing HS Ongoing HS Ongoing % Votes Both Parties 0.021 0.869 -0.373** 1.184** (0.226) (0.590) (0.173) (0.576) Frac. of Own Nat. Educated -0.368*** -0.101 (0.115) (0.174) Frac. of Own Nat. Employed 0.173 0.175 (0.207) (0.193) Frac of Own Nat. 0.501*** 1.824* (0.162) (1.029) Mother’s Education 0.014*** 0.010*** 0.014*** 0.010*** (0.001) (0.003) (0.001) (0.003) Father’s Education 0.014*** 0.007** 0.014*** 0.007** (0.001) (0.003) (0.001) (0.003) Parents Married 0.067*** 0.045 0.066*** 0.049 (0.008) (0.038) (0.008) (0.039) Father Employed 0.077*** 0.062** 0.076*** 0.061** (0.009) (0.025) (0.009) (0.025) Mother Employed 0.111*** 0.075*** 0.111*** 0.074*** (0.008) (0.026) (0.008) (0.027) Household Income/100000 0.006** -0.000 0.006** -0.000 (0.003) (0.007) (0.003) (0.007) % Natives Unemployed -0.839*** -0.829* (0.303) (0.433) % Western Imm Unemployed -1.351** -1.376** (0.589) (0.603) % Non Western Imm Unemployed 0.153 0.198 (0.221) (0.222) Population Density/1000 0.002 -0.000 -0.001 0.000 (0.003) (0.004) (0.003) (0.005) High School in Municipality 0.014 0.154*** 0.016* 0.159*** (0.009) (0.043) (0.009) (0.044) Origin Country Dummies? No Yes No Yes R20.081 0.235 0.081 0.233 N 24528 1533 24528 1533 Standard errors reported in parentheses are clustered at municipality level. Any HS Ongoing corresponds to either enrollment in regular high school, business high school, or vocational training programs (apprenticeships). * p<0.10, ** p<0.05, *** p<0.01. Examining males in Table 4, networking significantly increases the propensity of an immigrant to attend high school, where a one percentage point increase in the fraction of own nationality immigrants employed residing in the municipality would lead to a 0.47 percentage point increase in the probability of attending any high school. No equivalent significant effects are seen for natives, a finding which is consistent with networking amongst immigrants. The other networking variables, the fraction of own nationality individuals residing in the same municipality and the fraction of own nationality individuals with at least a high school education, are imprecisely estimated for both natives and immigrants. This is consistent with our theoretical model, where employment prospects 149 are key in determining the level of education an individual obtains, and it is reassuring that networking in terms of employed immigrants matters. The negative attitudes measure significantly increases an immigrant’s probability of attending high school, where a 1 percentage point increase in the fraction of votes for either political party significantly increases the probability of attending any high school by 1.3-1.5 percentage points, while no effects are seen for natives. For both natives and immigrants, household controls matter a lot for an individual’s propensity to attend high school, with education, employment, and marital status of both parents significantly increasing the probability of attending high school in all specifications. For females, in Table 5, a different picture is seen. While the fraction of own nationality immigrants leads to a significant and positive increase in the probability of attending high school for immigrants, there are no significant effects, either positive or negative, of the fraction of own nationality immigrants who are educated or employed. For natives, a significant positive effect is seen for the fraction of natives while a significant negative effect is seen for the fraction of natives with education to high school or beyond. For female immigrants, negative attitudes increase high school attendance, but is imprecisely estimated depending on which networking measure is used. For natives, a similar pattern emerges when networking is measured as the fraction of natives residing in a municipality. Similar to the male estimation, parental education, employment, and marital status significantly increase the probability of attending high school for both natives and immigrants. We find evidence that for males, negative attitudes towards immigrants increase the propensity of an immigrant to attend high school. For females, this effect is positive, but imprecisely estimated. For natives, no significant effects are seen for males nor for females. This is consistent with the macro-econometric analysis, which finds a positive, but insignificant, effect of negative attitudes on immigrant high school attendance. For male immigrants, networking seems to matter most in terms of employed immigrants of the same nationality, while for female immigrants, networking seems to matter in terms of the presence of any immigrants of the same nationality. The positive effect of negative attitudes on male immigrant education supports the second case of the theoretical model, where negative attitudes may have differential effects on immigrants propensity to attend high school depending on their productivity levels. In the case where high productivity workers are comparable to natives, as outlined in Section 3, negative attitudes only affect low productivity workers. This leads to lower employment perspectives for these low productivity workers, lowering 150 the future wages that young immigrants expect to receive and increasing the incentives of young immigrants to acquire education. 8 Robustness of Micro-econometric Results We examine the robustness of our micro-econometric analysis in the following subsections. In particular, we examine how the mobility of immigrants within Denmark affect the results obtained in Section 7.4, how sensitive our results on male immigrants are to the presence of unobservables, and how negative attitudes affect 1st generation immigrants compared to 2nd generation immigrants. 8.1 Exploring Mobility of Immigrants While the results presented in Section 7.4 are supportive of the second case of the theoretical model, it is possible our estimation fails to properly estimate the impact of negative attitudes on high school attendance. In particular, we focus on the educational decision of 16 year old individuals in order to disregard mobility concerns, as students of this age are likely to reside at home in this period. While this may be the case, it could be that parents either selectively locate to certain municipalities or move as a reaction to negative attitudes in a municipality. We examine the possibility that movers are driving the positive effect of negative attitudes we see for males in Appendix C by examining if our results are stable to restricting the sample to individuals who have resided in the same house for 3 or more years and 6 or more years. Similarly, we look at years since immigration for the non-native sample in order to see if recent immigrants, who could have selectively located within Denmark, are driving our results. On the whole, the results presented in Appendix C are very similar to the main results. For males, the negative attitude variable always increases the propensity to attend high school and is of a similar magnitude for immigrants, while there is no effect seen for natives. This is true for both the 3 or more years restriction as well as the 6 or more years restriction. For females, the effects of negative attitudes for immigrants is insignificant across specifications when imposing the years since moved restriction, which is consistent with the positive but imprecise effects seen in Table 5. The networking variables are less robust where, for males, the fraction of own nationality immigrants educated now matters while the fraction employed no longer does. For females, there are no effects of networking on the propensity to attend high school. A similar pattern is seen for estimation restricting the time since immigration for immigrants; 151