Essays on Labor Economics The Role of Government in Labor Supply Choices

 Niklas Blomqvist

Niklas Blom

qvist    Essays on Labor Econ

omics

Dissertations in Economics 2020:1

Doctoral Thesis in Economics at Stockholm University, Sweden 2020

Department of Economics

ISBN 978-91-7911-142-7ISSN 1404-3491

Niklas BlomqvistNiklas holds a B.Sc. and an M.Sc. inEconomics from StockholmUniversity

Essays on Labor EconomicsThe Role of Government in Labor Supply ChoicesNiklas Blomqvist

Academic dissertation for the Degree of Doctor of Philosophy in Economics atStockholm University to be publicly defended on Tuesday 9 June 2020 at 10.00 in sal G,Arrheniuslaboratorierna, Svante Arrhenius väg 20 C.

Abstract

"Right to Work Full-time" Policies and Involuntary Part-time EmploymentThis paper investigates the effect of right to full-time policies implemented to decrease involuntary part-time work for

public care workers employed by Swedish municipalities. Taking advantage of a staggered decision process, these policiesare evaluated using a difference-in-differences approach. Results show that involuntary part-time employment is real andsignificant, with 10% of part-time employed workers choosing full-time when given the opportunity. The effect mainlycomes from a decrease in contracts of <75% of full-time and an increase in contracts of 80% of full-time and above. Furtherresults from the full-time policies show that being more flexible in the choice of hours worked is popular among workers,indicated by an increase in tenure and reduced turnover in municipalities that offer more flexibility in the choice of hoursworked.

Hours Constraints and Tax Elasticity Estimates - Evidence from Swedish Public Care WorkersThere is a concern that tax elasticity estimates may be downward biased in the presence of optimization frictions for

workers. So far, there is limited evidence on the nature of these optimization frictions. This paper provides new insight intoone part of the optimization frictions black box, namely hours constraints. Using unique and newly collected data, I exploita staggered implementation of a policy that gave some public care workers the opportunity to choose their preferred hoursof work. Taking advantage of this policy, I estimate differences in tax elasticities between constrained and unconstrainedpublic care workers by comparing bunching at a large tax kink in the Swedish tax system. The empirical evidence pointsto the conclusion that hours constraints do not affect tax elasticity estimates.

Restricting Residence Permits - Short-Run Evidence from a Swedish ReformIn June 2016, the Swedish parliament decided to restrict the granting of permanent residence permits for asylum seekers

in Sweden. The new status quo for a refugee is a temporary rather than a permanent residence permit. In a first evaluationof this reform we use a Regression discontinuity analysis in which we follow refugees, aged 25-65, over their first yearsafter arrival. Our main results show that a temporary residence permit increases the probability of working and enrollingin regular education.

Mom and Dad Got Jobs: Natural Resources, Economic Activity, and Infant HealthThe impact of local economic shocks, such as the discovery and exploitation of natural resources, on labor markets and

health is not well understood. Both positive and negative effects have been documented in the literature. In this paper, weshow that the phase before active resource extraction begins directly affects the local economy. This implies that previousestimates – typically based on designs exploiting differences before and after the active phase of extraction begins - mayhave understated the actual effect of natural resource extraction on outcomes of interest. Using rich data from Swedencombined with differences in the timing and location of mineral exploitation permits, we find a positive impact on femaleand male employment and earnings and a negative effect on housing prices. Children’s health outcomes are also negativelyaffected, an effect likely driven by the increase in local economic activity rather than extraction-related externalities.

Keywords: Involuntary Part-time Employment, Labor Supply, Tax Elasticity, Refugees, Immigration, Integration,Natural Resource Extraction, Family Resources, Health.

Stockholm 2020http://urn.kb.se/resolve?urn=urn:nbn:se:su:diva-180933

ISBN 978-91-7911-142-7ISBN 978-91-7911-143-4ISSN 1404-3491

Department of Economics

Stockholm University, 106 91 Stockholm

ESSAYS ON LABOR ECONOMICS 

Niklas Blomqvist

Essays on Labor Economics 

The Role of Government in Labor Supply Choices 

Niklas Blomqvist

©Niklas Blomqvist, Stockholm University 2020 ISBN print 978-91-7911-142-7ISBN PDF 978-91-7911-143-4ISSN 1404-3491 Printed in Sweden by Universitetsservice US-AB, Stockholm 2020

Till den som känner sigträffad

Acknowledgements

First, I would like to thank my supervisors, Peter Skogman Thoursie,Martin Olsson, and Björn Tyrefors. Peter and Martin have helpedme, read and commented on my drafts more times than I would wishupon my worst enemy. Their help and support have been invaluableand for this I am grateful. Working together with Björn on two of mythesis chapters has been great since he has always been able to spotthe good things among the bad. It is also obvious how much Björncares for the welfare of his Ph.D. students and for this he will alwayshave my respect. Not being a supervisor, but a co-author on one ofthe thesis chapters, Andreas Madestam has been a great help to meas well. I would also like to thank Lisa Laun for a thorough readingof all chapters and many valuable comments.

Second, but first among equals, I have to mention Jonas Cederlöf,whom I have been sharing the experience of university studies withfor a decade. It looks crazy when I type it out, a decade togethercompleting both the Bachelor and Master program, before leavingme the last year of the Ph.D. program to finish it off at UppsalaUniversity. But I guess that time flies when you have fun, and havingfun is all but a guarantee when spending it with Jonas. I also thinkthat the end result, the thesis at this moment in your hand, would nothave been half as good without his help or without all our discussionsabout economics and econometrics, big and small.

I would also like to thank Elisabet Olme for many interesting and

fun, what English speaking countries think is called Happy Hours butin Sweden have the more apt name, After Works. I also much appreci-ated our accidental tradition of visiting Scandinavian cities together.Even though she had, and still have, strange working hours and I havecome to suspect that she does not understand what "impeccable senseof humor" means, she made the days at the office more enjoyable.

Kasper Kragh-Sørensen and Fredrik Paues deserve a special shoutout for, together with Jonas, making the first year of the Ph.D. pro-gram easier for me. Who would have thought that it could be reallyfun to sit next to another person and write code together in differentstatistic software programs? Furthermore, I like to thank BenedettaLerva who saved me from going insane in Berkeley. Jon Olofsson al-most seamlessly took over when Jonas abandoned Stockholm Uni-versity for Uppsala University, and let me ask stupid econometricquestions. Our "Poem of the day" was, of course, one of the dailyhighlights during the last year of the Ph.D. program. I would also liketo thank Roza Khoban and Ulrika Ahrsjö for being great office neigh-bors, Fredrik Runelöf for hoarding all the cups, Anna Linderoth forkeeping tabs on him, Louise Lorentzon for making the Ph.D. programa better social experience for everyone, Erik Lindgren for teaching mebouldering, Karin Kinnerud for showing me how to walk really longdistances, and Dany Kessel for being a great teacher and colleague.

Contents

Introduction 1

1 "Right to Work Full-time" Policies and InvoluntaryPart-time Employment 71.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . 81.2 The Right to Full-time Policies . . . . . . . . . . . . . 111.3 Data and Research Design . . . . . . . . . . . . . . . . 191.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . 251.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . 37References . . . . . . . . . . . . . . . . . . . . . . . . . . . . 381.A Appendix . . . . . . . . . . . . . . . . . . . . . . . . . 40

2 Hours Constraints and Tax Elasticity Estimates - Ev-idence from Swedish Public Care Workers 472.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . 482.2 Theory and Previous Literature . . . . . . . . . . . . . 532.3 Institutional Setting . . . . . . . . . . . . . . . . . . . 582.4 Empirical Models . . . . . . . . . . . . . . . . . . . . . 632.5 Data and Sample . . . . . . . . . . . . . . . . . . . . . 682.6 Evidence of Hours Constraints . . . . . . . . . . . . . 742.7 Hours Constraints and Tax Elasticities . . . . . . . . . 792.8 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . 86References . . . . . . . . . . . . . . . . . . . . . . . . . . . . 88

2.A Appendix . . . . . . . . . . . . . . . . . . . . . . . . . 902.B Appendix . . . . . . . . . . . . . . . . . . . . . . . . . 1012.C Appendix . . . . . . . . . . . . . . . . . . . . . . . . . 105

3 Restricting Residence Permits - Short-run Evidencefrom a Swedish Reform 1153.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . 1163.2 The Swedish Context . . . . . . . . . . . . . . . . . . . 1223.3 The Reform and Theoretical Predictions . . . . . . . . 1283.4 Data and empirical setting . . . . . . . . . . . . . . . . 1353.5 Main Results . . . . . . . . . . . . . . . . . . . . . . . 1423.6 Additional analyzes . . . . . . . . . . . . . . . . . . . . 1513.7 RD using decision date or age . . . . . . . . . . . . . . 1523.8 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . 154References . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1563.A Appendix . . . . . . . . . . . . . . . . . . . . . . . . . 162

4 Mom and Dad Got Jobs: Natural Resources, EconomicActivity, and Infant Health 1714.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . 1724.2 Institutional Setting and Data . . . . . . . . . . . . . . 1744.3 Methodology . . . . . . . . . . . . . . . . . . . . . . . 1784.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . 1794.5 Mechanism and Robustness . . . . . . . . . . . . . . . 1834.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . 186References . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1874.7 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . 1904.8 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . 1944.A Appendix . . . . . . . . . . . . . . . . . . . . . . . . . 196

Sammanfattning (Swedish Summary) 205

Introduction

Governments have a vast and variable impact on employment, wages,and hours of work. First, the government is an employer, with a directimpact on some workers’ wages and hours of work. In Sweden, thisis an important way in which the government can affect employmentconditions, with one-third of all workers being employed by the publicsector. Second, in order for the government to function, it taxes itscitizens. These taxes have an indirect impact on workers and theirchoice of hours worked, which depends on the type and level of the tax.Third, apart from taxes, the government decides on the institutionsthat in themselves affect choices and possibilities in the labor marketfor its citizens. This thesis consists of four self-contained chapters thateach focus on some of the different ways in which governments canhave an impact on employment, wages, and hours of work.

The first chapter of this thesis, "Right to Work Full-time"Policies and Involuntary Part-time Employment, visits thegovernment as an employer. In this chapter, I study the effect of apolicy change implemented by Swedish local governments on the mu-nicipality level. The municipalities decided to implement "right to full-time" policies. These policies gave public care workers, employed bythe municipalities, the right to choose how many hours they wanted towork, within certain limits. Taking advantage of a staggered decisionprocess, these policies are evaluated using a difference-in-differencesapproach. The results from the evaluation of the policies show that

1

2 INTRODUCTION

10% of part-time workers choose to work full-time instead, when giventhe opportunity. The study also showed that the changes in contractedhours mainly stem from workers with contracts of <75% of a full-timecontract deciding to increase their contracted hours. Furthermore, af-ter the local governments decided to implement full-time policies forpublic care workers, turnover in the sector decreased while tenureincreased, indicating the policies were popular.

The fact that public care workers did change their contractedhours of work when given the opportunity shows that a significantminority of them did not work their optimal hours. This, in turn,indicates that local governments acting as employers in the public caresectors can act as monopsonist employers to some extent. In Sweden,almost 18% of all workers are employed in the public sector on themunicipality level, and out of these, 38% are public care workers.Thus, a significant part of the labor market can be characterized asmonopsonistic (in a broad sense).

There has been a concern among politicians on the local govern-ment level that public care work is not attractive enough to meet thelong-term demand for public care workers. This chapter shows thatsuch concerns might be correct. Since public care employers can actas monopsonists, it might lead to cheaper employment solutions inthe short term and a lack of workers in the long term. This chaptershows that, since turnover decreased and tenure increased because ofthe right to full-time policies, it is possible for local governments tochange policies in such a way to make public work more attractive. Asone last point, leading up to the next chapter in the thesis, these re-sults strongly suggest that some workers are constrained in the choiceof hours worked.

The second chapter of this thesis, Hours Constraints and TaxElasticity Estimates - Evidence from Swedish Public CareWorkers, focuses on how we measure tax elasticities. Governmentsneed taxes to function. One problem is that taxes, to different de-

3

grees, affect labor supply. For tax policies to help reach the goalsof the public, it is important to understand how and by how muchtaxes affect labor supply. Thus, empirical tax elasticity estimates areparamount to study and understand in order to decide the optimallevel of taxes. By extension, it is important to understand if, and byhow much, optimization frictions affect empirical tax elasticity mea-sures. There has been a worry that tax elasticities estimated in theempirical literature are biased because of optimization frictions fac-ing workers. So far, there is limited evidence on the nature of theseoptimization frictions. This chapter provides insight into one part ofthe optimization friction black box, namely hours constraints.

Using the "right to full-time" policies from the previous chapter, Iestimate the difference in tax elasticities between public care workerswho are constrained in their choice of hours work compared withthose who are unconstrained. Workers who are unconstrained in theirchoice of hours work should have larger tax elasticity estimates thanconstrained workers. The reason for this is that constrained workersshould not be able to react to taxes by changing their labor supplyin the short run, while unconstrained workers can. Thus, if hoursconstraints create an important bias in tax elasticity estimates, publiccare workers in "right to full-time" municipalities should have largertax elasticity estimates than their counterparts in non "right to full-time" municipalities.

That some type of optimization friction affects empirical tax elas-ticity estimates is already known. The question is what these opti-mization frictions consist of. Hours constraints is one candidate, andlack of information or understanding of the tax system is another. Itis important to be able to differentiate between these two optimiza-tion frictions, since they might have different long-run implications.Hours constraints is a short-term constraint that will bias the esti-mated tax elasticity downwards, while workers will still react fully totaxes in the long run. Lack of information or understanding of the

4 INTRODUCTION

tax system, on the other hand, may affect how workers react to taxesboth in the short- and long run. If workers are uninformed in both theshort- and long run they will not react to taxes, which will yield smalltax elasticity estimates. However, as long as the lack of informationis persistent, the empirical observation that workers do not react totaxes is correct, rather than a result of a bias. Thus, it is important toseparate hours constraints and information as optimization frictions,since they might lead to different conclusions about a potential biasin tax elasticity estimates.

Using the bunching approach around a large kink in the Swedishtax system, I show that there is no difference in bunching for con-strained and unconstrained public care workers. The null result pointsto the conclusion that hours constraints do not significantly affect taxelasticity estimates for this group of public care workers. The impor-tance of information, and its persistence, as an optimization frictionremains to be studied.

The third and fourth chapters of this thesis go into two spe-cific institutions and policies that may affect employment, wages andhours of work. The third chapter, Restricting Residence Permits- Short-run Evidence from a Swedish Reform, jointly writtenwith Peter Skogman Thoursie and Björn Tyrefors, evaluates one ma-jor component of the Swedish integration policy, stipulating whethertemporary or permanent residence permits should be granted to asy-lum seekers. The question of how to integrate refugees has receivedgreat attention considering the rise in refugees arriving in the EU inthe last decade. Furthermore, with climate change, we can count onthis issue to be even more prominent in the future. This chapter an-swers the question of how two different types of residence permits,temporary or permanent, affect integration for refugees. Since it isimpossible to grant asylum to a refugee without giving some type ofresidence permit, the policy choice of granting temporary or perma-nent permits will affect all refugees and how it affects integration is

5

important to study.Using a policy change in June 2016, where the Swedish parliament

decided to restrict the granting of residence permits for asylum seek-ers in Sweden, this chapter uses a Regression discontinuity design inwhich we follow the refugees over their first years after arrival. Thisfirst study analyzes the effect on refugees 25-65 years old and findspositive effects on education and employment of receiving a temporaryinstead of permanent residency. One possible explanation for this re-sult is that the Swedish legislation provides work incentives for asylumseekers with temporary residence permits. A major component of theSwedish legislation is that an immigrant with a temporary residencepermit can receive a permanent residence permit by working. How-ever, we have yet to conduct a study on younger individuals, since toofew have received grades from primary and upper secondary schoolto do so. Furthermore, in the future, we are going to look into thehealth effects for individuals receiving temporary instead of perma-nent residency. This remains to be done. Without that information, itis too soon to use this study to give policy recommendations, or drawtoo stark conclusions about the effect of different types of residencepermits. It is also important to note that temporary residency per-mits can have other effects. One example is that it could reduce thenumber of asylum seekers arriving to a specific country, which couldbe a preference of the government.

The fourth chapter of this thesis, Mom and Dad Got Jobs:Natural Resources, Economic Activity, and Infant Health,jointly written with Andreas Madestam, Emilia Simeonova, and BjörnTyrefors, study another institutional setting that may be of impor-tance for employment, wages and health outcomes. Here we delvedeeper into the mining and fracking literature and the local economicand health impacts of resource extraction. The impact of local eco-nomic shocks, such as the discovery and exploitation of natural re-sources on labor markets and health is not well understood. Both

6 INTRODUCTION

positive and negative effects have been documented in the literature.This chapter shows that the phase before active resource extractionbegins, affect the local economy. We use rich data from Sweden com-bined with differences in the timing and location of mineral exploita-tion permits in a difference-in-differences setting. The results showa positive impact on employment and earnings and a negative ef-fect on housing prices. Children’s health outcomes are also negativelyaffected, an effect likely driven by the increase in local economic ac-tivity rather than extraction-related externalities. Previous studieshave typically based their research designs on exploiting differencesbefore and after the active phase of resource extraction begins. Ourresults imply that these previous estimates may have understated theactual effect of natural resource extraction on outcomes of interest.Taken together, the results point to the importance of accounting forall phases related to natural resource extraction to correctly assessthe full impact on local economies and health.

Chapter 1

"Right to Work Full-time"Policiesand Involuntary Part-time Employment∗

∗I thank Jonas Cederlöf, Lisa Laun, Jon Olofsson, Martin Olsson, Peter Skog-man Thoursie, and seminar participants at Stockholm University Department ofEconomics for valuable comments and feedback. I would also like to thank EmilJohansson who got me interested in this subject, to begin with. All errors are myown.

8 CHAPTER 1

1.1 Introduction

Regulation of working hours has long been an important topic bothin the political debate and in the economic literature (Boeri and vanOurs 2008). From the perspective of workers, it might not be pos-sible to choose the optimal amount of hours worked. If workers areconstrained in their choice of hours there exist under- and overemploy-ment, which, just like unemployment, may have welfare consequences.In the debate about the regulation of working hours, the choice be-tween part-time and full-time employment is important. Part-timework has, at least historically, enabled women to enter the labor force(Blau and Kahn 2013, Sundström 1991). At the same time, a sig-nificant minority of workers work part-time involuntary according tosurveys (Boeri and van Ours 2008). There is also a concern that part-time work might lead to women being marginalized in the labor mar-ket. Part-time work might come with a pay penalty (Manning andPetrongolo 2008) and it has been shown that part of the gender wagegap can be explained by employers rewarding those who work longhours (Goldin 2014).

In surveys from 1997, presented by Boeri and van Ours (2008),31% (35%) of women (men) worked part-time involuntary in Sweden.1However, the extent of involuntary part-time employment varies be-tween countries. For example, the US only had 8% (7%) of part-timework being involuntary during the same period, while France had39% (53%) involuntary part-time workers. In light of the evidence ofwidespread involuntary part-time employment, several Swedish mu-nicipalities started to implement "right to work full-time" policies(henceforth full-time policies) for public care workers. From 2000 to2013, 99 of Sweden’s 290 municipalities decided to implement a full-time policy. Two primary reasons motivated politicians to implementthese policies. First, they wanted to make public work in the munic-

1In a similar survey from 2002-2003, presented by Lundqvist et al. (2005), 20%of women and men worked part-time involuntary.

1.1. INTRODUCTION 9

ipality sector more attractive. Second, they wanted to decrease in-voluntary part-time employment, which was seen as one of the maindrivers of the gender earnings gap.

The setting, with a staggered decision process, provides a uniqueopportunity to evaluate the full-time policies extensively. To this endI have collected minutes from the municipal council meetings fromwhen the decisions to implement a full-time policy were made. Thepolicies made it possible for public care workers to choose how manyhours they wanted to work and the employer had to comply withthat choice.2 To evaluate the policies I use a difference-in-differencesmodel to first measure how the policies affected earnings, contractedhours and share of workers on a full-time contract in the public caresector. In order to better understand the full effect of the policies Ialso look at how the distribution of contracted hours changes. Second,to get an idea of whether hours constraints affect the match quality ofthe constrained workers I measure how the full-time policies affectedtenure and turnover.

Thanks to the minutes, it is possible to get a more detailed under-standing of the full-time policies. Some municipalities offered a freechoice of hours, while other municipalities offered a choice betweenpart-time and full-time employment only. Half of the municipalitiesalso implemented the policy for all public workers, not just publiccare workers. Furthermore, some municipalities implemented the full-time policy immediately and some municipalities implemented thefull-time policy a few years after the decision. The effects of thesedifferences are explored in a heterogeneity analysis.

I find that the full-time policies led to an increase in contractedhours of 1.4 percentage points on average for public care workers inthe municipalities. The increase in contracted hours came from a de-crease in contracts below 75% of a full-time contract and an increase

2The choice was typically restricted to be within a certain interval, e.g. within75-100%, of a full-time contract.

10 CHAPTER 1

in contracts of 80% of a full-time contract and above. When lookingat the change in the distribution of contracted hours, it seems as ifpublic care workers in practice could change their contracts in incre-ments of five percentage points. Furthermore, the annual earnings forthe public care workers increased by 3,000 SEK,3 while the share ofpublic care workers on a full-time contract increased by 6 percentagepoints. The last point constitutes 10% of part-time workers switchingto full-time. These results point to the conclusion that a significantminority of public care workers were, in fact, working part-time in-voluntary. There is also evidence of the policies being popular amongthe workers, as shown by a 5% increase in tenure and 7% fewer publiccare workers leaving their employment. Surprisingly, a heterogeneityanalysis shows that even in municipalities that implemented full-timepolicies for all public workers, only public care workers were affectedin practice.

These results give insights that relate to the literature that ex-amines the prevalence of hours constraints (see e.g. Beffy et al. 2019,Bloemen 2000, Blundell and Brewer 2008, Bryan 2007, Dickens andLundberg 1993, Johnson 2011, Kahn and Lang 1991, 1995). In gen-eral, these studies find that there are workers that are constrainedin their choice of hours worked − with some notable exceptions, seee.g. Ham and Reilly (2002) or Johnson (2011). Furthermore, this pa-per provides an extensive review of Swedish municipalities’ full-timepolicies which, being interesting in their own right, can be used asthe first stage in many potential studies of other economic questions.For example, as have been done in the second chapter of this thesis,these policies can be used to answer the question of how optimiza-tion frictions, in the form of hours constraints, affect tax elasticityestimates.

The rest of the paper is structured as follows. Section 1.2 goesthrough the institutional setting. Section 1.3 presents the data and

3∼315 USD in the exchange rate of 2019.

1.2. THE RIGHT TO FULL-TIME POLICIES 11

empirical model, while section 1.4 shows the results and robustnesstests. Finally, section 1.5 concludes.

1.2 The Right to Full-time Policies

The data on the decisions to implement full-time policies come frommunicipal council meeting minutes.4 I sent out requests to all munic-ipal archives for municipal council meeting minutes from the meetingwhen a decision to implement a full-time policy was made. 91% (265)of Sweden’s municipal archives answered. Out of the 265, 99 had de-cided to implement such a policy during 2000-2013. The first waveof data collection for municipal council meeting minutes started in2014, making 2013 the last year for which it is possible to know if afull-time policy was decided upon.

The purpose of the policies was to reduce involuntary part-timework among public workers, employed by the municipalities. Therewere usually two main arguments in favor prior to the decision toimplement full-time policies. First, politicians and officials worriedabout the weak interest of young people in working in the publicsector. With a large share of older workers, close to retirement, therewas a risk of labor supply shortage and a need of making work in thepublic sector more attractive. The full-time policies were meant to dojust that. Second, part-time is more common for women comparedto men. By reducing involuntary part-time politicians saw a way ofincreasing equality between men and women.

The decisions, and subsequent implementations, of full-time poli-cies differed from municipality to municipality. Since there was a lotof heterogeneity in the full-time rules I divided the decisions intothree categories. In the first, workers could choose hours freely be-

4These decisions are public documents and must be archived. This whole sec-tion is based on a thorough reading of minutes from municipal council meetingsfrom when the decisions of full-time policies were made.

12 CHAPTER 1

tween 75-100% of a full-time contract.5 In the second, workers couldchoose hours in increments of 5 or 10 percentage points between atleast 75-100% of a full-time contract. In the third, workers could onlychoose between working part-time or full-time. In the third category,it was unclear if there were several different part-time contracts tochoose from. Thus, this category could include municipalities that of-fered a range of different contracted hours. As Table 2.5 shows, 49%of the municipalities that decided to implement a full-time policy of-fered freely adjustable contracts. Thus, it was usually not necessaryto demand full-time. A 70% part-time worker could demand an 80%part-time contract, for example.

As shown in Table 2.5, 44% of the municipalities implementedthe policy almost immediately upon decision, while 56% implementedthe policy gradually over a few years. Some municipalities did nothave a specific date for implementation. Because of this, and becauseit is possible that some public employers started to act upon thedecisions even before implementation, I have to use the decision date,rather than the implementation date, as the treatment variable inthe empirical model. All municipalities included both present workersand future hires in the policy. In general, the biggest issue for themunicipalities was the public care sector. Involuntary part-time wasseen as more widespread in the care sector, compared to other sectors.This is why all municipalities that decided to implement a policyincluded the care sector. In half of the cases all sectors were includedin the full-time policy. Because of this, the main focus of this paperwill be the public care sector.

5This is the minimum requirement to be part of the first category. Some full-time municipalities had a wider range where the choice was free, for example from60-100% of a full-time contract. Furthermore, municipalities that implemented afree choice of hours without mentioning a restriction are part of this category. Inpractice, it is safe to assume that there were some restrictions downward in thechoice of contracted hours also in these municipalities.

1.2. THE RIGHT TO FULL-TIME POLICIES 13

Tab

le1.

1:Descriptiv

estatistic

sof

thedecision

toim

plem

entfull-tim

epolicies

Free

choice

Partly

free

choice

Part-tim

eor

All

ofho

urs

ofho

urs

Full-tim

e

Shareof

full-tim

emun

icipalities

0.49

0.15

0.36

1

Shareintrod

ucingfull-tim

e:with

in1year

0.59

0.42

0.27

0.44

successiv

elyover<5years

0.41

0.58

0.73

0.56

Shareintrod

ucingfull-tim

eto:

Caresector

11

11

Scho

olsector

0.48

0.62

0.68

0.57

Allsectors

0.38

0.54

0.68

0.51

Notes:Mun

icipalities

arecoun

ted

asprovidingFree

choice

ofho

ursif

itis

atleastpo

ssible

tochoo

seho

ursfreely

with

inan

interval

of75-100%

ofafull-tim

econtract.P

artly

free

choice

ofho

ursmeans

that

workers

canchoo

secertain

intervals(e.g.intervals

of5%

offull-tim

e).P

art-tim

eor

Full-tim

emeans

that

workers

canchoo

sebe

tweenon

lythose.

ForPart-tim

eor

Full-tim

e,itisoftenun

clearifpa

rt-tim

eisfix

ed,o

rifitispo

ssible

tochoo

sebe

tweenseverald

ifferent

part-tim

econtracts.

Thu

s,this

columninclud

esworkers

that

areprob

ably

morefree

intheirchoice

ofho

ursthan

just

choo

sing

betw

eentw

ofix

edcontracts.

Scho

olsector

includ

epreschoo

ls.

14 CHAPTER 1

In general, the public care sector workers are employed as nurses,assistant nurses, caretakers, and personal assistants working in the el-derly care sector or for people with disabilities. Another large group inthe public care sector are social workers. On average, 38% of the pub-lic workers employed by the municipalities are care workers. Aroundthe same share of public workers employed by the municipalities workin schools or preschools.

Only a few (13) municipalities specified when workers could choosetheir hours worked, but those who did stipulated that workers shouldbe able to change to their preferred hours of work at least once ayear. Even though the employer had to comply with their employees’wishes, extra hours did not always have to be situated in the sameworkplace. The extra hours demanded by part-time employees couldbe pooled by the municipality, meaning that workers could be sent toother workplaces substituting for workers on sick leave. In some mu-nicipalities this rule applied to all workers, meaning that all employeeshad some of their hours in a pool. One of the reasons full-time was notoffered before the policies were the fear of losing flexibility. Poolingworkers was one solution to this problem. Another solution presentedby some municipalities was a short-term injection of money in orderto give the establishments in the public care sector the possibility towork out scheduling issues.

Figure 1.1 shows the number of municipalities that decided to im-plement a full-time policy during the years 2000-2013. There does notseem to be any macro shocks behind the decisions, rather there was asteady increase in municipalities offering full-time policies. Not eventhe Great recession seems to have affected the rate of municipalitiesdeciding to implement such a policy.

Figure 1.2 and Table 1.3 show descriptive statistics for public careworkers in municipalities one year before a full-time policy was de-cided upon. These statistics are compared to a random sample ofpublic care workers in municipalities that never decided to implement

1.2. THE RIGHT TO FULL-TIME POLICIES 15

Figure 1.1: Timing of the decision to implement full-time policies0

2040

6080

100

Num

ber o

f mun

icip

aliti

es w

ith fu

ll-tim

e po

licy

2000 2002 2004 2006 2008 2010 2012year

Yearly decisionsCumulative sum

Notes: Yearly number of municipalities that decided to implement a full-time pol-icy.

a full-time policy, sampled to match the number of workers in eachyear in the full-time sample. Figure 1.2 shows that the most commoncontract for public care workers in all municipalities is a full-timecontract. There are spikes at part-time contracts offering 50, 75, 80,85, and 90% of a full-time contract. Figure 1.2 also shows that thedistribution of contracted hours does not differ between public careworkers in full-time municipalities and public care workers in non full-time municipalities before the policies take place. Table 1.3 shows thatin full-time municipalities, before deciding to implement a full-timepolicy, public care workers are quite similar to public care workersin municipalities that do not implement full-time policies. Earnings,wages, tenure, age, etc. are all similar. However, as shown in Table1.2 there are some differences when it comes to which municipalitiesthat decide to implement a full-time policy. Compared to the average

16 CHAPTER 1

Figure 1.2: Distribution of contracted hours before the reform

0.1

.2.3

.4D

ensi

ty o

f wor

kers

with

spe

cific

con

tract

ed h

ours

50 60 70 75 80 85 90 100contract

One year before non full-timeOne year before full-time

Notes: Density distribution of contracted hours for public care workers in full-timemunicipalities one year before the decision (maroon colored bars) and for a randomsample of public care workers in non full-time municipalities (uncolored bars)sampled to match the number of public care workers in full-time municipalitieseach year. The x-axis is defined as the percent of a full-time contract. All workerswith contracts above 100% are pooled in the 100% bar.

Swedish municipality the full-time municipalities are more left-wing.It is more common for medium-sized towns to implement a full-timepolicy and less common among large cities and municipalities nearlarge cities.

1.2. THE RIGHT TO FULL-TIME POLICIES 17

Table 1.2: Summary statistics for municipalities deciding to implement afull-time policy

Full-time Allmunicipalities municipalities

Share with:

Left-wing government 0.57 0.42

Right-wing government 0.26 0.40

Share type of municipality:

Large city 0.10 0.16

Medium sized town 0.43 0.38

Smaller town/rural 0.46 0.46

Notes: This table shows descriptive statistics of municipalities that decidedto implement a full-time policy, one year before the decision. The secondcolumn shows the average statistics for all municipalities in the sample (in-cluding the full-time municipalities). Large city includes municipalities nearlarge cities. Medium-sized town includes municipalities near medium-sizedtowns. Smaller town/rural includes smaller urban areas and rural munici-palities.

18 CHAPTER 1

Table 1.3: Summary statistics for public care workers

Full-time Controlmunicipality municipality

Share working full-time 0.38 0.35(0.49) (0.48)

Mean contracted hours (% of full-time) 77% 76%(27) (27)

Mean labor earnings (in SEK) 187,352 186,768(85,449) (85,562)

Mean labor PT earnings (in SEK) 156,633 158,225(77,075) (76,798)

Full-time equivalent wage (in SEK) 20,966 21,110(4,239) (4,269)

Mean tenure (in years) 4.1 4.1(4.1) (4.2)

Mean age 42 42(12) (12)

Share women 0.89 0.90(0.31) (0.31)

Share with children 0.38 0.38(0.48) (0.49)

Highest achieved education:College degree 0.23 0.24

(0.42) (0.43)High school degree 0.68 0.67

(0.29) (0.29)

Observations 112,335 112,335

Notes: The values in the first column come from all public care workers in full-time municipalities the year before a decision was made. The values in the secondcolumn come from a random sample of public care workers in non full-time mu-nicipalities, where the sample matches the number of public care workers in eachyear in full-time municipalities. "Mean labor PT earnings" is the mean earnings forworkers on a part-time contract. Both labor earnings variables are expressed in an-nual earnings. Full-time equivalent wage is expressed in monthly wages. Earningsand wages are inflation-adjusted (in 2019, 1 USD∼9.5 SEK). Standard deviationin parenthesis.

1.3. DATA AND RESEARCH DESIGN 19

1.3 Data and Research Design

1.3.1 Data and Sample

The data in this paper comes from four main sources. The firstsource is the minutes from the municipality council meetings,described above. From those minutes, I create a variable withinformation on the year when a full-time policy was decided on.Furthermore, I create dummy-variables for different decision types(if the municipality offered a free choice of hours or only offereda choice between part-time and full-time, if the decision wasimplemented within a year or successively and if other sectors thanthe public care sector were affected).

The second source is Statistic Sweden’s registers LISA6 which in-clude the full population of Swedish residents over the age of fifteen.From LISA I got information on annual labor earnings, age, gen-der, number of children and highest achieved education. LISA reporttwo-digit industry codes, which are used to establish if workers areemployed in the care sector, school sector, or another sector. All pub-lic workers employed in industries working with "Human health andsocial work activities" are defined as care workers. Thus care workin this setting include elderly care, health care, disability care, andsocial workers, but not child care workers.7

The third source is Statistic Sweden’s "Wage structure statistics"which report yearly panels of administrative data on all workers em-ployed by a municipality, and include the full population of (munici-pality employed) public care workers. The "Wage structure statistics"thus provide information on if workers are employed by the munici-pality or not. From these registers, I got information on contracted

6The "Longitudinal integrated database for health insurance and labour mar-ket studies".

7This is "The Swedish Standard Industrial Classification", or SNI codes. Forthe years 1996-2006, the two-digit SNI code 85 includes all care workers in thesample, while the years 2007-2013 have the SNI codes 86-88.

20 CHAPTER 1

hours (reported in percent of a full-time contract), and monthly full-time equivalent wage rates. Contracted hours is used to understandif a worker has a full-time contract or not. In this paper, a full-timecontract is defined as having contracted hours of at least 90% of afull-time contract or more, which is in line with the definition of full-time used by Statistic Sweden. Tenure is defined as the number ofconsecutive years working in the same municipality in the public caresector. If a worker works somewhere else for a year, and then return,the tenure variable is reset to zero.8

The fourth source comes from the Swedish Association of LocalAuthorities and Regions (SALAR). This data is openly available andprovides information on what type of majority run the municipalitycouncils (left-, right-wing, or bipartisan) as well as information onthe type of municipality (large city, medium sized town, or smalltown/rural).

The main sample is restricted to all public care workers employedby the municipalities 1996-2013. Workers in the municipalities thatdid not answer if they have a full-time policy are excluded. This meansthat the sample consists of repeated cross-sections of all public careworkers in full-time municipalities and municipalities that never de-cide to implement a full-time policy.

1.3.2 Model and Research Design

To measure the effect of deciding to implement the full-time poli-cies employment in municipalities I use the following difference-in-differences model,

Yimt = α+ δSDSimt + δMD

Mimt + δLD

Limt + µm + µt + X imt + eimt,(1.1)

8From the perspective of the municipality, what is interesting is to retainworkers in the public care sector, not which specific elderly care center a workeris employed at, which is why I use this definition of tenure.

1.3. DATA AND RESEARCH DESIGN 21

where Yimt is the outcome variable of interest. µm are municipalityfixed effects, µt are year fixed effects and X imt is a vector of controlvariables. DS

imt is a dummy variable equal to one if it is 0-3 yearsafter the decision to implement a full-time policy in a municipality.Similarly, DM

imt is equal to one if is 4-7 years after a decision, andDLimt is equal to one if it is 8 or more years after a decision. Thus,

δS shows the short run effect of the full-time policy, while δM and δLshows the medium- and the long run effects, respectively.

To test the common trends assumption, I also estimate the fol-lowing event study model,

Yimt = α+∑k

δkDkimt + µm + µt + X imt + eimt, (1.2)

where Dkimt are dummy variables that equal one when it is k periods

to (from) the decision to implement a full-time policy in a munici-pality. Thus, holding time- and municipality trends constant, δk showthe average difference in Yimt each period compared to the referenceperiod, which is one year before implementation. If δk = 0 for all pe-riods prior to the full-time policy it lends credibility to the commontrends assumption.

All regressions are carried out using robust standard errors clus-tered at the municipality level (Moulton, 1990). The number of clus-ters, and treatment units, are more than enough to get the correctstandard errors (Bertrand et al. 2004, Conley and Taber 2011). Fur-thermore, all regressions include individuals from never-treated mu-nicipalities.9

As a robustness test, I also run the control variables as dependent

9Borusyak and Jaravel (2017) have shown that event study estimations mayhave a problem identifying a linear trend in the pre-trend path and dynamictreatment effects. The fix for this problem is to include a control group that can pindown the year effects. Thus, the event study regressions in this paper will includethe 166 never treated municipalities as well as the 99 treated municipalities.

22 CHAPTER 1

Table 1.4: Number and share of municipalities that are included in eventtime

∑k

Lead Number of Share of Lag Number of Share ofmunicipalities municipalities municipalities municipalities

-1 99 1 1 86 0.87-2 99 1 2 73 0.74-3 99 1 3 67 0.68-4 99 1 4 58 0.59-5 97 0.97 5 50 0.51-6 87 0.88 6 43 0.43-7 80 0.81 7 36 0.36-8 76 0.77 8 29 0.29-9 73 0.74 9 26 0.26-10 70 0.71 10 23 0.23-11 63 0.64 11 19 0.19-12 56 0.57 12 12 0.12

variables, using

Ximt = α+ δSDSimt + δMD

Mimt + δLD

Limt + µm + µt + eimt, (1.3)

where Ximt is the control variable.10

Table 1.4 shows the number of municipalities included in eachevent time. Only 30% of municipalities are left to estimate an effectafter 8 years, and after 12 years only 12% of the municipalities arepresent. This means that the long run effect, δL, should be interpretedwith caution in the next section.

There’s been a recent discussion about the use of staggereddifference-in-differences models in the presence of dynamic effects

10Pei et al. (2017) caution against using control variables on the right-hand sideof regressions. Adding control variables affect the δ estimate of interest throughtwo channels, the effect of the control on Yimt and the correlation between thecontrol variable and the independent variable of interest. Thus, the effect on theδ estimate of interest of including control variables might be attenuated towardszero, especially if the control variables contain classical measurement errors.

1.3. DATA AND RESEARCH DESIGN 23

(see e.g. Goodman-Bacon 2018, Meer and West 2015).11 If thereare dynamic effects, the difference-in-differences estimate will bebiased towards zero. One way to overcome this problem is to use anevent study model instead. In this paper, I present the main resultsusing both event study- and difference-in-differences estimates.However, the difference-in-differences estimates are divided onshort-, medium-, and long run effects, which in practice is a middleway between an event study and a pure difference-in-differencesmodel. This will to some extent alleviate the potential problem ofthe estimates being biased toward zero.

11The main problem arises because a staggered difference-in-differences modelwill be a weighted average of all two-by-two difference-in-differences estimators inthe panel data set. What this means is that units that are treated early will actas a control for units that are treated later (Goodman-Bacon 2018). Early treatedunits acting as controls for later treated units are only a problem if the treatmenteffect is dynamic. In that case, an early treated unit’s outcome variable will be ona different trend path because of the treatment and the comparison will necessarilybecome biased.

24 CHAPTER 1

Figure 1.3: Density of contracted hours

0.0

5.1

.15

.2D

ensi

ty o

f wor

kers

with

spe

cific

con

tract

ed h

ours

50 60 70 75 80 85 90 100contract

One year before non full-timeFive years after non full-time

(a) Distribution before/after a non decision

0.0

5.1

.15

.2D

ensi

ty o

f wor

kers

with

spe

cific

con

tract

ed h

ours

50 60 70 75 80 85 90 100contract

One year before full-timeFive years after full-time

(b) Distribution before/after a decision

Notes: Density distribution of contracted hours for public care workers in full-timemunicipalities and for a random sample of public care workers in non full-time mu-nicipalities sampled to match the number of public care workers in full-time mu-nicipalities each year. The x-axis is defined as the percent of a full-time contract.Panel (a) includes a random sample of public care workers from municipalitiesthat never decided to implement a full-time policy. The maroon colored bars showthe distribution of contracted hours for the random sample of public care workersdrawn to match the yearly number of public care workers in full-time municipal-ities one year before the decision. The uncolored bars show the distribution ofcontracted hours for the random sample of public care workers drawn to matchthe yearly number of public care workers in full-time municipalities five years af-ter a decision. Panel (b) shows the distribution of contracted hours for public careworkers in actual full-time municipalities one year before (maroon colored bars)and five years after (uncolored bars) a full-time decision, respectively.

1.4. RESULTS 25

1.4 Results

1.4.1 Raw Distributions of Contracted Hours

Before moving to the regression results it is enlightening to look at theraw distributions of contracted hours. Figure 2.5 shows the distribu-tion of contracted hours (in percent of a full-time contract) for publiccare workers. Panel (a) shows the distribution for a random sampleof public care workers drawn from municipalities that never decidedto implement a full-time policy. The maroon colored bars representa random sample drawn to match the yearly number of public careworkers employed in a full-time municipality one year before a full-time decision. The uncolored bars represent a random sample drawnto match the yearly number of public care workers employed in a full-time municipality five years after a full-time decision. By creatingthese samples from non full-time municipalities it is possible to seethat there does not seem to be any major changes in the distributionof contracted hours over time in municipalities that have not decidedto implement full-time policies.

Panel (b) shows the distribution of contracted hours for publiccare workers in full-time municipalities one year before an actual de-cision compared to five years after. The change in distribution comesfrom increased density for contracts of 80, 85, and 90% of a full-timecontract and a decrease in contracts below 80% of full-time. Thesefigures have left out a 100% full-time contract, since that type of con-tract dwarfs the other and thus obscures changes in the distribution.Furthermore, for readability purposes contracts below 50% of full-time have been left out. For the full set of contracts, see Figure 1.8 inAppendix A, which also shows that the major change after a full-timepolicy has been decided upon seems to be the increase in contractson exactly 100% of full-time. Figure 1.9 in Appendix A shows thatthese discrete changes in increments of five percentage points are atwork also in municipalities that offer "free choice of hours".

26 CHAPTER 1

Panel (a) and (b) of Figure 1.7, in Appendix A, is another way torepresent the same change reported here. Panel (a) shows that the dis-tribution of hours for public care workers in full-time municipalities,one year before a decision, is similar to the distribution of hours forpublic care workers in non full-time municipalities. Panel (b) showsthat five years after the decision to implement a full-time policy, thisis no longer the case. Five years after the decision, there are moreworkers on 80, 85, and 90% contracts than in the non full-time mu-nicipalities. At the same time, contracts below 80% of full-time workhave decreased. Again, Figure 1.8, in Appendix A shows that there isalso an increase in density for contracts on exactly 100% of full-time.

1.4.2 Contracted Hours and Annual Labor Earnings

If the existing contracts were preferred by all public care workers,a full-time policy would not change contracted hours of work for theemployees. Thus, to continue to gauge at the effect on the distributionof contracted hours Figure 1.4 shows the outcomes from 100 regres-sions where the probability of being above different sets of contractedhours are the dependent variables and the independent variables arethe medium run (4-7 years) difference-in-differences estimates. Thatis, in the first regression the dependent variable is the probability ofhaving contracted hours above 1% of a full-time contract, which isrepresented by the first blue dot in the figure. In the last regressionthe dependent variable is the probability of having contracted hoursabove 99% of a full-time contract, which is represented by the lastblue dot in the figure. The results from this exercise indicate thatthe change in contracted hours comes from an increase in contractedhours above 75% of a full-time contract. The jump in probability ofbeing above 75% of a full-time contract tells the same story as the rawdistribution of contracted hours in Figure 2.5, namely that most ofthe effect comes from workers on contracted hours of 75% and belowincreasing their hours.

1.4. RESULTS 27

Figure 1.4: Change in distribution of contracts-.0

2-.0

10

.01

.02

.03

.04

.05

.06

.07

.08

.09

.1

Cha

nge

in P

(Con

tract

ed h

ours

>x)

5 10 15 20 25 30 35 40 45 50 55 60 65 70 75 80 85 90 95 100Contracted hours (percent of full-time)

Notes: The results come from equation (1.1) in section 1.3.2. The regressions in-clude municipality and year fixed effects, as well as controls for local governmentmajority, age, gender, child, and educational dummies. The blue, dotted line rep-resents average treatment effects for the medium run (4-7 years) and the dashed,red lines represent the 95% confidence interval. Standard errors clustered on themunicipality level. Each dot represents a regression on the dependent variableP(Contracted hoursimt >x), where x is the number represented on the x-axis.

Contracted hours and share of full-time workers are the outcomesdirectly targeted by the policy. However, contracted hours could intheory change without actual hours changing, which is why it is alsoimportant to look at labor earnings. Thus, the rest of this section willlook into how the full-time policies affected the mean of contractedhours, share full-time workers and annual labor earnings. Figure 1.5shows that the pre-trends are stable for all outcomes, indicating thatthe common trends assumption is plausible. The effects of the policiesare clearly dynamic, increasing the first few years after the decision.

Panel A of Table 1.5 shows the outcome in the short run (0-3

28 CHAPTER 1

Figure 1.5: Event-study estimates on earnings, contracted hours and full-time work

-200

00

2000

4000

6000

Annu

al e

arni

ngs

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5 6 7Event time in years

(a) Annual labor earnings-1

-.50

.51

1.5

22.

5

Con

tract

ed h

ours

in p

erce

nt o

f ful

l-tim

e

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5 6 7Event time in years

(b) Contracted hours

-.05

-.025

0.0

25.0

5.0

75.1

Shar

e w

orki

ng fu

ll-tim

e

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5 6 7Event time in years

(c) Share working full-time

Notes: The blue, dotted line represents average treatment effects and the dashed,red lines represent the 95% confidence interval. The results come from the eventstudy regression (1.2) in section 1.3.2, where event time t-1 is the reference period.The regressions include municipality and year fixed effects, as well as controls forlocal government majority, age, gender, child, and educational dummies.

years after policy), medium run (4-7 years), and the long run (8+years). In the short run, the change is not significant, but after 4-7years annual earnings have increased by 3, 142 SEK on average (or∼ 2% of mean earnings). Since 38% of the public care workers alreadyhad a full-time contract, that is an increase of ∼ 5, 000 SEK for theworkers on part-time contracts (or ∼ 3% of mean part-time earnings).

1.4. RESULTS 29

In the medium run contracted hours are 1.38 percentage points longerand the share of full-time workers has increased by 6%. The last pointconstitutes ∼ 10% of workers on part-time contracts switching to full-time contracts. The mid-point estimates for the long run effects aresomewhat higher, but insignificantly so. Furthermore, they are lessprecise, because there are fewer observations left to measure a longrun effect.

Panel B, C, and D of Table 1.5 show the same outcomes butdivided into the three types of policy decisions with respect to howfree the public care workers were in their choice of contracted hours(see Table 2.5 in Section 1.2). In the long run, the effects are notsignificantly different for public care workers in municipalities thatoffer "free choice of hours" to municipalities that offer either a part-time or a full-time contract. The positive effect on annual earningsand share working full-time is more immediate in the "free choice ofhours" municipalities, with a significant effect already in the mediumrun. This can be explained by the fact that municipalities that offera "free choice of hours" in general also implemented the policy fasterthan municipalities that offered a choice between part-time and full-time (see Table 2.5 in Section 1.2). In Appendix A, Table 1.9 indeedshows that there is a more immediate effect of the full-time policiesin municipalities that implement the decision within a year.

Panel C shows the effect for those municipalities that offered sev-eral contracted hours options, but with increments of 5, or 10 per-centage points, rather than a free distribution. However, since only15 municipalities offered this type of contract, the results are notvery precise. There is a significant, and positive, effect on contractedhours and share working full-time in the long run, but a negative, andinsignificant, effect on annual earnings.

30 CHAPTER 1

Table 1.5: Main outcomes

(1) (2) (3)Annual Contracted Share workingearnings hours full-time

Panel A: All public care workersShort-run (0-3 years) 829 0.39 0.02∗∗∗

(515) (0.20) (0.00)Medium run (4-7 years) 3,142∗∗∗ 1.38∗∗∗ 0.06∗∗∗

(865) (0.31) (0.01)Long run (8+ years) 3,632∗∗ 1.44∗∗∗ 0.06∗∗∗

(1,264) (0.37) (0.01)Observations 3,958,528 3,958,528 3,958,528

Panel B: Free choice of hours municipalitiesShort-run (0-3 years) 1,464∗ 0.72∗ 0.03∗∗∗

(662) (0.30) (0.01)Medium run (4-7 years) 4,343∗∗∗ 1.81∗∗∗ 0.07∗∗∗

(897) (0.34) (0.01)Long run (8+ years) 4,121∗∗ 1.74∗∗∗ 0.07∗∗∗

(1,328) (0.38) (0.01)Observations 2,817,413 2,817,413 2,817,413

Panel C: Partly Free choice of hours municipalitiesShort-run (0-3 years) -425 -0.03 0.01

(827) (0.63) (0.01)Medium run (4-7 years) 263 1.02∗∗ 0.04

(1,387) (0.32) (0.02)Long run (8+ years) -1,152 1.60∗∗∗ 0.04∗

(1,819) (0.44) (0.02)Observations 2,247,692 2,247,692 2,247,692

1.4. RESULTS 31

Panel D: Part-time or Full-time municipalitiesShort-run (0-3 years) -483 -0.03 0.02∗∗

(1,086) (0.30) (0.01)Medium run (4-7 years) 2,000 0.79 0.05∗∗∗

(1,506) (0.61) (0.01)Long run (8+ years) 4,360∗∗ 0.95 0.07∗∗∗

(1,551) (0.61) (0.02)Observations 2,597,562 2,597,562 2,597,562

Notes: The results come from the regression equation (1.1) in section 1.3.2. PanelB, C, and D only include subsets of public care workers depending on what type ofmunicipality they work for, as defined in Table 2.5. The regressions include munici-pality and year fixed effects, as well as controls for local government majority, age,gender, child, and educational dummies. Annual earnings are inflation-adjustedand expressed in SEK. Contracted hours is defined as the percent of a full-timecontract. Full-time is the share of full-time workers. Standard errors clustered atthe municipality level in parenthesis. ∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001

In Appendix A, Table 1.8 shows the same outcome for the subsetof public workers employed by those municipalities that claim to im-plement the full-time policy for all workers. Panel A shows the effectfor public care workers in those municipalities, Panel B for all otherpublic workers, Panel C for public school (and preschool) workers, andPanel D for public child care workers. Public care workers in thesemunicipalities have comparable effects to the full sample of public careworkers. However, there does not seem to be a significant effect onother public workers. Only when focusing on public child care work-ers, a significant positive effect on earnings is visible. However, theeffect is not stable, nor explained by an increase in contracted hoursand should be interpreted with caution. In all, the full-time policiesseem to mainly target public care workers, even in municipalities thatimplement the policy for all public workers.

32 CHAPTER 1

Table 1.6: Tenure and turnover

(1) (2) (3) (4)Tenure Share leaving Share leaving Share leaving

to other to othercare employer municipality

Short run 0.06 -0.004 -0.004 0.000(0-3 years) (0.04) (0.003) (0.003) (0.000)

Medium run 0.22∗∗ -0.013∗∗ -0.012∗∗ 0.001(4-7 years) (0.08) (0.004) (0.004) (0.001)

Long run 0.40∗∗∗ -0.011∗ -0.008 0.000(8+ years) (0.11) (0.005) (0.005) (0.001)

Mean one year 4.1 0.18 0.13 0.01before decision

Observations 3,958,528 3,731,406 3,731,406 3,731,406

Notes: The results come from the regression equation (1.1) in section 1.3.2. Theregressions include municipality and year fixed effects, as well as controls for localgovernment majority, age, gender, child, and educational dummies. Tenure is mea-sured in years and defined as consecutive years working in the public care sectorfor the same municipality. Column (2) shows the share leaving the public caresector in the municipality for any reason. Column (3) shows the share leaving thepublic care sector in the municipality to work in the private care sector or anotherlevel of public care (e.g. county hospitals). Column (4) shows the share leavingthe public care sector in a municipality for public care employment in anothermunicipality. Leaving can not be observed in 2013, which is why column (2)-(4)have fewer observations. Standard errors clustered on the municipality level inparenthesis. ∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001

1.4.3 Match Quality

One of the two main goals of the full-time policies was to make publicwork for the municipality more attractive. One way to measure thesuccess of the policies and to understand if the possibility to choosehours worked more flexibly is popular among workers is to estimatethe policies’ effect on tenure and turnover. If the turnover rate de-

1.4. RESULTS 33

creases and workers stay employed by the municipality longer, it is asign of the full-time policies having increased the match quality andbeing popular among the workers. Thus, Table 1.6 shows the effectof the full-time policies on tenure and different measures of the shareof public care workers leaving the municipality employment. Column(1) shows the effect on tenure, defined as consecutive years workingin the public care sector for the same municipality. Column (2) showsthe effect on the share leaving employment in the public care sec-tor in the municipality that decided to implement a full-time policy.Column (3) shows the effect on the share leaving employment in thepublic care sector in the municipality to work in the private care sec-tor or another level of public care (e.g. county hospitals). Column(4) shows the effect on the share leaving employment in the publiccare sector in the municipality to work in the public care sector inanother municipality. If public care employers use the full-time poli-cies to compete for workers from other municipalities, the last columncould have shown such an effect. However, there are few transitionsfrom municipality to municipality and it does not seem to change asa result of the full-time policies.

Table 1.6 shows that tenure increase by 0.22 years 4-7 years afterpolicy decision, or 5% compared to the mean tenure the year before afull-time policy was decided on. The point estimate is almost twice aslarge, 0.4 years, in the long run. Here, it could perhaps be more illu-minating to look at the long run effects, since it could take some timefor reduced turnover to translate to increased tenure. However, thereis still the issue of there only being 30% of the full-time municipalitiesleft to measure an effect on 8 years after the reform.

Further results show that the share leaving the public care sectorat all in a municipality decreases by 1.3 percentage points, or 7%, 4-7years after the decision. The effect is of the same magnitude for shareleaving to another care employer, but that effect is not stable in thelong run.

34 CHAPTER 1

Figure 1.6: Event-study estimates on labor demand- and supply proxies-.0

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1.4.4 Robustness Checks

Demand and Supply Rather Than Policy?

One worry in the estimation of a policy effect is that there might besomething else driving both the implementation of a full-time policyand hours worked. This does not show up in the common trendsanalysis, but it could potentially be the case that politicians decide

1.4. RESULTS 35

to implement a policy because of changes in demand for or supply ofpublic care sector workers. To exclude this possibility I use outcomevariables that can act as proxies for supply and demand changes.

As a proxy for the demand of public care workers, I use the shareof residents over the age of 65. Since public care workers employed bythe municipality usually work in the elderly care sector, the share ofolder residents should affect the demand for public care workers.

Another proxy for both the demand and supply of public careworkers is the share of care workers in the private sector. Last, if de-mand or supply factors lie behind the decision to implement full-timepolicies, this should be visible in the general wage trend of public careworkers. If the demand for public care workers increases more in full-time municipalities prior to the policies, wages should go up. Thus, Irun the regression specified in equation (1.2) on these outcomes. Fig-ure 1.6 shows the result of this exercise. None of the outcome variablestrend differently before the decision to implement full-time policies.Wages do not change, either before or after the policies, the only thingthat changes are hours worked, the outcome targeted by the policy.Thus, the common trends tests, both for the main outcome variablesand the proxies for demand and supply factors point to the conclusionthat it is the policies themselves, and not any underlying factors, thatlie behind the effects found in Tables 1.4, 1.5, and 1.6.

The effect of full-time policies on the monthly wage rate could beinteresting as an outcome in its own right. However, it is not straight-forward to interpret a wage effect. If full-time work is desirable fromthe workers’ perspective, but not the employers’, a potential effectof a full-time policy could have been a wage cut to compensate theemployers. But since the full-time policies were forced upon the em-ployers, the expectations could also have been a wage hike, if workersnegotiate over hours and wage and now with the policy do not needto negotiate for more hours. Panel (c) in Figure 1.6 shows that thereis no effect on the wage rate, as a result of the full-time policies.

36 CHAPTER 1

Table 1.7: Full-time policies effect on sorting

(1) (2) (3) (4)Share Share with Share with Share withwomen children high school degree college degree

Short-run 0.000 0.001 0.002 -0.001(0-3 years) (0.001) (0.002) (0.003) (0.002)

Medium run 0.003 0.002 0.006 -0.003(4-7 years) (0.002) (0.004) (0.005) (0.004)

Long run 0.009∗∗∗ 0.008 0.011 -0.003(8+ years) (0.003) (0.005) (0.006) (0.004)

Observations 3,963,728 3,963,728 3,958,528 3,958,528

Notes: The results come from the regression equation (1.3) in section 1.3.2. Theregressions include municipality and year fixed effects. Standard errors clusteredon the municipality level in parenthesis.∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001

Sorting

If public care workers get the opportunity to work full-time, it mightbecome more attractive to work for the municipality for individualslooking for full-time work. Similarly, for workers not interested in full-time the municipality might become less attractive as a workplace.Thus, there is a possibility that the effects depend on sorting, ratherthan those originally employed by the municipality starting to workmore. Since the estimations above are measured using repeated cross-sections it is not possible to separate these two potential effects.

Instead, to investigate the sorting mechanism, I run difference-in-differences regressions (see equation (1.3)) on outcome variables thatshould change if sorting takes place as an effect of the policies. Table1.7 shows how the share of workers with children, share female work-ers, and share workers with different educational levels are affectedby the policies. None of these changes as a result of the policies in the

1.5. CONCLUSION 37

short- or medium run. Thus, there is no aggregate evidence of sort-ing, indicating that the effects found above do not depend on sorting.However, the long run effect on the share of women is positive andsignificant, which is further evidence in favor of being cautious wheninterpreting the estimated long run effects as causal.

Here, age is left out, since the positive effect on tenure leads to apositive effect on age as well. Instead, as a robustness check, panel Bof Figure 1.10 shows that the main effects are stable to the exclusionof age as a control variable. In fact, the point estimates are somewhathigher, which is expected if age increases (with tenure) as an effect ofthe full-time policies.

1.5 Conclusion

In this paper, I thoroughly investigate the effect of full-time poli-cies implemented to decrease involuntary part-time work for publiccare workers employed by Swedish municipalities. Taking advantageof a natural experiment where several Swedish municipalities imple-mented full-time policies for public care workers, this paper estimatesthe causal effect of reducing workers’ hours constraints. Results showthat involuntary part-time employment and hours constraints are realand significant, with 10% of part-time employed workers choosingfull-time when given the opportunity. The effect mainly comes froma decrease in contracts below 75% of full-time and an increase in con-tracts of 80% of full-time and above. Further results from the full-timepolicies show that being more flexible in the choice of hours workedis popular among workers, indicated by an increase in tenure andreduced turnover in municipalities that offer more flexibility in thechoice of hours worked.

38 CHAPTER 1

ReferencesBeffy, Magali; Richard Blundell; Antoine Bozio; Guy Laroque; Maxime Tô. 2019."Labour supply and taxation with restricted choices," Journal of Econometrics,211(1): 16-46.

Bertrand, Marianne, Esther Duflo, Sendhil Mullainathan. 2004. "How MuchShould We Trust Differences-in-Differences Estimates?," The Quarterly Journalof Economics, 119(1): 249-275.

Blau, Francine D.; Lawrence M. Kahn. 2013. "Female Labor Supply: WhyIs the United States Falling Behind?," American Economic Review, 103(3): 251-56.

Bloemen, Hans G. 2000. "A model of labour supply with job offer restrictions,"Labour Economics, 7(3): 297-312.

Blomqvist, Niklas. 2020. "Essays on Labor Economics - The Role of Governmentin Labor Supply Choices," Chapter 2, dissertation, Stockholm University.

Blundell, Richard; Mike Brewer, Marco Francesconi. 2008. "Job Changes andHours Changes: Understanding the Path of Labor Supply Adjustment," Journalof Labor Economics, 26(3): 421-453.

Boeri, Tito; Jan van Ours. 2008. "The Economics of Imperfect Labor Markets:First Edition," Princeton University Press, 101-120.

Borusyak, Kirill; Xavier Jaravel. 2017. "Revisiting Event Study Designs,"(May 8, 2017). Available at SSRN: https://ssrn.com/abstract=2826228 orhttp://dx.doi.org/10.2139/ssrn.2826228.

Bryan, Mark L. 2007. "Free to Choose? Differences in the Hours Determinationof Constrained and Unconstrained Workers," Oxford Economic Papers, 59(2):226-252.

Conley, Timothy G.; Christopher R. Taber. 2011. "Inference with “Difference inDifferences” with a Small Number of Policy Changes," The Review of Economicsand Statistics, 93(1):113-125.

Dickens, William T.; Shelly J. Lundberg. 1993. "Hours Restrictions and LaborSupply," International Economic Review, 34(1): 169-192.

Goldin, Claudia. 2014. "A Grand Gender Convergence: Its Last Chapter,"American Economic Review, 104(4): 1-30.

REFERENCES 39

Goodman-Bacon, Andrew. 2018. "Difference-in-Differences with Variation inTreatment Timing," NBER Working Papers 25018, National Bureau of EconomicResearch, Inc.

Ham, John C.; Kevin T. Reilly. 2002. "Testing Intertempo-ral Substitution, Implicit Contracts, and Hours Restriction Models ofthe Labor Market Using Micro Data," American Economic Review, 92(4): 905-927.

Johnson, William R. 2011. "Fixed Costs and Hours Constraints," Journal ofHuman Resources, 46(4): 775-799.

Kahn, Shulamit; Keving Lang. 1991. "The Effect of Hours Constraints onLabor Supply Estimates," The Review of Economics and Statistics, 73(4): 605-611.

Kahn, Shulamit; Keving Lang. 1995. "The Causes of Hours Constraints: Evidencefrom Canada," The Canadian Journal of Economics, 28(4a): 914-928.

Lundkvist, Helén; Cecilia Nergårdh; Petra Ulmanen; Lars Wittenmark. 2005."Makt att forma samhället och sitt eget liv jämställdhetspolitiken mot nya mål -Slutbetänkande av Jämställdhetspolitiska utredningen," SOU 2005:66, Stockholm.

Manning, Alan, Barbara Petrongolo. 2008. "The Part-time Pay Penalty foWomen in Britain," The Economic Journal, 118 (February): 28–51.

Meer, Jonathan, Jeremy West. 2016. "Effects of the Minimum Wage onEmployment Dynamics," Journal of Human Resources, 51(2): 500-522.

Moulton, Brent R. 1990. "An Illustration of a Pitfall in Estimating the Effects ofAggregate Variables on Micro Units," The Review of Economics and Statistics,72(2): 334-338.

Pei, Zhuan; Jörn-Steffen Pischke; Hannes Schwandt. 2017. "Poorly MeasuredConfounders are More Useful on the Left Than on the Right," Journal ofBusiness and Economic Statistics, 37(2): 205-216.

Sundström, Marianne. 1991. "Part-Time Work in Sweden: Trends and EqualityEffects," Journal of Economic Issues, 25(1): 167-178.

40 CHAPTER 1

1.A Appendix

Density of Contracted Hours

Figure 1.7: Density of contracted hours0

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Notes: Density distribution of contracted hours for public care workers in full-time municipalities one year before decision and for a random sample of publiccare workers in non full-time municipalities sampled to match the number of publiccare workers in full-time municipalities each year. The x-axis is defined as percentof a full-time contract. All workers with contracts above 100% are pooled in the100% bar. Panel (a) and (b) compares public care workers in actual full-timemunicipalities to non full-time municipalities one year before and five years aftera full-time decision, respectively.

1.A. APPENDIX 41

Figure 1.8: Density of contracted hours

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Notes: Density distribution of contracted hours for public care workers in full-timemunicipalities and for a random sample of public care workers in non full-timemunicipalities sampled to match the number of public care workers in full-timemunicipalities each year. The x-axis is defined as percent of a full-time contract.All workers with contracts above 100% are pooled in the 100% bar. Panel (a)shows the difference in the distribution of contracted hours for public care workersone year before compared to five years after a non decision of full-time. Panel(b) shows the difference in distribution for public care workers one year beforecompared to five years after an actual full-time decision was made. Panel (c) and(d) compares public care workers in actual full-time municipalities to non full-timemunicipalities one year before and five years after a full-time decision, respectively.

42 CHAPTER 1

Figure 1.9: Density of contracted hours before and after decision - differentmunicipality types

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Notes: Density distribution of contracted hours for public care workers in full-timemunicipalities one year before a decision compared to five years after. The x-axisis defined as percent of a full-time contract. Panel (a) shows the distribution ofcontracted hours for public care workers in municipalities that implemented full-time policies as "Free choice of hours" as defined in Section 1.2. Panel (b) shows thedistribution for public care workers in "Partly free choice of hours" municipalitiesand panel (c) shows the distribution for public care workers in municipalities wherethe choice was between working a full-time or part-time contract.

1.A. APPENDIX 43

Main Outcome in Other Sectors

Table 1.8: Main outcome for different sectors

(1) (2) (3)Annual Contracted Share workingearnings hours full-time

Panel A: Public care workers

Short-run (0-3 years) 745 0.46 0.03∗∗∗

(739) (0.28) (0.01)Medium run (4-7 years) 3,082∗∗ 1.33∗∗ 0.06∗∗∗

(1,038) (0.41) (0.01)Long run (8+ years) 3,599∗ 1.45∗∗ 0.07∗∗∗

(1,548) (0.45) (0.01)Observations 3,102,665 3,102,665 3,102,665

Panel B: All other public workers

Short-run (0-3 years) 400 0.17 0.01(582) (0.22) (0.01)

Medium run (4-7 years) -582 -0.07 0.01(936) (0.24) (0.01)

Long run (8+ years) -1,538 0.03 0.01(1,806) (0.33) (0.01)

Observations 5,170,622 5,170,622 5,170,622

Panel C: Public school workers

Short-run (0-3 years) 456 0.28 0.01(627) (0.28) (0.01)

Medium run (4-7 years) 146 0.01 0.01(888) (0.29) (0.01)

Long run (8+ years) -142 0.25 0.01(1,628) (0.34) (0.01)

Observations 3,512,062 3,512,062 3,512,062

44 CHAPTER 1

Panel D: Public child care workers

Short-run (0-3 years) 996 0.12 0.01(819) (0.32) (0.01)

Medium run (4-7 years) 2,025∗ -0.06 0.01(975) (0.34) (0.01)

Long run (8+ years) 2,983 0.23 0.02(2,041) (0.43) (0.01)

Observations 1,561,446 1,561,446 1,561,446

Notes: The results come from the regression equation (1.1) in section 1.3.2. Re-gressions in all panels includes public workers in full-time municipalities that claimto implement the full-time policy for all public workers and public workers in con-trol municipalities. The regressions include municipality and year fixed effects, aswell as controls for local government majority, age, gender, child, and educationaldummies. Annual earnings is expressed in SEK. Contracted hours is defined as per-cent of a full-time contract. Full-time is the share of full-time workers. Standarderrors clustered on the municipality level in parenthesis. ∗ p < 0.05, ∗∗ p < 0.01,∗∗∗ p < 0.001

1.A. APPENDIX 45

Main Outcome for Immediate and Successive Implemen-tation of Policy

Table 1.9: Main outcome for different timing of implementation

(1) (2) (3)Annual Contracted Share workingearnings hours full-time

Panel A: Implementation within a year

Short-run (0-3 years) 2,162∗∗ 0.88∗∗∗ 0.03∗∗∗

(692) (0.26) (0.01)

Medium run (4-7 years) 3,394∗∗∗ 1.38∗∗∗ 0.05∗∗∗

(1,006) (0.31) (0.01)

Long run (8+ years) 2,054 1.48∗∗∗ 0.05∗∗∗

(1,459) (0.40) (0.01)

Observations 2,720,905 2,720,905 2,720,905

Panel B: Successive introduction over five years

Short-run (0-3 years) -564 -0.08 0.02∗

(788) (0.31) (0.01)

Medium run (4-7 years) 2,616∗ 1.24∗ 0.07∗∗∗

(1,230) (0.54) (0.01)

Long run (8+ years) 4,846∗∗∗ 1.38∗ 0.08∗∗∗

(1,419) (0.53) (0.01)

Observations 2,980,055 2,980,055 2,980,055

Notes: The results come from the regression equation (1.1) in section 1.3.2. PanelA only includes public care workers from control municipalities and full-time mu-nicipalities that claim to implement the full-time policies within a year of decision.Panel B only includes public care workers from control municipalities and full-timemunicipalities that claim to implement the full-time policies successively over sev-eral years after decision. The regressions include municipality and year fixed effects,as well as controls for local government majority, age, gender, child, and educa-tional dummies. Annual earnings is expressed in SEK. Contracted hours is definedas percent of a full-time contract. Full-time is the share of full-time workers. ∗

p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001

46 CHAPTER 1

Robustness Tests

Table 1.10: Main outcome - robustness

(1) (2) (3) (4) (5)Annual Contracted Share working Tenure Shareearnings hours full-time leaving

Panel A: Regression on public care workers, excluding controlsShort-run 1,607∗∗ 0.62∗∗ 0.02∗∗∗ 0.11∗ -0.01∗

(0-3 years) (588) (0.22) (0.00) (0.05) (0.00)Medium run 4,208∗∗∗ 1.70∗∗∗ 0.06∗∗∗ 0.30∗∗∗ -0.02∗∗∗

(4-7 years) (1,038) (0.35) (0.01) (0.08) (0.00)Long run 5,098∗∗ 1.91∗∗∗ 0.07∗∗∗ 0.50∗∗∗ -0.02∗∗∗

(8+ years) (1,622) (0.37) (0.01) (0.12) (0.01)Observations 3,963,728 3,963,728 3,963,728 3,963,728 3,736,354Panel B: Regression on public care workers, excluding age controls

Short-run 1,566∗∗ 0.62∗∗ 0.02∗∗∗ 0.10∗ -0.00(0-3 years) (583) (0.22) (0.00) (0.04) (0.00)Medium run 4,280∗∗∗ 1.69∗∗∗ 0.06∗∗∗ 0.29∗∗∗ -0.01∗∗

(4-7 years) (1,011) (0.34) (0.01) (0.08) (0.00)Long run 5,249∗∗ 1.88∗∗∗ 0.07∗∗∗ 0.50∗∗∗ -0.01(8+ years) (1,582) (0.36) (0.01) (0.12) (0.00)Observations 3,958,528 3,958,528 3,958,528 3,958,528 3,958,528

Panel C: Regression on data aggregated to municipality levelShort-run 1,275∗ 0.65∗∗ 0.03∗∗∗ 0.11∗∗ -0.00(0-3 years) (578) (0.22) (0.01) (0.04) (0.00)Medium run 3,655∗∗∗ 1.65∗∗∗ 0.06∗∗∗ 0.27∗∗∗ -0.01∗

(4-7 years) (1,050) (0.38) (0.01) (0.06) (0.00)Long run 4,038∗∗ 1.83∗∗∗ 0.07∗∗∗ 0.49∗∗∗ -0.01(8+ years) (1,463) (0.45) (0.01) (0.10) (0.00)Observations 4,760 4,760 4,760 4,760 4,495

Notes: The results come from the regression equation (1.1) in section 1.3.2. Theregressions include municipality and year fixed effects in Panel A. In Panel B theregressions only exclude age controls. In Panel C the regressions are performedon data collapsed to the municipality level. Annual earnings is expressed in SEK.Contracted hours is defined as the percent of a full-time contract. Tenure is mea-sured in years. Standard errors clustered on the municipality level in parenthesis.∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001

Chapter 2

Hours Constraints and TaxElasticity EstimatesEvidence from Swedish Public Care Workers∗

∗I thank Jonas Cederlöf, Lisa Laun, Jon Olofsson, Martin Olsson, David Seim,Peter Skogman Thoursie and seminar participants at the Center for EconomicBehavior and Inequality at Copenhagen University, and Stockholm University De-partment of Economics for valuable comments and helpful discussions. All errorsare my own.

48 CHAPTER 2

2.1 Introduction

How workers react to income taxes is an important question in theeconomic literature. Knowledge about the tax elasticity is needed fortheoretical labor supply models as well as for deriving optimal in-come tax schedules (see e.g. Diamond and Saez 2011, and Saez 2001).Correct estimation of the tax elasticity is vital for tax policy. How-ever, in the literature on labor supply and taxation, there has beena concern that tax elasticity estimates might be biased in the pres-ence of optimization frictions for workers (see e.g. Chetty et al. 2011,Gelber et al. 2019, Kleven and Waseem 2013, Kleven 2016, Zaresani2019). Such bias can be significant and make the difference betweenan optimal top marginal income tax of ∼56% rather than ∼99%.1Furthermore, the nature of the optimization frictions is important inunderstanding the potential bias in the empirical tax elasticity lit-erature. If workers are constrained in their choice of hours worked,then tax elasticity estimates are downward biased (Chetty 2012). Ifinstead, workers are misinformed about the tax system, the empiricaltax elasticity estimates may not be biased after all.2

Since Saez (2010) showed how to use a bunching estimator to cal-culate the income tax elasticity, several empirical papers have foundthat the tax elasticity is smaller than previously believed.3 It is im-portant to understand if empirical tax elasticities are small because

1Calculated using the top marginal income tax formula from Saez (2001) andthe empirically estimated tax elasticity of 0.001 compared to the tax elasticity of0.4 in a model with optimization frictions in Bastani and Selin (2014).

2Chetty et al. 2011 attribute a lack of bunching around tax kinks to workersbeing hours constrained. If instead, the lack of bunching depends on workers beingmisinformed about the tax system, and this misinformation persists, the estimatedtax elasticity lines up with workers’ long term behavioral response to taxes. Rees-Jones and Taubinsky (2016) show that workers in the US seem to mistake theiraverage tax for their marginal tax.

3Amongst others, Bastani and Selin (2014), Chetty et al. (2011), and Saez(2010) find empirical elasticities of zero for wage earners in Sweden, Denmark,and the US, respectively.

2.1. INTRODUCTION 49

they are biased by optimization frictions, or because workers do notchange their labor supply to a great extent in reaction to taxes. Sofar, there is limited evidence on the nature of these optimization fric-tions. It is not known if optimization frictions should be modeled asa cost to changing hours, or if it should be modeled as lack of infor-mation, or workers not paying attention to their earnings (Søgaard2019). Present literature on tax elasticities either assumes that work-ers face no optimization frictions or, following Chetty et al. (2011),assume that there are frictions but are agnostic about what that theyconsist of.

This paper presents evidence on one potential optimization fric-tion, hours constraints, and its relative importance for tax elasticityestimates. To do this, I use newly collected data on implementationsof so-called "right to full-time" (RTF) policies in Swedish municipal-ities. These policies made some public care workers less constrainedin their choice of hours worked. Taking advantage of these policies,I use a bunching approach to compare tax elasticities between pub-lic care workers with different hours constraints. While much of theliterature that estimates optimization frictions uses tax changes totrack out the total effect of the frictions, this paper uses a changein hours constraints directly to estimate its impact on tax elasticityestimates. Thus, this paper provides new insight into one part of theoptimization frictions black box.

Between the years 2000 and 2013, 99 of Sweden’s 290 municipali-ties decided to implement RTF policies, allowing public care workersto adjust working hours within a certain interval (e.g. within 75-100%of a full-time contract). Importantly, the decision to change hoursworked was entirely up to the worker, and the employer had to ac-commodate that request.

To identify municipalities where public care workers have differenthours constraints I use event study estimation where treatment is thedecision to implement an RTF policy. The results show that public

50 CHAPTER 2

care workers in municipalities that decided to implement RTF poli-cies got contracted hours that were on average 1.8 percentage pointslonger than public care workers in non-RTF municipalities. I take thisas evidence that a significant share of public care workers was con-strained in their choice of hours worked and that the RTF policiessignificantly decreased the cost of adjusting hours.

Because of the way the RTF policies were implemented it is pos-sible to estimate the specific impact of hours constraints on tax elas-ticity estimates. The RTF policies only affected the cost of changinghours worked. The cost of paying attention to one’s earnings did notchange as a result of the RTF policies. Changes to the cost of be-ing informed about the tax system should only occur on the nationallevel. Thus, other optimization frictions should remain constant whencomparing RTF and non-RTF municipalities, making it possible toevaluate the relative importance of hours constraints.

Having identified groups with different hours constraints, I turn tothe main question of how hours constraints impact tax elasticity es-timates. A natural test is to compare bunching around marginal taxkink points between municipalities where public care workers havedifferent costs for adjusting hours and within municipalities, wherethis cost changes over time. The staggered implementation of RTFpolicies makes both of these comparisons possible. Using a bunchingtechnique and a large tax kink, I compare bunching before and afterthe decision to implement an RTF policy as well as bunching in RTFmunicipalities after a decision compared to non-RTF municipalities.Public care workers in RTF municipalities where the cost to adjusthours is lower than in non-RTF municipalities do not display largerelasticity estimates. Furthermore, public care workers in municipali-ties that implement RTF policies do not display increased bunchingas a result of the implementation. In fact, in all cases, the measuredtax elasticities were precisely estimated zeros.

One problem with bunching estimation is that it might be difficult

2.1. INTRODUCTION 51

for workers to precisely target specific annual earnings. In a sensitivityanalysis, in the Appendix, I use two-year panel estimations on a taxchange over time, rather than a cross-section as in the bunching case.By doing this it is possible to measure if workers change their laborsupply differently depending on hours constraints, without the needto target specific annual earnings. I estimate the effect of a marginaltax cut generated by the introduction of the earned income tax credit(EITC) in 2007. Specifically, I measure differences in reaction to thetax cut for public care workers in RTF and non-RTF municipalities.These tests show that there is no discernible difference in reaction toa marginal tax cut between constrained and less constrained workers.However, the sample and the difference in marginal tax is smallerthan in the bunching approach, making the estimate less precise.

The results from both bunching estimates and panel regressions ona marginal tax change indicate that the hours constraints part of theoptimization frictions has a negligible effect on tax elasticity measuresfor public care workers. Thus, if there are optimization frictions thatsignificantly affect tax elasticity estimates, they should come fromother frictions, such as lack of information or attention, not fromhours constraints, for this group of workers.

To my knowledge, this paper is the first to test the relative im-portance of hours constraints for tax elasticity estimates in a settingwhere workers have different hours constraints. Søgaard (2019) eval-uates the importance of different underlying optimization frictionsby using a change in a sharp kink in Danish students’ budget sets.He does not look at hours constraints specifically, but the findingssuggest that rational inattention explains a lack of bunching for thisgroup. However, without looking at hours constraints directly, it isnot possible to confidently reject its importance as an optimizationfriction.

This paper is closely related to the model in Chetty et al. (2011),where hours constraints come from a fixed cost of changing jobs. It

52 CHAPTER 2

also relates to the growing literature that uses changes in the tax sys-tem to estimate optimization frictions. Kleven and Waseem (2013)look at the extent to which workers in Pakistan have earnings instrictly dominated pre-tax regions to establish the existence of opti-mization frictions. Gelber et al. (2019) and Zaresani (2019) both usechanges to kinks in the welfare system, effectively acting as incometaxes, to evaluate the extent to which optimization frictions affect taxelasticity estimates. While they look at the total friction, this paperfocuses on hours constraints. My empirical approach, with the im-plementation of RTF policies, makes it possible to look at the effectof changes to hours constraints while holding all else (information,attention, etc.) constant.

The rest of the paper is organized as follows. Section 2.2 describesthe theory behind hours constraints and its potential bias in tax elas-ticity estimates, as well as previous literature relating to optimizationfrictions. Section 2.3 describes the institutional setting for public careworkers in RTF municipalities, and the income tax system they face.Section 2.4 provides the empirical strategy. Section 2.5 describes thedata and sample selection. Section 2.6 presents evidence on how theRTF policies affect public care workers, while section 2.7 examineshow hours constraints impact tax elasticity estimates. Finally, sec-tion 2.8 concludes.

2.2. THEORY AND PREVIOUS LITERATURE 53

Figure 2.1: Bunching in theory

H1

H3

H2

K

H4

Worker iindifference

curves

Afte

r tax

inco

me:

c =

wh(

1-t)

Before tax income: wh

Notes: Earnings are decided by the wage, w, and hours worked, h. The y-axisrepresents after tax income and the x-axis before tax income. For a fixed wage, theworker decides how many hours to work in order to optimize her utility function(depicted by the indifference curves). A worker draws a job with a fixed set ofhours and earnings, H4. In the absence of a tax, the worker change hours workedin order to reach point H3 in earnings. In the presence of a tax, the after taxincome of the worker decreases to point H2 and the worker optimizes by choosingpoint H1, instead.

2.2 Theory and Previous Literature

To fix ideas I will briefly describe how the labor supply model inChetty et al. (2011) explains how hours constraints might affect em-pirical tax elasticity estimates. This section will have bunching esti-mation as a starting point, even though most of the results can betransferred to other empirical models, such as difference-in-differencesestimations.

Consider a general labor supply model without frictions. Workingyield positive utility from after tax income (consumption) and neg-

54 CHAPTER 2

ative utility from the effort cost of working. If there is a higher taxrate for earnings above a threshold, K, some workers that, in absenceof a tax, preferred earnings above K will decrease their work hoursand bunch at that kink point. Figure 2.1 shows why this is the case.A worker optimizes hours worked and choose earnings H3, in the ab-sence of a tax. When there is a tax, the optimum is H1 instead, theearnings threshold where the tax rate is higher. Since it is at pointK that the value of working an extra hour decreases, there will be anexcess of workers choosing exactly that point when optimizing overhours worked and consumption. This will create bunching of work-ers around that kink point, which can be used to estimate the taxelasticity (see section 2.4.2 for more details).4

The same argument can be made for a worker with contractedhours such that earnings are below the kink, as in point H4. Giventhe opportunity to change hours, and in the absence of a tax, a workerat point H4 will increase hours until reaching point H3. In presenceof a tax at point K the same worker will instead only increase hoursup until point H1 is reached.

By introducing optimization frictions to this model, the tax elas-ticity estimate may become biased. Chetty et al. (2011) show how onepotential optimization friction, hours constraints, create a downwardbias. In the hours adjustment cost model from Chetty et al. (2011)workers search for and draw a random job with a fixed set of hours.For example, in Figure 2.1, the fixed set of hours could lead to earn-ings at point H4, while the optimum amount of hours would be suchthat earnings are at point H1 (H3 in absence of a tax). Firms havea specific hours demand because of a short term commitment to aproduction technology. To change hours to what is preferred, H1, theworker has to pay a fixed cost, φ. The fixed cost is what creates thehours constraint for the worker, and represents the cost of changingjobs to get the preferred hours. This means that a worker will only

4For an overview of the use of bunching, see Kleven (2016).

2.2. THEORY AND PREVIOUS LITERATURE 55

change hours worked to the optimum if the following condition holds;

u(ci(H1), hi(H1)) − u(ci(H4), hi(H4)) > φ, (2.1)

were ci(.) is consumption and hi(.) is hours worked.u(ci(H1), hi(H1)) − u(ci(H4), hi(H4)) is the utility gain for workeri from working the preferred hours, rather than those given by theoriginal contract. That is, only if the utility gain from changinghours is larger than the fixed cost will worker i change hours to H1.Using this model, Chetty et al. (2011) show that because of thehours constraint fewer workers will choose to bunch at the tax kink,which will yield a downward bias in the elasticity estimate.

There are several different potential optimization frictions withpotentially different implications for the bias in elasticity estimates.If hours constraints are important, then firms will change the hoursoffered in the long run, in order to match workers’ demand for hours,making the observed long run (structural) tax elasticity higher thanwhat is observed using the bunching approach. Firms offer a specificset of hours because of a short term commitment to a production tech-nology. In the long run, firms can change this production function tomatch the workers’ demand for hours. If instead, lack of informationabout the tax system is the most important reason why workers do notreact to tax changes, this might have different implications for the ob-served long run tax elasticity, depending on how information spreadsamong workers. If workers stay uninformed their demand for hoursworked will not change with taxes and firms will not change theiroffered hours in the long run. Rees-Jones and Taubinsky (2016) showthat workers in the US react to average taxes, rather than marginaltaxes. This would also lead to a lack of bunching at kink points wherethe marginal tax increases. However, if this misperception of the taxsystem is constant over time, then the estimated tax elasticity cor-rectly estimates the long run reaction to taxes and can still be usedin labor supply models and for estimating optimal income taxes. If

56 CHAPTER 2

inattention is the main optimization friction, workers will still reactto taxes by, e.g., setting an annual earnings target. However, work-ers may miss their target because of inattention to unforeseen events,such as sick days and overtime, which will create a lack of bunching,even though workers adjust their labor supply in response to marginaltaxes. The difference between lack of information, inattention, andhours constraints as optimization frictions makes it important to un-derstand how much each potential underlying optimization frictionaffects tax elasticity estimates.

Earlier literature can shed some light on the question of how im-portant different optimization frictions are for potential bias in taxelasticity estimates. Saez (2010), Bastani and Selin (2014), and Klevenand Schultz (2014) all find larger tax elasticity estimates for self-employed compared to wage earners.5 This could depend on a numberof things. Self-employed might be less constrained in their choice ofhours, they might have better information about the tax system andtheir earnings,6 and they might misreport their earnings so that theirelasticity looks larger than it is. However, Chetty et al. (2011) assumethat self-employed are not constrained in their choice of hours, andit is interesting to note that many of these articles find small elas-ticity estimates also for this group.7 Saez (2010) is an exception inthis case with an elasticity of one, but Saez assumes that much of thelarge elasticity for self-employed depends on how income is reported,rather than actual changes in hours worked. Since we do not knowwhy self-employed have larger elasticity estimates, this in itself is notenough to understand the relative importance of hours constraints.

5Saez (2010) find an elasticity of 1 for self-employed, and 0 for wage earners.Bastani and Selin (2014) find an elasticity of 0.07 for self-employed, and 0.001 forwage earners. Kleven and Schultz (2014) in general find elasticity estimates thatare twice as high for self-employed compared to wage earners.

6For example, if self-employed pay themselves even during sick-days, creatingfewer unexpected earnings shocks.

7Small compared to an elasticity of 0.3 or 0.4 that Chetty et al. (2011) andBastani and Selin (2014) find plausible if hours constraints exist.

2.2. THEORY AND PREVIOUS LITERATURE 57

Kleven and Waseem (2013) look at notches in the Pakistani taxsystem. The notches create strictly dominated pre-tax income regions,where individuals work more for a lower post-tax income. Individu-als who earn income in that region should do so either because itis costly to change hours, because they do not understand the taxsystem (information), or because they miss their target earning level(inattention). In the Pakistani sample, there is a subgroup of indi-viduals who are both wage earners and self-employed. Among them,there is a spike in reported earnings with an exact split between self-employed and labor earnings. Had these individuals just had one per-centage point more labor earnings their average tax would have beencut dramatically. This is suggestive evidence that information aboutthe tax system is an important part of the optimization frictions.More evidence that information is important for tax elasticity esti-mates comes from Chetty et al. (2013). They show that tax elasticityestimates from bunching around tax kinks, created by the US EITC,are higher in counties where knowledge about the EITC kinks arehigher.

Even though evidence from earlier papers suggests that lack ofinformation is an important part of the optimization frictions, theeffect of hours constraints on tax elasticity estimates have not beenthoroughly tested empirically. To my knowledge, Søgaard (2019) isthe first to separate different optimization frictions. He uses a Danishreform to how much university students might earn while simultane-ously receiving student grants. He finds that students react to changesin the earnings threshold but that they do not bunch around the taxkink. This suggests that a rational inattention to annual earnings gen-erates a downward bias in tax elasticity estimates using the bunchingapproach. However, in the model from Chetty et al. (2011) hours con-straints affect those close to a tax kink, since the fixed cost of changinghours is not worthwhile to pay for them. If the tax kink is moved itcould be the case, even with hours constraints, that it becomes worth-

58 CHAPTER 2

while to pay the fixed cost in order to change hours worked. Thus, theevidence in Søgaard (2019) does not reject the model in Chetty et al.(2011) or the possibility of hours constraints affecting bunching esti-mates. In conclusion, there is some evidence in favor of information(Chetty et al. 2013, Kleven and Waseem 2013), inattention (Søgaard2019), and hours constraints (Chetty et al. 2011), but the relativeimportance of these optimization frictions is not known.

2.3 Institutional Setting

2.3.1 The Right to Full-time Policies

Between the years 2000 and 2013, 99 of Sweden’s 290 municipalitiesdecided to implement an RTF policy (see Blomqvist 2020 for a thor-ough review of the RTF policies). These were policies targeting publiccare workers, employed by the municipalities, with the intended effectof reducing involuntary part-time work. The RTF policies were de-signed to make it easier for public care workers to choose how manyhours they wanted to work. In the previous section, I explained howoptimization frictions in the form of hours constraints, in theory, willlead to a downward bias in tax elasticity estimates. The RTF poli-cies should reduce hours constraints for public care workers and can,therefore, be used to test this theory.

The RTF policies stated that public care workers could demanda change in their contracted hours, and the employer had to accom-modate that wish. However, the decisions and subsequent implemen-tations of RTF policies differed from municipality to municipality. Insome cases, all public care workers received a full-time contract andcould take unpaid leave to get back to their original, or any otherpreferred, hours if they wished. In most municipalities, it was notnecessary to demand full-time. A part-time worker on a 70% con-tract could demand an 80% part-time contract, for example. Therewas a lot of heterogeneity in the RTF rules but the decisions can be

2.3. INSTITUTIONAL SETTING 59

divided into three categories. In the first, public care workers couldchoose hours freely between 75-100% of a full-time contract.8 In thesecond, public care workers could choose hours in increments of 5 or10 percentage points between at least 75-100% of a full-time contract.In the third, public care workers could only choose between workingpart-time or full-time. In the third category, it was unclear if therewere several different part-time contracts to choose from. Thus, thiscategory could include municipalities that offered a range of differentcontracted hours. As Table 2.5 in Appendix B shows, half of the mu-nicipalities that decided to implement an RTF policy offered freelyadjustable contracts. Furthermore, Table 2.5 in Appendix B showsthat 56% of the municipalities implemented the RTF policies succes-sively over some years. When testing the theory that reduced hoursconstraints should lead to larger tax elasticity estimates, it is impor-tant to take into account that the RTF policies were not implementedimmediately in over half of the treated municipalities.

All treated municipalities included both present workers and fu-ture hires in the policy. Only thirteen municipalities specified whenworkers could choose their hours worked, and they specified thatworkers should be able to change to their preferred hours of workat least once a year. Altogether, the RTF policies did, at least on pa-per, significantly reduce the constraint of adjusting hours for publiccare workers.9

The relative freedom in the choice of contracted hours is what isimportant when considering the RTF decisions and their effects onhours constraints and tax elasticity estimates. For the municipalities

8This is the minimum requirement to be part of the first category. Some RTFmunicipalities had a wider range where the choice was free, for example from60-100% of a full-time contract.

9The relative freedom of choosing hours after an RTF implementation comesfrom my reading of the municipal council meeting minutes. As such, some decisionsmay be interpreted incorrectly. It is also possible that the reality of implementationdeparts from the writings in the decision process. However, in section 2.6, I do mybest to show that hours constraints are significantly reduced in RTF municipalities.

60 CHAPTER 2

that offered free and partly free adjustable contracts it was also possi-ble to reduce hours worked. For example, a worker on a 100% contractcould change to an 85% contract as a result of the RTF policy. Re-lating this point to the theory of hours constraints and bunching inthe previous section, this means that all workers with full-time earn-ings above a tax kink should be able to bunch at that kink whenthe RTF policy is introduced. The RTF policies make it possible forfull-time workers to cut back on hours, while part-time workers canincrease their hours in order to reach the tax kink, as explained inthe previous section. To the extent that RTF municipalities in thethird group, part-time or full-time, offered several different part-timecontracts, this is true also for that category.

2.3.2 Labor Income Taxation in Sweden

In Sweden, the labor income tax system consists of two main parts, thelocal and the central government taxes.10 All labor income is subjectto a proportional local tax and, for labor incomes above certain levels,there are two central government taxes on top of the local tax. Theproportional local tax varies between municipalities and over time.The difference in taxes between the most extreme municipalities issubstantial, varying from 26.5% to 33.2% in the year 2000. Changesover time have been less dramatic than the difference between mu-nicipalities, with an average local tax of 30.4% in 2000 to 31.7% in2013.

Figure 2.2, panel (a), shows the marginal tax rate on labor in-come in Sweden in 2006. The dashed line points out the marginaltax increase at the first central government kink point. There is abasic deduction that differs slightly with income, which is the reasonwhy the marginal tax is not entirely flat up until the first centralgovernment tax. Except for the increase in the marginal tax just at

10This section relies heavily on Du Rietz et al. 2013, and publicly available taxdata provided by The Swedish Tax Agency and Statistics Sweden.

2.3. INSTITUTIONAL SETTING 61

Figure 2.2: The Swedish labor income tax system

0.2

.4.6

0

5000

0

1000

00

1500

00

2000

00

2500

00

3000

00

3500

00

4000

00

4500

00

5000

00

5500

00

6000

00

(a) Marginal tax rate in Sweden 2006

0

100000

200000

300000

400000

500000

600000

1999 2001 2003 2005 2007 2009 2011 2013

First central government kinkSecond central government kink

(b) Income needed to reach the first centralgovernment kink point

Notes: Panel (a) plots the marginal tax rate in 2006, using the average municipaltax (31.6%), for different labor incomes (expressed in 1999 prices). The dashed linepoints out the first central government kink point. The payroll tax is not includedin this graph. Panel (b) shows the labor income needed to reach the first andsecond central government kink points. The income is expressed in SEK, deflatedby the consumer price index (1999 prices).

the bottom of the income distribution, the first central governmenttax kink yields the largest change of the marginal tax in the Swedish

62 CHAPTER 2

Table 2.1: Marginal tax change at the first central government kink point1999-2013

Year τ1 τ2 log 1−τ11−τ2

Year τ1 τ2 log 1−τ11−τ2

1999 0.366 0.540 0.321 2007 0.316 0.516 0.3462000 0.340 0.530 0.340 2008 0.314 0.514 0.3452001 0.330 0.523 0.340 2009 0.315 0.515 0.3452002 0.317 0.514 0.340 2010 0.316 0.516 0.3462003 0.324 0.520 0.342 2011 0.316 0.516 0.3462004 0.327 0.524 0.346 2012 0.316 0.516 0.3462005 0.322 0.520 0.345 2013 0.317 0.517 0.3462006 0.316 0.516 0.346

Notes: This table shows the yearly marginal tax rate for incomes just be-low (τ1) and above (τ2) the first central government kink, as well as thepercentage jump in marginal net-of-tax rate for workers at the threshold.

labor income tax system.11

Figure 2.2, panel (b), shows the annual earnings needed to reachthe two thresholds where the central government taxes kick in. Laborincome above the lower threshold is taxed with an extra 20 percentagepoints while labor income above the second threshold is taxed withan extra 5 percentage points on top of that. The income needed toreach the tax kinks increases with 2% plus inflation in order to followthe general yearly increase in wages. In 2009 there was a significantjump in both thresholds, decreasing the share of workers with incomesabove them.

Table 2.1 shows the yearly marginal tax rate just below (τ1) andabove (τ2) the first central government kink, as well as the percentagejump in marginal net-of-tax rate for workers at that threshold. Onaverage, there is a 34% change in the marginal net-of-tax rate when

11The figure disregards the payroll tax, which, being proportional, do not affectthe level change in marginal taxes imposed by the other labor income taxes.

2.4. EMPIRICAL MODELS 63

exceeding the threshold. As explained by Bastani and Selin (2014) thefirst central government tax is salient and well-known. However, theremight have been some issues calculating its exact position since thebasic deduction (and, before 2006, the general pension contribution)had to be added to the threshold stated by the Swedish Tax Agency.Two important things to note with the Swedish labor tax system isthat capital is taxed separately from labor income, and spouses payseparate taxes on their income. This will make empirical estimationson the individual level more straightforward.

In 2007 an important change was made to the labor income tax.The center-right government of the time introduced the earned in-come tax credit (EITC). The EITC is a tax reduction scheme wereworkers receive a refund on part of their labor income tax payment.For the years relevant to this paper, 2007-2013, the EITC led to loweraverage labor income taxes for all workers, but only marginal tax re-ductions for middle-income workers. The maximum amount of theEITC increased, due to political decisions from the then center-rightgovernment, every year from 2008 to 2011. However, the EITC did notaffect the marginal tax change at the central government thresholds.In Appendix A, where the marginal tax cut from the EITC is usedto estimate differences in tax elasticities, this tax cut is explained inmore detail.

2.4 Empirical Models

The goal of this paper is to measure if workers that are not constrainedin their choice of hours react differently to tax kinks, compared toworkers that are constrained. To do this, I use the RTF policies, tar-geting public care workers and implemented in a staggered fashion inSwedish municipalities. The RTF policies made public care workersmore free in their choice of hours, at least on paper. Thus, I com-pare the tax elasticity of public care workers in RTF and non-RTF

64 CHAPTER 2

municipalities, using the bunching approach. However, first I needto show that my natural experiment, the RTF policies, made pub-lic care workers less constrained in their choice of hours worked, inpractice. To this end, I run an event study regression on a repeatedcross-section of the same public care workers that are included inthe different bunching estimations. The event study estimation onthe RTF policies works as a first stage to see that the policies hadthe intended effect. The bunching estimation on public care workersin RTF and non-RTF municipalities, to see if workers with differenthours constraints have different tax elasticities, is the main focus ofthe paper.

2.4.1 Event Study Estimation

The outcome of interest in the event study estimation is contractedhours. In order to measure the effect of the RTF policies, I use thefollowing event study model:

Yimt = α+∑n

δnDnimt + µm + µt + γX imt + εimt. (2.2)

This regression will show if there is a shift in the number of con-tracted hours among public care workers around the tax thresholdwhen an RTF policy is introduced. Yimt is the contracted weeklyhours for worker i in municipality m in year t. µm are municipalityfixed effects, µt are year fixed effects, and X imt is a vector of con-trol variables. Dn

imt are dummy variables that equal one when it isn periods to (from) a decision of a full-time policy for worker i inmunicipality m. Thus, δn shows the effect of the policy on Yimt eachperiod compared to the reference period, which is one year before adecision. If δn = 0 for all periods prior to the full-time policy it lendscredibility to the common trends assumption. δn in the periods afterdecision are the variables of interest.

All regressions are carried out using robust standard errors

2.4. EMPIRICAL MODELS 65

clustered at the municipality level. The number of clusters, andtreated clusters, is more than enough to get the correct standarderrors (Bertrand et al. 2004, Conley & Taber 2011).

Since the RTF policies were decided upon in different years for dif-ferent municipalities, the sample is unbalanced in event time. Somemunicipalities will not be present at the endpoints, so these coeffi-cients give unequal weight to municipalities depending on when thedecision to implement the policy was made. As a robustness test, Iwill run the same regression on a sub-sample of municipalities thatare balanced around event time zero.

2.4.2 Bunching Estimation

The theory of using bunching around a tax kink point to estimate thetax elasticity comes from Saez (2010). The idea behind this is simple.Individuals derive utility from after-tax earnings and disutility fromworking more hours or increasing effort. If a tax kink is introducedat a certain level of earnings, some individuals that earn above thatthreshold will re-optimize and start earning exactly at the kink point.

Saez (2010) shows that bunching is proportional to the compen-sated elasticity, e. This elasticity can be measured empirically by usingthe number of individuals that bunch at a tax kink, k, compared tothe number of individuals that would have had earnings at that kinkin absence of the tax change. The elasticity is estimated using theformula:

e(k) = B

k × h0(k) × log(1−τ11−τ2

), (2.3)

where k is the kink point, τ1 is the tax below the kink, and τ2 is thetax above the kink. h0(k) is the counterfactual mass of individualsat the kink point in absence of the tax. B is the number of individ-uals bunching above the counterfactual mass of individuals. Thus, tocalculate the elasticity, both h0(k) and B has to be estimated.

66 CHAPTER 2

Since it is difficult for workers to control their earnings perfectly,empirical estimations of bunching calculate the number of bunchers inan income band around the tax kink, instead of calculating B exactlyat point k. To obtain the counterfactual distribution around the kink,I follow Chetty et al. (2011) and fit a seventh order polynomial to theobserved income distribution, omitting the observed distribution foran income band, [−R, R], around the kink. The data is collapsedinto earnings bins, Zj . The bins have a width of d, in this case, 2,500SEK. For each year, the earnings necessary to reach the kink point issubtracted from the earning bins, such that the earnings bin at thekink point has the value zero. Following Bastani and Selin (2014), mymain estimation will omit an income band around the kink of [-5,000SEK, 5,000 SEK].

The counterfactual number of individuals in each bin, j, is givenby:

Cj = ξ(Zj , R) + εj , (2.4)

where ξ is the seventh order polynomial in Zj , and R are the omittedincome bins around the kink point. To calculate the number of indi-viduals bunching, B, the predicted number of individuals in each bin,Cj , is compared to the actual number of individuals. Since bunchingis calculated using an income band, equation (2.3) has to be changedslightly to estimate the elasticity. Let b = B

ho(k) refer to the excessmass of taxpayer at k. The empirically estimated equivalent is:

b =∑Rj=−R

(Cj − Cj)∑Rj=−R

Cj/(2R+ 1), (2.5)

where∑Rj=−R

Cj is the counterfactual number of individuals inthe income bins [−R, R] around the kink, and

∑Rj=−R

Cj is the ac-tual number of individuals. Thus, the nominator shows the number of

2.4. EMPIRICAL MODELS 67

workers bunching above the counterfactual distribution and the de-nominator shows the number of workers given by the counterfactualdistribution, divided by the number of omitted income bins. Now,using b, it is possible to estimate the elasticity using the followingformula:

e(k) = b

k × log(1−τ11−τ2

), (2.6)

In order to use equation (2.6) to calculate the elasticity, k is ex-pressed in units of d, the binwidth. Standard errors are calculatedusing the bootstrap routine in Chetty et al. (2011).12

The elasticity estimated by this formula is unbiased under theassumption that there are no optimization frictions and no tax avoid-ance or evasion. If adjusting hours worked comes with a fixed cost,the elasticity estimate will be downward biased, as explained in sec-tion 2.2. Estimating tax elasticities using the bunching method, whilechanging the cost of adjusting hours makes it possible to test thistheory.

In my empirical approach, comparing RTF to non-RTF munici-palities, only the cost of adjusting hours will change. If that cost playsan important role in creating a bias in tax elasticity estimates thisshould be visible in the bunching estimation. That is, in my empir-ical model, I set the fixed cost of adjusting hours to zero for sometreated workers, lower it for other treated workers, and let it remainconstant for the control group of workers. If that parameter is impor-tant, treated workers should react differently to tax kinks comparedto untreated workers, even if the model also includes other optimiza-tion frictions. For example, if there is a fixed cost of information inequation (2.1), in section 2.2, setting φ to zero for workers would stilllead to a smaller cost of optimizing, and thus more workers bunching.

12The resamplings are performed 250 times to get the standard errors.

68 CHAPTER 2

Thus, comparing bunching between public care workers in RTF andnon-RTF municipalities will show the impact of hours constraints ontax elasticity estimates.

2.5 Data and Sample

2.5.1 Data Description

The data come from three different sources. The first source is data onthe RTF policies which are collected from municipal council meetingminutes. To find out if and when municipalities decided to implementan RTF policy, I contacted all municipal archives and asked for acopy of the minutes from the municipal council meetings when (if)the decision to implement a full-time policy took place. 91% (265)of Sweden’s municipalities answered. Out of the 265, 99 had decidedto implement such a policy during 2000-2013. From those minutes, Icreate a variable with information on the year when a full-time policywas decided on. Furthermore, I create dummy-variables for differentdecision types (if the municipality offered a free choice of hours or onlyoffered a choice between part-time and full time, and if the decisionwas implemented within a year or successively).

The second source is Statistic Sweden’s registers LISA.13 LISAreports yearly panels of administrative data on all registered res-idents over the age of fifteen. LISA include variables such as age,gender, number of children, and highest achieved education. Further-more, from LISA labor earnings together with unemployment bene-fits, parental leave income, and pension benefits were added together,creating a broad income variable.14 The broad income variable is used

13The "Longitudinal integrated database for health insurance and labour mar-ket studies".

14My data include income from sickness insurance for consecutive spells shorterthan 14 days (since it is included in labor earnings). Long-term sickness insuranceis missing in the data. This is not likely to pose a problem since it is probably notcommon for public care workers on long-term sick leave to reach the first central

2.5. DATA AND SAMPLE 69

for the estimation of bunching around the first central governmentkink point. The basic deduction and the general pension contribu-tion (when applicable) are subtracted from the broad income vari-able. However, private deductions are not, because of a lack of data.The most important deductions are private pension contributions andcommuting expenses (Bastani and Selin 2014). Since capital incomeis taxed separately, deductions for interest expenses do not affect tax-able income and are not included. LISA also reports two-digit industrycodes, which are used to establish if workers are employed in the caresector or not. Care work is defined as being employed in industriesworking with "Human health and social work activities". Thus carework in this setting include elderly care, health care, disability care,and social workers.15

The third source is Statistic Sweden’s "Wage structure statistics"which include yearly panels of administrative data on the full popula-tion of public workers employed by the municipalities. This is used toestablish if workers are public or private employees. The "Wage struc-ture statistics" have a more detailed description of job status, such ascontracted hours and monthly full-time equivalent wage rate, whichis not included in LISA. Contracted hours is measured in percent ofa full-time contract.

All workers with full-time earnings 5,000 SEK below the first cen-tral government tax kink or higher should, in theory, be able to bunchif they can choose hours freely.16 Thus, when an RTF policy is intro-duced, these workers are the ones that should be able to change hourssuch that their earnings reach the tax kink and bunch. To pinpoint

government tax kink.15This is "The Swedish Standard Industrial Classification", or SNI codes. For

the years 1999-2006, the two-digit SNI code 85 includes all care workers in thesample, while the years 2007-2013 have the SNI codes 86-88.

16In the bunching estimation workers earning within 5,000 SEK of the taxkink can be considered a buncher, which is why workers with earnings of 5,000SEK below the first central government tax kink can be considered as potentialbunchers, see section 2.4.2.

70 CHAPTER 2

the workers that should be able to bunch at the kink point I createa dummy variable for "potential bunchers". A worker is a potentialbuncher if full-time broad income is 5,000 SEK below the first centralgovernment tax kink or higher. To see if part-time workers would beable to bunch if they increase their contracted hours to at most afull-time contract I create a full-time earnings variable. The full-timeearnings variable is created using the following formula;

(Broad income) + (Monthly wage) × 12 × (1 − Contracted hours),(2.7)

where contracted hours are equal to one for full-time employees.17 Themonthly (full-time equivalent) wage is used to estimate potential full-time earnings without including overtime pay, pension benefits, etc.,which is included in the broad income variable. For example, a part-time worker on a 50% contract could have a broad income of 132,000SEK and a monthly full-time equivalent wage of 21,000 SEK. In thatcase, full-time earnings would be 132, 000 + 21, 000 × 12 × (1 − 0.5) =258, 000. Note that a monthly full-time wage of 21,000 on a 50%contract would generate annual labor earnings of 126,000. However,the broad income variable includes overtime, pension benefits, etc.,making it possible for the full-time annual wage to deviate somewhatfrom the broad income.

One necessary assumption for the variable to accurately defineactual full-time earnings is that it is possible to keep the same benefits(e.g. unemployment benefit) overtime pay and potential wages fromother employers while increasing the contracted hours to full-time.To make this assumption more plausible when looking at potentialbunchers I define potential bunchers only as workers with contractedhours of at least 50% of a full-time contract. Those workers shouldplausibly be able to change earnings enough to bunch when giventhe opportunity to do so. It is important to note that just because a

17For workers with contracted hours on or above full-time, potential earningsis Broad income, only.

2.5. DATA AND SAMPLE 71

worker is a potential buncher it is not necessarily the case that theworker wants to bunch. Some potential bunchers may already worktheir optimal amount of hours, some may want to work more, but notso much more as to reach the tax kink, etc. However, since it is at thetax kink that the value of working an extra hour decreases, accordingto the theory presented in section 2.2 it will be the case that an excessmass of potential bunchers do want to work such that they exactlyreach the tax kink, given that hours constraints is why they have notchanged hours worked.

2.5.2 Sample Restrictions

For the empirical estimations in the main section, the sample willconsist of repeated cross-sections of public care workers, employed bythe 265 municipalities that answered if they decided to introduce anRTF policy. Workers in the 25 municipalities where it is unknown ifan RTF policy has been introduced are dropped. The reason for usingrepeated cross-sections, rather than a balanced panel of individuals,is that bunching estimation, by nature, uses those individuals that ina certain year are close to a kink or notch. These are not necessarilythe same individuals in different years.

In some municipalities, other sectors than the care sector wereincluded in the RTF policies as well. However, as shown in Blomqvist(2020) public workers in these sectors did not react to the policies.Thus, this sample will only constitute of public care workers in treatedand control municipalities.

In the empirical section, I first show that the RTF policies affectedhours constraints, using an event study estimation, before turning tothe bunching estimations. In order for my sample to be the same inboth estimations, and to make sure that the RTF policies actuallyaffected workers close to the first central government tax kink, I re-strict the sample to only include those public care workers that in aspecific year were at most 50,000 SEK away from the tax kink. Table

72 CHAPTER 2

Table 2.2: Summary statistics for public care workers close to the firstcentral government kink point

RTF municipalitiesMean Sd

Share working full-time 0.69 0.46

Contracted hours 91% 20

Broad labor income 263,000 39,000

Share female 0.81 0.39

Age 47 10

Share with children 0.32 0.47

Share married 0.47 0.50

Share with any college degree 0.61 0.49

Notes: All values are taken the year before an RTF decision. The sampleincludes all public care workers that are employed by the municipalities,and earn within 50,000 SEK of the first central government kink point.Contracted hours is measured in percent of a full-time contract. Broad la-bor income is measured annually in SEK and inflation-adjusted. In 2019, 1USD∼9.5 SEK.

2.2 shows summary statistics of the relevant sample, one year beforeimplementation for the RTF municipalities.

In 2000, around 20% of all taxpayers had labor earnings abovethe first central government kink point. Only 4.4% of all public careworkers employed by the municipalities had labor earnings above thekink point in the same year.18 One year before the RTF policies,the sample of public care workers had a mean broad labor incomeof 263,000 SEK and the tax kink was located at annual earnings of

18For the more narrow sample of public care workers with earnings at most50,000 SEK away from the tax kink, 20% had earnings above the kink in the year2000.

2.5. DATA AND SAMPLE 73

286,000 SEK. In the public care sample, those with earning above thecut-off are usually nurses or social workers, while very few assistantnurses reach the cut-off, even though they constitute the largest shareof the public care workers in the municipalities. One interesting thingto note here is that 80% of the sample consists of women, and halfof the workers in the sample are married. In Chetty et al. (2011)it is shown that married women have a higher tax elasticity thanthe average worker, which indicates that the sample here consists ofworkers that potentially should bunch more than the full Swedishpopulation of taxpayers.

As a robustness check, the event study estimation on the effectof RTF policies and the bunching estimations will be performed onpublic care workers working in their home municipality. The reason forthis sample restriction is to test the importance of using broad incomeas the dependent variable, rather than taxable income (which includesprivate deductions). Deductions for commuting expenses only appliesto those living five kilometers or more from their workplace. Thus, fora sample of public workers working in their municipality of residence,a deduction for commuting expenses are less likely.19

Using the bunching approach on repeated cross-sections comeswith the issue that some public care workers that are included willnot be able to bunch because their full-time earnings will still be belowthe tax kink. Using the bunching approach on a cross-section of onlypotential bunchers will instead create bunching mechanically. Full-time workers with earnings at the tax kink will be potential bunchers(since all workers with full-time earnings at or above the tax kink arepotential bunchers) and they will bunch at the same time, since they

19However, they may still make deductions for private pension contributions.In Chetty et al. (2011), using Danish data, it is shown that private pension contri-butions do not affect the bunching estimate. Furthermore, to make sure that thebroad income measure can pick up bunching I estimate bunching for self-employedworkers with a limited company, a group of workers in Sweden already shown tobunch (Bastani and Selin 2014). Figure 2.20, in Appendix C, shows that my broadincome measure can pick up bunching.

74 CHAPTER 2

are at the kink. Full-time workers just below the kink will not be po-tential bunchers. Thus, just at the tax kink the number of bunchers,measured as potential bunchers, will increase. The fix for this problemis to estimate bunching on repeated cross-sections of the full-sample,while showing how many workers that have full-time earnings abovethe tax kink, and thus have the potential to bunch if they can choosehours freely. As a robustness check on this bunching estimation, Idepart from the repeated cross-section framework and take a sampleof workers who are estimated to be potential bunchers one year be-fore an RTF decision. Then I follow them before and after the RTFdecision to see if they start bunching when given the opportunity todo so. This will alleviate the problem of mechanical bunching for thepotential bunchers, but comes at the cost of losing observations.

2.6 Evidence of Hours Constraints

In this section I show that the natural experiment, the RTF policies,actually succeed in making public care workers less constrained.20

Thus, Figure 2.3 shows the outcome from the event study regression(2.2) in section 2.4.1. This is the effect of the RTF policies on con-tracted hours (measured in percent of a full-time contract), for publiccare workers with broad income within 50,000 SEK of the first centralgovernment tax kink.

The RTF policies led to an average increase in contracted hoursby 1.8 percentage points five years after a decision. Since only 31%worked part-time before the decision, that is an increase of almost 6percentage points for those workers being able to change their hoursupwards, given that downward changes in hours were insignificant.The effect on contracted hours is dynamic, clearly increasing the first

20In a companion paper (Blomqvist 2020), I show that the RTF policies af-fected the whole sample of public care workers in terms of increased earnings andcontracted hours.

2.6. EVIDENCE OF HOURS CONSTRAINTS 75

Figure 2.3: Effect of RTF policies on contracted hours-1

01

23

Con

tract

ed h

ours

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

Notes: The outcome is contracted hours (in percent of full-time). The blue, dottedline represents average treatment effects and the dashed, red lines represent the95% confidence interval. The result comes from the event study regression (2.2) insection 2.4.1, where event time t-1 is the reference period. The regression includesmunicipality and year fixed effects, as well as local government majority, age,gender, education, and children dummies.

five years after the policies took place. Contracted hours exhibit com-mon trends before the RTF policies take place. This is evidence infavor of a causal interpretation of the effects. There could, however,be some potential confounding explanations for this. Even though thecommon trends assumption seems to hold, one could worry about un-derlying demand and supply factors affecting both the RTF decisionand contracted hours. In Blomqvist (2020) I show that this is unlikelysince wages remain the same before and after RTF for the full sam-ple of public care workers. Furthermore, the share of residents overthe age of 65 (those most likely to generate demand for public careworkers) do not change before or after an RTF decision. The other

76 CHAPTER 2

worry is that the effect is driven by sorting. That is, different typesof workers might choose to work in the public care sector as a resultof the RTF policies. However, Figure 2.8 in Appendix B shows that,at least on observables, there does not seem to be any sorting as aneffect of the RTF decisions. Thus, it seems as if the effect of the RTFpolicies comes from workers being able to choose hours more flexibly,rather than the RTF policies affecting the composition of workers.Figure 2.9 in Appendix B shows that the effect does not depend onthe sample being unbalanced in event time.

The increase in contracted hours is evidence of a pre-existing con-straint in public workers’ choice of hours worked. Since nothing elsechanges but the possibility to choose another set of hours worked forthe same employer, the fact that workers react to these policies showsthat the constraint is significantly lower in RTF municipalities.

Before turning to the bunching estimation it is valuable to betterunderstand what happens to contracted hours for public care workersin the sample. To do that I have taken the mean of contracted hoursin income bins of 2,500 SEK 1-5 years after an RTF decision andsubtracted the mean of contracted hours 1-5 years before a decision.21

Figure 2.4 shows the result of this exercise. As already understoodfrom the event study, in general, public care workers within 50,000SEK of the tax kink have higher contracted hours after the RTFdecision. Figure 2.4 also shows that contracted hours mostly increasedbelow the tax kink.

To probe further at the question if the RTF policies made pub-lic care workers more free in their choice of hours worked Figure 2.5shows the distribution of contracted hours. Panel (a) shows the dis-tribution for the sample of public care workers employed five yearsbefore (maroon colored bars) and one year before (uncolored bars)an RTF decision. Panel (b) shows the distribution for the sample ofpublic care workers employed one year before (maroon colored bars)

21This is the same bin size used for the bunching estimation.

2.6. EVIDENCE OF HOURS CONSTRAINTS 77

Figure 2.4: Difference in contracted hours before and after RTF for differ-ent income bins

-8-6

-4-2

02

46

8

Mea

n di

ffere

nce

in c

ontra

cted

hou

rs

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Notes: This graph shows the mean of contracted hours 1-5 years after RTF, sub-tracted by the mean of contracted hours 1-5 years before RTF.

and five years after (uncolored bars) an RTF decision.22

Two things are clear from this exercise. First, fewer workerschanged their contracted hours in the period before the RTF policieswere in place, as evident from panel (a) where there are only smalldifferences in contracted hours five years before compared to oneyear before an RTF policy. Second, the change in contracted hoursafter the introduction of RTF policies seems to have taken place inincrements of five percentage points. There are decreases in contractsat 64, and 75% of full-time and increases in 80, 85, 90, and 99% of afull-time contract (see panel (b)). Given that the average threshold

22Figure 2.5 have excluded contracts on exactly full-time, because that inclusionwill obscure the changes taking place on intervals below. In Appendix B, FigureFigure 2.10 includes the full-time contracts.

78 CHAPTER 2

Figure 2.5: Distribution of contracted hours

0.0

5.1

.15

Den

sity

of w

orke

rs w

ith s

peci

fic c

ontra

cted

hou

rs

50 60 70 75 80 85 90 100contract

Five years before full-timeOne year before full-time

(a) Distribution before a decision

0.0

5.1

.15

Den

sity

of w

orke

rs w

ith s

peci

fic c

ontra

cted

hou

rs

50 60 70 75 80 85 90 100contract

One year before full-timeFive years after full-time

(b) Distribution before/after a decision

Notes: Density distribution of contracted hours for public care workers in RTFmunicipalities. The x-axis is defined as the percent of a full-time contract. InPanel (a) the maroon colored bars show the distribution of contracted hours forpublic care workers five years before a decision. The uncolored bars show thedistribution of contracted hours for public care workers in RTF municipalities oneyear before a decision. Panel (b) shows the distribution of contracted hours forpublic care workers in RTF municipalities one year before (maroon colored bars)and five years after (uncolored bars) a full-time decision, respectively.

2.7. HOURS CONSTRAINTS AND TAX ELASTICITIES 79

value for the kinkpoint is 286,000 SEK, a worker that can reachthat point would be able to change annual earnings by incrementsof 14,000 SEK (when changing contracted hours in increments offive percentage points). In the bunching approach below, the rangeof earnings close to the kink that is used for bunching estimationis 10,000 SEK (20,000 SEK as robustness test) which means thatmost, if not all, workers should be able to change their earnings suchthat they fall within the bunching range.

This section shows that the RTF policies did, in fact, have posi-tive hours worked effect on public care workers with a broad incomeclose to the tax threshold. The question now is if that also meantmore bunching. That is, if the tax elasticity in RTF municipalities isdifferent from tax the elasticity in non-RTF municipalities.

2.7 Hours Constraints and Tax Elasticities

2.7.1 Main Effect

One natural test for the importance of hours constraints and its poten-tial bias when empirically estimating tax elasticities is the bunchingmethod. Elasticities measured from bunching at kink points shouldbe downward biased if hours constraints are important. For example,Bastani and Selin (2014) show that an elasticity of 0.001, estimatedusing the bunching approach, could come from a true elasticity of 0.4if there are hours constraints. If hours constraints is an important op-timization friction, public care workers in RTF municipalities shouldbunch more than public care workers in non-RTF municipalities, sincethe RTF policies significantly decreased hours constraints.

In theory, public care workers should be able to increase or de-crease their contracted hours as a result of the RTF policies. In prac-tice, as shown in the section above, it is only possible to be certain thatthey can increase their contracted hours. That means that all work-ers with full-time earnings that would place them above the kink, but

80 CHAPTER 2

that have an actual broad income below the kink should be able tobunch when allowed to change contracted hours.

There are several ways to measure if the bunching estimate isaffected by hours constraints. It is possible to compare public careworkers in RTF municipalities before and after an RTF decision. Itis also possible to compare public care workers in RTF municipalitiesto public care workers in non-RTF municipalities. In my preferredspecification, I pool public care workers who work in a municipalityone to five years before deciding on an RTF policy. I then pool publiccare workers who work one to five years after deciding on an RTFpolicy. The reason for pooling is to gain more observations, but alsobecause the RTF policies took a few years to have a full effect so it isimportant to measure the outcome a few years after a decision. Thecomparison of workers before and after an RTF decision comes closerto the difference-in-differences ideal than a comparison of workers inRTF and non-RTF municipalities, which is why it is the preferredspecification. Figure 2.6 shows the result of this exercise. The blackline with solid dots is the actual number of workers in each bin, whilethe red solid line is the counterfactual number of workers. The greensolid line shows the number of potential bunchers (workers with full-time earnings of -5,000 SEK or above the tax kink). Since all workerswith actual earnings on or above the tax kink are potential bunchers(they can decrease their hours to reach the kink) there is a mechan-ical increase in potential bunchers just at the kink. Panel (a) showsbunching before RTF is introduced and panel (b) shows bunchingafter RTF is introduced. There is no difference in bunching in munic-ipalities after the introduction of RTF policies. In fact, in panel (b),elasticity estimates above 0.002 can be ruled out with confidence.23

In Figure 2.11, Appendix C, I show yearly (in event time) bunchingestimates. There is no upward trend in bunching as an effect of theRTF policies.

23Calculated using the upper level of the 95% confidence interval.

2.7. HOURS CONSTRAINTS AND TAX ELASTICITIES 81

Figure 2.6: Bunching in RTF municipalities before and after decision

020

0040

0060

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.0029Standard error = 0.0954Implied elasticity = -0.0001

(a) Five to one years before RTF,pooled

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.1668Standard error = 0.1175Implied elasticity = -0.0047

(b) One to five years after RTF, pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: The figures show the income distribution of public care workers aroundthe first central government tax kink. Panel (a) shows the distribution of publiccare workers in RTF municipalities five to one years before an RTF decision andpanel (b) shows the distribution one to five years after the decision. The dottedline shows the true distribution, while the red solid line shows the seventh-orderpolynomial fitted to the distribution with the income band [-5,000 SEK, 5,000SEK] omitted. Each point represents the number of observations within a 2,500SEK bin. The green solid line is the number of potential bunchers. In panel (b)there are 44,000 observations and 12,000 potential bunchers, where 4,250 of thepotential bunchers are located to the left of the kink.

82 CHAPTER 2

One worry could be that there simply are not enough public careworkers who can, or want to, start bunching when the RTF policieslower the cost of adjusting hours. To check this, I count the number ofworkers who should be able to bunch in Figure 2.6, panel (b).24 Theseare the workers with full-time earnings of -5,000 SEK and above. Ifind that approximately 12,000 of the 44,000 public care workers haveearnings and a contracted hours range that would enable them tobunch. 4,250 of the potential bunchers are located to the left of the taxkink. In Appendix C, Figure 2.12 shows how the bunching estimatewould be affected if different shares of the potential bunchers wouldhave chosen to bunch. In panel (b) 10% of the potential bunchers tothe left of the tax kink have their earnings changed such that theybunch. In panel (c) 20% of potential bunchers bunch and in panel(d) 50% of them bunch. Not all potential bunchers want to bunch,because their optimum will be located below or above the tax kink.That is why it is important that this exercise shows that even withonly 10% of potential bunchers to the left of the kink bunching (andnone of the potential bunchers to the right bunching) the effect isvisible, albeit small, in the graph. Thus, there seem to be enoughpotential bunchers to create visible bunching if they would choose tobunch when given the opportunity.

There are two other concerns with this comparison. One is that,in practice, the RTF policies might not have let public care workersadjust hours in small enough intervals to bunch, even though theycould adjust freely on paper. They should, however, be able to comecloser to the bunching threshold. In the previous section, I show thatthe sample of public care workers should be able to change earningsin increments of 14,000 SEK, which should make it possible for allworkers to come within 20,000 SEK of the tax kink if they changehours. In Appendix C, panel (a) and (b) in Figure 2.13 show that thiscomparison is stable to a wider bunching range of +/− 10, 000 SEK

24See section 2.5.2 for a description of how potential bunching is calculated.

2.7. HOURS CONSTRAINTS AND TAX ELASTICITIES 83

around the kink point. The other concern is that in 2009 the earningsnecessary to reach the kink point for the first central governmenttax jumped. This might make it harder to bunch for workers even ifthey get the right to choose hours more freely. Thus, I run the samebunching tests, excluding the years 2009-2013 (see panel (e) and (f)in Appendix C, Figure 2.13). The null result of more bunching forRTF workers is stable for these tests.

2.7.2 Robustness Tests

As mentioned above, another potential comparison of bunching is be-tween public care workers in RTF municipalities after the decision andnon-RTF municipalities, rather than RTF municipalities before andafter a decision. In Appendix C, Figure 2.14 shows these bunchingestimates for different bunching ranges and years. There is no evi-dence of bunching for public care workers in either treated or controlmunicipalities in any of the estimates. Bunching is even lower, butinsignificantly so, in RTF municipalities after the decision (implyingan elasticity of -0.004 in RTF municipalities and -0.001 in non-RTFmunicipalities). Furthermore, it could be the case that the municipal-ities that only offered part-time or full-time contracts did not offer achoice of contracted hours free enough to bunch. Thus, Figure 2.18 inAppendix C, shows the bunching results when only including publiccare workers in municipalities that offered a free choice of hours (asdefined in section 2.3.1). No bunching can be detected for this groupbefore or after the RTF policies. There is also a concern that work-ers may not bunch when looking at broad income, since it includesbenefits which might make calculations of own earnings relative tothe kink harder. They may, however, bunch when looking at annuallabor income, only. Figure 2.19 shows bunching when using only laborincome. Again, there is no bunching detected before or after the RTFpolicies.

84 CHAPTER 2

Figure 2.7: Bunching in RTF municipalities before and after decision, po-tential bunchers

5010

015

020

025

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.2059Standard error = 0.142Implied elasticity = 0.0058

(a) Five to two years before RTF,pooled

5010

015

020

025

030

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.121Standard error = 0.1054Implied elasticity = -0.0034

(b) One to five years after RTF, pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: The figures show the income distribution of public care workers around thefirst central government tax kink for a sub-sample of public care workers that werepotential bunchers one year before an RTF policy decision. Panel (a) shows thedistribution in RTF municipalities five to two years before an RTF decision andpanel (b) shows the distribution one to five years after the decision. The dottedline shows the true distribution, while the red solid line shows the seventh-orderpolynomial fitted to the distribution with the income band [-5,000 SEK, 5,000SEK] omitted. Each point represents the number of observations within a 2,500SEK bin.

2.7. HOURS CONSTRAINTS AND TAX ELASTICITIES 85

As a last robustness check, I zoom in on a sub-sample of thepublic care workers. I take a sample of public care workers who oneyear before treatment has full-time earnings that would enable themto bunch. There are almost 8,000 public care workers with full-timeearnings high enough to bunch in this sample. Then I measure theirearnings relative to the kink point in the same way as before. Thisis a group of workers where everyone can bunch one year before anRTF policy is in place if they can choose hours freely. Given thatthere have not been significant downward changes to their wages orovertime pay, they should be able to bunch in the years after theintroduction of the RTF policy as well, when they are more free tochange their hours worked. Again, there is no evidence of bunchingeither before or after the decision to implement an RTF policy (seeFigure 2.7, panel (a) and (b)). In panel (b) of Figure 2.7 elasticityestimates over 0.002 can be ruled out with confidence also for thissample.25

Comparing bunching between public care workers in RTF munic-ipalities after the decision and non-RTF municipalities or comparingRTF municipalities before and after RTF is introduced yield the sameresult. RTF policies that significantly decrease the hours adjustmentcost for workers have no effect on the estimated tax elasticity usingthe bunching method. In fact, the tax elasticity estimates are pre-cisely measured zeros throughout all estimations. This suggests thathours constraints have a negligible impact on tax elasticity estimatesmeasured using the bunching approach for this sample of public careworkers.

25Figure 2.15 in Appendix C shows that this result is robust to different bunch-ing ranges and choice of years included.

86 CHAPTER 2

2.7.3 Testing Tax Changes Instead of Kinks

Even though Figure 2.5, shows that public care workers seem to beable to choose from a wide set of contracted hours as a result of theRTF decisions, it is still possible that they are not free enough toexactly bunch. Thus, in Appendix A, as a sensitivity analysis, I usea marginal tax change over time, rather than a tax kink, to measurea potential difference in tax elasticities between RTF and non-RTFworkers. With a tax change over time, workers do not need to targeta specific annual earning (as in the bunching case), they only need tobe able to change their hours worked.

In a two-year panel setting, I compare how public care workers inRTF and non-RTF municipalities react to a marginal tax cut in theform of the EITC. The 2007 EITC led to a marginal tax cut of 3 per-centage points for some middle-income workers. The difference in taxelasticities, measured using this tax cut, between public care workersin RTF and non-RTF municipalities was not statistically significant.However, the sample and the difference in marginal tax is smallerthan in the bunching estimate, making the estimate less precise. It isonly possible to reject differences in tax elasticity estimates, betweenRTF and non-RTF workers, over 0.2 with confidence.

2.8 Conclusion

Even though there is a growing concern that optimization frictionsmight lead to biased empirical tax elasticity estimates, and that thenature of the optimization frictions is important for the understandingof potential bias as well, empirical evidence on these frictions is scarce.There are not many instances where it is possible to separate differentoptimization frictions to understand their impact on tax elasticityestimates. Thanks to a unique institutional setting, where some publiccare workers become less constrained in their choice of hours worked,I present evidence on one part of the optimization frictions black box,

2.8. CONCLUSION 87

namely hours constraints. This paper examines if hours constraints,as a potential optimization friction, create a bias in empirical taxelasticity estimates for public care workers.

The results in this paper point to the conclusion that the costof adjusting hours has a negligible impact on tax elasticity estimates.This indicates that if empirical tax elasticity estimates are biased, thisshould stem from other sources of optimization frictions, such as lackof attention or information. This is true for the sample of public careworkers used in this paper and the results may not be transferableto the larger private sector. However, since Chetty et al. (2011) showthat married women have larger tax elasticities than other groups ofworkers, and the public care sector consists of a large share of marriedwomen, arguments could be made that if hours constraints affect taxelasticity estimates, this is a group of workers for which it should bemore, not less, noticeable.

Considering that bias in tax elasticity estimates can make thedifference between a top marginal income tax of ∼56% rather than∼99%, it is important to get a deeper understanding of how differentoptimization frictions affect tax elasticity estimates. Earlier work hasshown that a lack of attention and information affect how workers re-act to taxes. However, how much these channels affect tax elasticityestimates is not well understood. If a lack of information about thetax system is persistent and can explain the lack of bunching, tax elas-ticity estimates are not necessarily biased. If instead, lack of bunchingcan be explained by workers targeting earnings based on taxes butnot paying attention to earnings shocks, tax elasticity estimates willbe biased. Thus, more work is needed to understand to what extentthese channels affect tax elasticity estimates and how persistent theyare.

88 CHAPTER 2

ReferencesBastani, Spencer; Håkan Selin. 2014. "Bunching and non-bunching at kink pointsof the Swedish tax schedule," Journal of Public Economics, 109:36-49.

Bertrand, Marianne, Esther Duflo, Sendhil Mullainathan. 2004. "How MuchShould We Trust Differences-in-Differences Estimates?," The Quarterly Journalof Economics, 119(1): 249-275; MIT Press.

Blomquist, Sören; Håkan Selin. 2010. "Hourly wage rate and taxable laborincome responsiveness to changes in marginal tax rates," Journal of PublicEconomics, 94(11-12):878-889.

Blomqvist, Niklas. 2020. "Essays on Labor Economics - The Role of Governmentin Labor Supply Choices," Chapter 1, dissertation, Stockholm University.

Chetty, Raj; John N. Friedman; Tore Olsen; Luigi Pistaferri. 2011. "AdjustmentCosts, Firm Responses, and Micro vs. Macro Labor Supply Elasticities: Evi-dence from Danish Tax Records," Quarterly Journal of Economics, 126(2):749-804.

Chetty, Raj. 2012. "Bounds on elasticities with optimization frictions: a synthesisof micro and macro evidence on labor supply," Econometrica, 80(3):969-1018.

Chetty, Raj; John N. Friedman; Emmanuel Saez. 2013. "Using Differences inKnowledge across Neighborhoods to Uncover the Impacts of the EITC onEarnings," American Economic Review, 103(7):2683-2721.

Conley, Timothy G.; Christopher R. Taber. 2011. "Inference with “Difference inDifferences” with a Small Number of Policy Changes," The Review of Economicsand Statistics, 93(1):113-125.

Diamond, Peter; Emmanuel Saez. 2011. "The Case for a Progressive Tax: FromBasic Research to Policy Recommendations," Journal of Economic Perspectives,25(4):165-190.

Du Rietz, Gunnar, Dan Johansson, Mikael Stenkula. 2013. "Swedish LaborIncome Taxation (1862–2013)," IFN Working Paper No. 977, 2013

Gelber, Alexander M. 2014. "Taxation and the Earnings of Husbands andWives: Evidence from Sweden," Review of Economics and Statistics, 96(2):287-305.

Gelber, Alexander M.; Damon Jones; Daniel W. Sacks. 2019. "EstimatingEarnings Adjustment Frictions: Method and Evidence from the Social Security

REFERENCES 89

Earnings Test," NBER Working Paper No. 19491.

Kleven, Henrik Jacobsen; Mazhar Waseem. 2013. "Using Notches to UncoverOptimization Frictions and Structural Elasticities: Theory and Evidence fromPakistan," Quarterly Journal of Economics, 128(2):669-723.

Kleven, Henrik Jacobsen; Esben Anton Schultz. 2014. "Estimating TaxableIncome Responses Using Danish Tax Reforms," American Economic Journal:Economic Policy, 6(4):271-301.

Kleven, Henrik Jacobsen. 2016. "Bunching," Annual Review of Economics,8(1):435-464.

Meer, Jonathan; Jeremy West. 2016. "Effects of the Minimum Wage onEmployment Dynamics," Journal of Human Resources, 51(2): 500-522.

Moulton, Brent R. 1990. "An Illustration of a Pitfall in Estimating the Effects ofAggregate Variables on Micro Units," The Review of Economics and Statistics,72(2): 334-338.

Piketty, Thomas; Emmanuel Saez; Stefanie Stantcheva. 2014. "Optimal Taxationof Top Labor Incomes: A Tale of Three Elasticities," American EconomicJournal: Economic Policy, 6(1 B):230-271.

Rees-Jones, Alex; Dmitry Taubinsky. 2016. "Measuring “Schmeduling”," NBERWorking Papers 22884, National Bureau of Economic Research, Inc.

Saez, Emmanuel. 2001. "Using Elasticities to Derive Optimal Income Tax Rates,"The Review of Economic Studies, 68(1):205-229.

Saez, Emmanuel. 2010. "Do Taxpayers Bunch at Kink Points?," AmericanEconomic Journal: Economic Policy, 2(3):180-212.

Søgaard, Jakob Egholt. 2019. "Labor supply and optimization frictions: Evidencefrom the Danish student labor market," Journal of Public Economics, vol. 173,issue C, 125-138.

Zaresani, Arezou. 2019. "Adjustment Costs and Incentives to Work: Evidencefrom a Disability Insurance Program," IZA DP No. 12136.

90 CHAPTER 2

2.A Appendix

2.A.1 Sensitivity Analysis - Two-year Panels

In this section, I use two-year panel estimation to see if workers inRTF and non-RTF municipalities react differently to a tax cut in theform of the Swedish Earned Income Tax Credit (EITC). The mainestimation used the bunching approach, but causal effects estimatesmight be biased as well in the presence of hours constraints. Thus, asa sensitivity analysis, this section runs estimations on a tax changeover time. First, section 2.A.2 describes the Swedish EITC. Section2.A.3 describes the sample restrictions, while section 2.A.4 providesthe empirical strategy. Section 2.A.5 presents the results on how theRTF policies affect public care workers, and section 2.A.6 examineshow hours constraints impact tax elasticity estimates in a two-yearpanel setting.

2.A.2 The Swedish EITC

The Swedish EITC was first introduced in January 2007 by the newlyelected center-right government. With the introduction of the EITCand, at the same time, lowering of unemployment benefits, the center-right government wanted to increase labor supply. The EITC is struc-tured to increase labor supply both on the extensive and intensivemargin. Just as the EITC in the US, it has a phase-in region wherethe tax reduction in SEK increases. Unlike the US EITC, the Swedishone did not have a phase out region when it was introduced. Also un-like in the US, everyone with labor earnings qualifies for the SwedishEITC. There is no need to have children, or even file for it. The phase-in of the Swedish EITC meant that labor earnings between 123, 000and 306, 000 SEK, in 2007, received a marginal tax rate cut of threepercentage points.26 Workers earning over 306, 000 SEK still got a

26Note that these earnings levels change slightly depending on the municipalitytax rate. However, the difference is not very large, and the municipality tax rates

2.A. APPENDIX 91

tax reduction, but their marginal tax was unaffected. Important forthe panel estimation, described below, there was an EITC of sorts inplace during the years 2000-2002.27 This EITC affected workers withearnings of up to 245, 000 SEK. Because of that early EITC, and therisk of 2003 being an "adjustment year" to the removal of the earlyEITC, the panel estimations for the tax cut will only have placeboregressions where 2004 is the earliest base year.

To react to the EITC, workers had to know about its existence.According to a survey by the Swedish National Audit Office (2009),made in October 2009, 45% of workers knew about the EITC. Evenmore important, as mentioned in the main text, in a model with botha cost to changing hours and a cost of getting information about thetax system, we should still observe a difference between workers thatare unconstrained and workers that are constrained. If the cost ofchanging hours decrease, the relative value of information about thetax system increases, and more workers will pay the information cost.Thus, if hours constraints is an important part of why optimizationfrictions lead to biased tax elasticity estimates, this should be visi-ble in the empirical estimation, even in a model that includes a costof information. Tax elasticity estimates between constrained and un-constrained workers should be similar only if the information cost ismuch larger than the cost of changing hours or if both the informa-tion cost and the cost of changing hours have an insignificant effecton tax elasticity estimates. In either case, it is possible to estimatethe importance of hours constraints specifically.

Furthermore, the EITC was known in advance, since it was themain election promise of the winning right-wing alliance. This gaveworkers in the public sector, in municipalities that had introducedRTF policies, plenty of time to demand a change in hours worked forthe coming year 2007 when the EITC was introduced.

are relatively stable.27See Du Rietz et al. 2013

92 CHAPTER 2

2.A.3 Sample Restrictions

The data used here is described in the main section. However, forthe panel estimation below, there are some differences in the samplebeing used. Just as in the bunching analysis the goal is to compareworkers in RTF municipalities to workers in non-RTF municipalities.The estimation of interest is not the general effect of the marginal taxcut from the EITC, but the difference in reaction to this marginal taxcut between workers with different hours constraints. Thus, only thoseworkers that receive a marginal tax cut are included in the sample.

For a specific two-year panel, the sample consists of workers that inthe first year of the panel work in the public care sector, employed bya municipality, and have earnings that would entitle them to the 2007marginal tax cut if it had been implemented that year. For public careworkers, those with earnings in the 13th to the 95th percentile receivea marginal tax cut in 2007. Thus, for each two-year panel, workerswho in the base year are part of the 13-95th percentiles are includedin the sample. As long as a worker is included in the base year, thatworker will also be included in the end year of the sample, even ifthe worker is unemployed or has changed employer.28 The sample isdecided depending on the first year of the panel to avoid endogeneityproblems, since the marginal tax cut might affect earnings. Since theSwedish EITC is introduced in 2007, the sample is also restricted topanels were the base years are 2000-2006.

Two main regressions are performed. One to measure the effect ofthe RTF policies, and one to measure the difference in reaction to themarginal tax cut between workers in RTF and non-RTF municipali-ties.

For the first regression, treatment is decided in the base year.Workers who in the first year of the two-year panels work for a mu-nicipality that has not yet, but will introduce an RTF policy before

28Even those who in the end year of a panel work in a municipality where it isunknown if an RTF policy have been introduced are included in the sample.

2.A. APPENDIX 93

the end year of the panel are treated. Workers who in the first year ofthe two-year panels work for a municipality that has not and will notintroduce an RTF policy before the end year of the panel are in thecontrol group. Workers who work for a municipality that has alreadyintroduced an RTF policy before the first year of the panel are alsoincluded in the control group. This can be viewed as a before-aftercomparison of earnings and hours worked between two groups whereone group receives a cut in the cost of changing hours, which willshow the effect of introducing an RTF policy.

The second regression also has the base year decide treatment. Inthis regression, a worker is treated if she works for a municipality thathas introduced an RTF policy already in (or before) the first year ofthe two-year panel. A worker belongs to the control group if she worksfor a municipality that has not introduced an RTF policy and will notintroduce one before the end year of the panel. In this regression, allworkers receive a marginal tax cut, while treatment is having a lowercost of adjusting hours. Thus, the difference between the treatmentand control group will show the difference in tax elasticity estimatesbetween workers with different hours adjustment costs.

2.A.4 Two-year Panel Estimation

The goal of this sensitivity analysis is to estimate the difference inreaction to a marginal tax cut between constrained and unconstrainedworkers. To fix ideas, let’s consider the following equation:

ln(Eit) = β0 + β1RTFi × EITCt + β2RTFi

+ β3EITCt + uit, (2.8)

where RTF is one in all municipalities where a full-time policy is inplace, and zero otherwise. EITC is one in all periods from 2007 andafter, when it has been introduced, and zero otherwise. By only follow-

94 CHAPTER 2

ing individuals with earnings in a range that give them a marginal taxcut, I restrict the sample to two groups. Those in the treatment groupcan change hours worked for a smaller cost than those in the controlgroup. Both groups will receive a marginal tax cut. β1 is the estimateof interest, which is the effect of receiving a marginal tax cut in theform of the EITC, while working in an RTF municipality, comparedto workers in non-RTF municipalities. However, this is not possible todo since the implementation of RTF policies happened continuouslyover the years 2000 and forward. Thus, RTFi changes over time. In-stead, I will follow Gelber (2014) and create several two-year panelsand run first differences regressions, to remove individual-level fixedeffects that may be correlated with the outcome variable of interest.

First I test if the two-year panel estimation approach also yieldssignificant effects for the introduction of RTF policies on earnings.Then I test if those who work in an RTF municipality before theintroduction of an EITC reacts differently to the marginal tax cutthan those in non-RTF municipalities. By itself, this can not be seenas a causal effect, since RTF and non-RTF municipalities might bedifferent. Thus, as a placebo test, I run regressions comparing thereaction to placebo introductions of an EITC in RTF and non-RTFmunicipalities. The base year of the two-year panels always decidestreatment status to avoid endogeneity problems. Individuals who areemployed by a municipality and work in the public care sector in thefirst year of each panel are included in the sample.

To measure the effect of the RTF policies I estimate the followingfirst difference model:

∆ln(Eit) = β0 + β1∆RTFit +XiT + uit, (2.9)

where ∆ln(Eit) refers to changes in log earnings for individual i inperiod t.29 XiT represents age, gender, number of children under six-

29In order to not have missing values where there should be zeros, earnings isincreased by one (hundred) SEK before taking logs; ln(1 +Eit). The same regres-

2.A. APPENDIX 95

teen, and education fixed effects, and linear control for virtual income,all measured in the base year. β1 is the percentage change in incomethat comes from working in a municipality that introduces an RTFpolicy, which is the estimate of interest.

For the estimation of the difference in reaction to a marginal taxcut between workers in RTF and non-RTF municipalities, considerequation (2.8). In a setting with two years, taking the first differenceof equation (2.8), ∆EITCt will be equal to one for all observations,∆RTFi will be zero for all,30 while ∆(RTFi × EITCt) will be zerofor workers in non-RTF municipalities and one for workers in RTFmunicipalities. Taking the first difference of equation (2.8) will resultin the following regression:

∆ln(Eit) = β0 + β1∆(RTFi × EITCt) +XiT + uit, (2.10)

where β1 is the estimate of interest. It shows the effect of working in amunicipality with an RTF policy while receiving a tax cut. However,since RTF status changes in some municipalities, there is a risk ofconfounding the effect of receiving a marginal tax cut while workingfor an RTF municipality with the effect of the introduction of an RTFpolicy. Thus,XiT now also controls for working for a municipality thatintroduces an RTF policy during the years covered in the panel. Thismeans that the estimated effect is only for those workers that alreadyin the first year of the panel work for an RTF municipality.

In the specifications above there is a risk that the evolution ofearnings changes is different for the treatment and control group.To control for this, I use the evolution of earnings in the income

sions are performed with a hyperbolic transformation of the log earnings, as wellas adding 0.01 instead of 1 to the earnings before taking the log, and lastly, adding0 before taking logs. The results are robust to these different log transformations.Furthermore, I run the same regression with the change in contracted hours as thedependent variable. The results are in line with the estimated earnings effect.

30RTF will either take the value 0 in both periods or 1 in both periods.

96 CHAPTER 2

distribution from a one year-earlier period. Following Gelber (2014)I run the following regression:

∆ln(Eit) = γ0 + f [ln(Eit−1)]γE +XiT + vit, (2.11)

where f is a ten-piece spline in lagged log earnings with knots atthe deciles. XiT represents the same control variables as above, butnow also include municipality fixed effects. γE represents how incomeevolves in earlier periods when the tax has not changed. For the laterperiods I partial out this predicted effect of base year earnings byresidualizing the log earnings variable:

∆ln(Eit) = ∆ln(Eit) − f [ln(Eit−1)]γE . (2.12)

Then I re-run equations (2.9) and (2.10), using the variation in thechange of log earnings that is left after the predicted effect of laggedearnings is removed, ∆ln(Eit), as the dependent variable.

2.A.5 Hours Constraints in a Two-year Panel Setting

Table 2.3 shows the effect of the RTF policies from different regressionspecifications and sample restrictions. Column (1) and (2) in table 2.3,comes from pooled panel regressions, equation (2.9) above, where baseyear and end year are one year apart. Column (3) and (4) in the sametable use the same model, but where base year and end year are twoyears apart. Column (2) and (4) show results from regressions onresidualized log earnings outcomes, as explained above. All repeatedtwo-year panels with start year from 2000 to 2006 are pooled.

2.A. APPENDIX 97T

able

2.3:

Effectof

RTFon

logearnings

(1)

(2)

(3)

(4)

Pooled

two-

Pooled

two-

Pooled

two-

Pooled

two-

year

pane

ls-

year

pane

ls-

year

pane

ls-

year

pane

ls-

oneyear

apart

oneyear

apart,

twoyearsap

art

twoyearsap

art,

resid

ualiz

edresid

ualiz

ed

Pane

lA:E

ffect

ofRT

Fpo

licies

Unc

onstrained

0.01

1∗0.01

2∗0.01

9∗0.01

9∗(0.005

0)(0.005

0)(0.008

6)(0.008

6)

N(T

reated

)34

,382

34,382

100,36

710

0,36

7

Pane

lB:P

lacebo

effects

Unc

onstrained

0.00

30.00

3-0.011

-0.010

(0.005

8)(0.005

7)(0.007

7)(0.007

7)

N(T

reated

)24

,798

24,798

80,629

80,629

N98

8,75

898

8,75

81,11

2,72

71,11

2,55

4

Notes:L

ogearnings

outcom

esfrom

first

diffe

renceregressio

ns.I

ncluding

allm

unicipalities.B

aseyear

decide

treatm

ent.

PanelA

show

stheeff

ectof

RTF

polic

ieson

earnings.Pa

nelB

show

stheresults

from

thesame

type

ofregressio

n,bu

twith

treatm

entbe

ingworking

foramun

icipality

that

will

introd

ucean

RTF

polic

yin

thenear

future.S

tand

arderrors

clusteredat

themun

icipality

levelinpa

renthesis

.∗p<

0.05,∗

∗p<

0.01,∗

∗∗

p<

0.00

1

98 CHAPTER 2

Panel A of table 2.3 shows that one year after the introduction ofRTF policies earnings increased with one percent, and two years afterit had increased by two percent. If workers had not been constrained intheir choice of hours worked before the introduction of RTF policies,earnings would not have changed. These short-term effects are in linewith the event study effects on the RTF policies in my companionpaper, Blomqvist (2020). Thus, this is evidence in favor of publicworkers being constrained in their choice of hours worked and thatthe RTF policies significantly reduced that constraint.

Panel B of table 2.3 shows results from the same regressions as inPanel A, but where treatment is working for a municipality that willimplement an RTF policy in the near future (one to three years afterthe end year of each panel). This can be viewed as placebo regressions,testing if RTF municipalities had different trends from non-RTF mu-nicipalities before the implementation of the RTF policies. As shownin Panel B, no placebo regression is statistically different from zero,and the point estimates are smaller than the point estimates of theactual effects in Panel A. These results strengthen the claim that theresults in Panel A come from the actual policy and not some inter-mediary unobserved variable.

2.A. APPENDIX 99

Table 2.4: Difference in tax elasticity estimates for unconstrained and con-strained workers

(1) (2) (3)2004-2005 2005-2006 2006-2007

Panel A: Controls

Unconstrained× 0.049 0.022 0.040Tax Cut (0.118) (0.105) (0.077)

Panel B: Residualized

Unconstrained× 0.077 0.108 0.079Tax Cut (0.120) (0.097) (0.072)

N 164,066 164,047 163,015N (Treated) 3,324 3,765 3,656

Notes: Results expressed as tax elasticities. Including education dummies,controls for demographic characteristics, and virtual income. Column (1)-(2)are placebo regressions. Standard errors clustered on the municipality levelin parenthesis. ∗ p < 0.05, ∗∗ p < 0.01, ∗∗∗ p < 0.001

2.A.6 Hours Constraints and Tax Elasticities in a Two-year Panel Setting

In this section, I turn to evaluate the effect of hours constraints ontax elasticity estimates in the case of tax reforms across years usingthe introduction of the Swedish EITC in 2007. I use two-year panelsto estimate if public workers in RTF municipalities exhibit differenttax elasticity estimates than public workers in non-RTF municipali-ties. The results from regression (2.10) is shown in Table 2.4. PanelA shows the results from a first differenced regressions while PanelB shows the results from the same regressions, but with the outcomevariable residualized to account for different income trends. Columns(1) and (2) are placebo effects. None of the placebo regressions are

100 CHAPTER 2

statistically different from zero. This reinforces the claim that theeffect in column (3) can be interpreted as the causal effect on taxelasticity estimates for workers that have received a significant reduc-tion in its hours constraints. The actual effect of receiving a tax cutwhile being less constrained is close to zero and not statistically sig-nificant. Running the regression on a residualized outcome does notchange this finding (Panel B).

These results point to the same conclusion as for the bunching es-timate in the main analysis. It seems as even though hours constraintsdo exist it does not have a significant impact on tax elasticity esti-mates. This holds for both bunching and when using tax changes overtime to estimate the elasticity. However, while the bunching approachcould reject elasticity estimates over 0.002, the panel regressions canonly reject differences in elasticity estimates over 0.2 with confidence.

2.B. APPENDIX 1012.B

App

endix

Tab

le2.

5:Ty

peof

RTFpolicy

Free

choice

Partly

free

choice

Part-tim

eor

ofho

urs

ofho

urs

Full-tim

eAll

Shareof

full-tim

emun

icipalities

0.49

0.15

0.36

1

Shareintrod

ucingfull-tim

e:with

in1year

0.59

0.42

0.27

0.44

successiv

elyover<5years

0.41

0.58

0.73

0.56

Notes:Mun

icipalities

arecoun

ted

asprovidingFree

choice

ofho

ursif

itis

atleastpo

ssible

tochoo

seho

ursfreely

with

inan

interval

of75-100%

ofafull-tim

econtract.P

artly

free

choice

ofho

ursmeans

that

workers

canchoo

secertain

intervals(e.g.intervals

of5%

offull-tim

e).P

art-tim

eor

Full-tim

emeans

that

workers

canchoo

sebe

tweenon

lythose.

ForPart-tim

eor

Full-tim

e,itisoftenun

clearifpa

rt-tim

eisfix

ed,o

rifitispo

ssible

tochoo

sebe

tweenseverald

ifferent

part-tim

econtracts.

Thu

s,this

columninclud

esworkers

that

areprob

ably

morefree

intheirchoice

ofho

ursthan

just

choo

sing

betw

eentw

ofix

edcontracts.

102 CHAPTER 2

Figure 2.8: Effect of RTF policies on sorting-.0

4-.0

20

.02

.04

Shar

e ha

ving

chi

ldre

n

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

(a) Share having children

-.04

-.02

0.0

2.0

4

Shar

e w

omen

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

(b) Share women

-.04

-.02

0.0

2.0

4

Shar

e hi

ghly

edu

cate

d w

omen

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

(c) Share highly educated women

-1-.5

0.5

1

Age

in y

ears

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

(d) Age in years

Notes: The blue, dotted line represents average treatment effects and the dashed,red lines represent the 95% confidence interval. The results come from the eventstudy regression (2.2) in section 2.4.1, where event time t-1 is the reference period.The regression includes municipality and year fixed effects.

2.B. APPENDIX 103

Figure 2.9: Effect of RTF policies on contracted hours, balanced in eventtime

-10

12

3

Con

tract

ed h

ours

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

(a)

-10

12

3

Con

tract

ed h

orus

-7 -6 -5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

(b)

Notes: Outcome is contracted hours (in percent of full-time). The blue, dottedlines represent average treatment effects and the dashed, red lines represent the95% confidence interval. The results come from the event study regression (2.2)in section 2.4.1, where event time t-1 is the reference period. The regression in-cludes municipality and year fixed effects, as well as local government majority,age, gender, education, and children dummies. In panel (a), treated municipalitiesoutside the years 2002-2010 are excluded in order for event time -3 to 3 to includethe same number of treated municipalities. In panel (b), treated municipalitiesoutside the years 2003-2009 are excluded in order for event time -4 to 4 to includethe same number of treated municipalities.

104 CHAPTER 2

Figure 2.10: Distribution of contracted hours

0.2

.4.6

.8D

ensi

ty o

f wor

kers

with

spe

cific

con

tract

ed h

ours

50 60 70 75 80 85 90 100contract

Five years before full-timeOne year before full-time

(a) Distribution before a decision

0.2

.4.6

.8D

ensi

ty o

f wor

kers

with

spe

cific

con

tract

ed h

ours

50 60 70 75 80 85 90 100contract

One year before full-timeFive years after full-time

(b) Distribution before/after a decision

Notes: Density distribution of contracted hours for public care workers in RTFmunicipalities. The x-axis is defined as percent of a full-time contract. In Panel(a) the maroon colored bars show the distribution of contracted hours for publiccare workers five year before decision. The uncolored bars show the distributionof contracted hours for public care workers in RTF municipalities one year beforea decision. Panel (b) shows the distribution of contracted hours for public careworkers in RTF municipalities one year before (maroon colored bars) and fiveyears after (uncolored bars) a full-time decision, respectively.

2.C. APPENDIX 105

2.C Appendix

Figure 2.11: Bunching in RTF municipalities over time

-.04

-.02

0.0

2.0

4

Elas

ticity

est

imat

e

-5 -4 -3 -2 -1 0 1 2 3 4 5Event time in years

Notes: Elasticity estimates using the bunching approach in RTF municipalities inthe years before and after an RTF decision. Each point represent a single bunchingestimate for all RTF municipalities in the specific event time given by the x-axis.

106 CHAPTER 2

Figure 2.12: Bunching in RTF municipalities after decision with "forced"bunching

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.1668Standard error = 0.1175Implied elasticity = -0.0047

(a) One to five years after RTF,no forced bunching

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.4975Standard error = 0.1273Implied elasticity = 0.0141

(b) One to five years after RTF,10% bunch

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 1.176Standard error = 0.1381Implied elasticity = 0.0332

(c) One to five years after RTF,20% bunch

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 3.307Standard error = 0.1764Implied elasticity = 0.0934

(d) One to five years after RTF,50% bunch

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: The figures show the income distribution of public care workers around thefirst central government tax kink. Panel (a) shows the distribution of public careworkers in RTF municipalities one to five years before an RTF decision. Panels(b)-(d) shows the same distribution but where different percent of the potentialbunchers have been given earnings such that they bunch. In panel (b) 10% ofpotential bunchers bunch, in panel (c) and (d) 20% and 50% of potential bunchersbunch, respectively. The dotted line shows the true distribution, while the redsolid line shows the seventh-order polynomial fitted to the distribution with theincome band [-5,000 SEK, 5,000 SEK] omitted. Each point represents the numberof observations within a 2,500 SEK bin. There are 44,000 observations and in panel(a) there are 4,250 potential bunchers to the left of the tax kink.

2.C. APPENDIX 107

Figure 2.13: Bunching in RTF municipalities before and after decision0

2000

4000

6000

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = 0.0463Standard error = 0.214Implied elasticity = 0.0013

(a) Five to one years beforeRTF, pooled

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.3844Standard error = 0.2254Implied elasticity = -0.0109

(b) One to five years after RTF,pooled

Bunching range +/− SEK 10,000 (+/− 4 bin points)

010

0020

0030

0040

0050

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.0284Standard error = 0.1134Implied elasticity = -0.0008

(c) Four to one years beforeRTF, pooled

010

0020

0030

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.135Standard error = 0.1328Implied elasticity = -0.0038

(d) One to four years after RTF,pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

010

0020

0030

0040

0050

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = 0.0337Standard error = 0.0969Implied elasticity = 0.0010

(e) Five to one years beforeRTF, pooled

050

010

0015

0020

0025

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.2209Standard error = 0.119Implied elasticity = -0.0062

(f) One to five years after RTF,pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: Panels (e) and (f) only includes observations up until year 2009. The figuresshow the income distribution of public care workers around the first central gov-ernment tax kink. The dotted line shows the true distribution, while the red solidline shows the seventh-order polynomial fitted to the distribution with the incomeband [-5,000 SEK, 5,000 SEK] or [-10,000 SEK, 10,000 SEK] omitted. Each pointrepresents the number of observations within a 2,500 SEK bin. The green solidline is the number of potential bunchers.

108 CHAPTER 2

Figure 2.14: Bunching in non-RTF and RTF municipalities0

1000

020

000

3000

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.0426Standard error = 0.0462Implied elasticity = -0.0012

(a) 2000-2013, pooled, non-RTFworkers

020

0040

0060

0080

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.1281Standard error = 0.1059Implied elasticity = -0.0036

(b) 2000-2013, pooled, RTFworkers

Bunching range +/− SEK 5,000 (+/− 2 bin points)

010

000

2000

030

000

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.1581Standard error = 0.0817Implied elasticity = 0.0045

(c) 2000-2013, pooled, non-RTFworkers

020

0040

0060

0080

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.1137Standard error = 0.2013Implied elasticity = 0.0032

(d) 2000-2013, pooled, RTFworkers

Bunching range +/− SEK 10,000 (+/− 4 bin points)

050

0010

000

1500

020

000

2500

0

Num

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.0456Standard error = 0.0533Implied elasticity = -0.0013

(e) 2000-2008, pooled, non-RTFworkers

010

0020

0030

0040

0050

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.1062Standard error = 0.1477Implied elasticity = -0.0030

(f) 2000-2008, pooled, RTFworkers

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: The figures show the income distribution of public care workers around thefirst central government tax kink. The dotted line shows the true distribution, whilethe red solid line shows the seventh-order polynomial fitted to the distribution withthe income band [-5,000 SEK, 5,000 SEK] or [-10,000 SEK, 10,000 SEK] omitted.Each point represents the number of observations within a 2,500 SEK bin.

2.C. APPENDIX 109

Figure 2.15: Bunching in RTF municipalities before and after decision,potential bunchers

5010

015

020

025

030

0

Num

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.509Standard error = 0.2729Implied elasticity = 0.0144

(a) Five to two years beforeRTF, pooled

5010

015

020

025

030

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.2698Standard error = 0.1923Implied elasticity = -0.0076

(b) One to five years after RTF,pooled

Bunching range +/− SEK 10,000 (+/− 4 bin points)

5010

015

020

025

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.1552Standard error = 0.1279Implied elasticity = 0.0044

(c) Four to two years beforeRTF, pooled

5010

015

020

025

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.1325Standard error = 0.1265Implied elasticity = -0.00003741

(d) One to four years after RTF,pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

5010

015

020

025

0

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.139Standard error = 0.1514Implied elasticity = 0.0039

(e) Five to two years beforeRTF, pooled

050

100

150

200

Num

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.2147Standard error = 0.1379Implied elasticity = 0.0061

(f) One to five years after RTF,pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: Panels (e) and (f) only includes observations up until year 2009. The fig-ures show the income distribution of public care workers around the first centralgovernment tax kink for a sub sample of public care workers that were potentialbunchers one year before an RTF policy decision. The dotted line shows the truedistribution, while the red solid line shows the seventh-order polynomial fitted tothe distribution with the income band [-5,000 SEK, 5,000 SEK] or [-10,000 SEK,10,000 SEK] omitted. Each point represents the number of observations within a2,500 SEK bin.

110 CHAPTER 2

Figure 2.16: Bunching in RTF municipalities before and after decision,home municipality

010

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0050

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.0648Standard error = 0.1097Implied elasticity = -0.0018

(a) Five to one years before RTF, pooled

010

0020

0030

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.1167Standard error = 0.1381Implied elasticity = -0.0033

(b) Five to one years after RTF, pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: Only includes observations on workers who work in their home municipality.The figures show the income distribution of public care workers around the firstcentral government tax kink. The dotted line shows the true distribution, whilethe red solid line shows the seventh-order polynomial fitted to the distributionwith the income band [-5,000 SEK, 5,000 SEK] omitted. Each point represents thenumber of observations within a 2,500 SEK bin. The green solid line is the numberof potential bunchers.

2.C. APPENDIX 111

Figure 2.17: Bunching in RTF municipalities before and after decision,married women

050

010

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0025

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = 0.0537Standard error = 0.1329Implied elasticity = 0.0015

(a) Five to one years before RTF, pooled

050

010

0015

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.0413Standard error = 0.2127Implied elasticity = -0.0012

(b) Five to one years after RTF, pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: Only includes observations on married women. The figures show the incomedistribution of public care workers around the first central government tax kink.The dotted line shows the true distribution, while the red solid line shows theseventh-order polynomial fitted to the distribution with the income band [-5,000SEK, 5,000 SEK] omitted. Each point represents the number of observations withina 2,500 SEK bin. The green solid line is the number of potential bunchers.

112 CHAPTER 2

Figure 2.18: Bunching in RTF municipalities with free choice of hoursbefore and after decision

050

010

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uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = 0.0992Standard error = 0.1595Implied elasticity = 0.0028

(a) Five to one years before RTF, pooled

050

010

0015

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed CounterfactualPotential bunchers

Excess mass (b) = -0.2249Standard error = 0.1662Implied elasticity = -0.0064

(b) Five to one years after RTF, pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: Only includes observations from RTF municipalities that offered free choiceof hours (as defined in section 2.3.1). The figures show the income distribution ofpublic care workers around the first central government tax kink. The dottedline shows the true distribution, while the red solid line shows the seventh-orderpolynomial fitted to the distribution with the income band [-5,000 SEK, 5,000SEK] omitted. Each point represents the number of observations within a 2,500SEK bin. The green solid line is the number of potential bunchers.

2.C. APPENDIX 113

Figure 2.19: Bunching in RTF municipalities measured using labor income

010

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0030

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0050

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.0346Standard error = 0.0915Implied elasticity = -0.0010

(a) Five to one years beforeRTF, pooled

010

0020

0030

0040

00

Num

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f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Labor income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.22Standard error = 0.1161Implied elasticity = -0.0062

(b) Five to one years after RTF,pooled

Bunching range +/− SEK 5,000 (+/− 2 bin points)

010

0020

0030

0040

0050

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Broad income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 0.0303Standard error = 0.2091Implied elasticity = 0.0009

(c) Five to one years beforeRTF, pooled

010

0020

0030

0040

00

Num

ber o

f ind

ivid

uals

-50 -40 -30 -20 -10 0 10 20 30 40 50Labor income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = -0.4619Standard error = 0.2206Implied elasticity = -0.0131

(d) Five to one years after RTF,pooled

Bunching range +/− SEK 10,000 (+/− 2 bin points)

Notes: Only includes observations from RTF municipalities that offered free choiceof hours (as defined in section 2.3.1). The figures show the income distribution ofpublic care workers around the first central government tax kink. The dottedline shows the true distribution, while the red solid line shows the seventh-orderpolynomial fitted to the distribution with the income band [-5,000 SEK, 5,000SEK] omitted. Each point represents the number of observations within a 2,500SEK bin. The green solid line is the number of potential bunchers.

114 CHAPTER 2

Figure 2.20: Bunching for self-employed with a limited company, 2007-2013

050

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2500

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-50 -40 -30 -20 -10 0 10 20 30 40 50Taxable income relative to tax kink (in 1,000 SEK)

Observed Counterfactual

Excess mass (b) = 2.331Standard error = 0.3746Implied elasticity = 0.0515

Bunching range +/− SEK 5,000 (+/− 2 bin points)

Notes: The figures show the income distribution of self-employed workers aroundthe first central government tax kink. The dotted line shows the true distribution,while the red solid line shows the seventh-order polynomial fitted to the distribu-tion with the income band [-5,000 SEK, 5,000 SEK] omitted. Each point representsthe number of observations within a 2,500 SEK bin.

Chapter 3

Restricting Residence PermitsShort-run Evidence from a Swedish Reform∗

∗This chapter was co-authored by Peter Skogman Thoursie, and Björn Tyre-fors. We thank Lisa Laun, Elisabet Olme, and seminar and conference participantsat the EARN Workshop on Integration, Institute for Evaluation of Labour Mar-ket and Education Policy (IFAU), Lund University Department of Economics,National conference in economics at Linneaus University, Research Institute of In-dustrial Economics (IFN), Stockholm University Department of Economics, andUC Berkeley Fall 2017 Visitors’ Workshop for valuable comments and helpful dis-cussions. Björn thanks the Jan Wallander and Tom Hedelius Foundation and theTore Browaldh Foundation for generous financial support. We thank IFAU forfinancial support. All errors are our own.

116 CHAPTER 3

3.1 Introduction

Europe has recently experienced the largest refugee crisis since WorldWar II. Due to civil wars, state failures and poverty, more than onemillion individuals applied for asylum in the European Union in 2015.The most common countries of origin among these asylum seekersare Afghanistan, Iraq and Syria (Hangartner and Sarvimäki 2017).In Sweden, with a population of approximately 10 million, more than160,000 refugees applied for asylum in 2015. Integrating immigrantsand refugees into the labor market is documented to be a difficult task(e.g., Blau et al. 2011; Bratsberg et al. 2014; Böhlmark 2008; Cortes2004; Sarvimäki 2011). In Sweden, for example, among refugees whocame during the period 2006-2010 in the age group 20-50, it takes atleast seven years to achieve an employment rate of 60 percent — andconsiderably longer time if looking at females separately.1 One keycomponent for successful integration has found to be education (e.g.,Carnevale et al. 2001; Dustmann and Fabbri 2003; Bleakley and Chin2004). The education level for recent refugees are in general lowercompared to both native born as well as the entire population of for-eign born.2 The recent large influx of refugees to Europe thereforeposes a major challenge for European governments to formulate poli-cies that integrate newcomers into the labor market for a long periodto come.

Previous empirical literature on immigration addresses, for exam-ple, the question as to how immigration affect the labor market of na-tives in the host country (see, e.g., Borjas 1999, 2003; Card 1990, 2012;Dustmann et al. 2016; Foged and Peri 2016).3 Research on integration

1See e.g., Figures 2.1 and 2.2 in Ruist (2018).2See statistics from the Swedish immigration board and Statistics Sweden.3Several studies also analyze how immigration affects political preferences,

such as voting behavior and attitudes toward welfare state spending (see the recentsurvey by Hangartner and Sarvimäki 2017) in the host country. Another strand ofthe literate studies the role of proficiency in the host country’s language (see, e.g.,Tainer 1988; Chiswick and Miller 1995, 2002, 2003; Dustmann and Fabbri 2003;

3.1. INTRODUCTION 117

policies, such as labor market programs targeted at immigrants andhow the asylum process is formulated, is more rare.4 Many countriessuch as Austria, Denmark, Germany and Sweden have recently triedto decrease the number of refugees by imposing a stricter asylum pro-cess. A key policy parameter in this regard is whether asylum seekersare granted a temporary or a permanent residence permit.5 The con-sequences of the type of residence permits on labor market integrationis empirically unexplored, which is surprising given the attention thequestion has received in the political debate. Proponents of perma-nent permits believe that less uncertainty about the probability ofstaying in the host country creates stronger incentive to invest in, forexample, language and education since immigrants are more certainthat they can receive returns from their human capital investment.6Proponents of temporary residence permits, on the other hand, ar-gues that a temporary permit creates stronger incentives to integrate,especially when work or education increase the probability that thepermit can be transformed into a permanent permit.

In this paper, we analyze how a temporary residence permit in-stead of a permanent permit affects intermediate labor market inte-gration in terms of the probability of working and education. TheSwedish government decided that if the decision about granting asy-lum was taken by the Immigration board after July 20, 2016, asylumseekers should be granted temporary residence permits. When deci-sions were taken before this date, the norm was to grant permanentresidence permits. However, there are exceptions to this rule. Themost important exception is when the application was registered. Ifan application was registered before November 25, 2015, it increased

Miranda and Zhu 2013; and Bleakley and Chin 2004, 2010).4See Hangartner and Sarvimäki (2017) for an overview of these studies.5Rules for residence permits differ widely across EU members (Hangartner and

Sarvimäki 2017).6In addition, temporary conditions can create stress and impaired health,

which in turns affect integration negatively (see Swedish Red Cross (2018)).

118 CHAPTER 3

the probability of receiving a permanent residence permit. The prob-ability increased since families with children under the age of 18 atthe time of decision would still get a permanent residence permit ifthey applied before November 25, 2015. As the new legislation wasdiscussed and implemented after the registration threshold, asylumseekers should not be able to sort around this registration date thresh-old, which is also confirmed by our empirical analyzes. As such, thispolicy change that made the asylum process stricter offers a greatopportunity to estimate the causal effects of receiving a temporaryinstead of a permanent residence permit. The reform allows us to ex-ploit the discontinuity in the date of the eligibility rule and apply aRegression discontinuity design in order to make comparable groupswith permanent and temporary residence permits.

From a theoretical perspective, the effect of having a temporaryresidence permit instead of a permanent permit is ambiguous. How-ever, based on the human capital investment model incorporatingimmigrants and developed by Duleep and Regets (1999), we can de-rive some clear theoretical predictions for the Swedish context. TheSwedish legislation stipulates that temporary residence permit couldbe transformed into a permanent residence permit if the immigrantis working. According to the theoretical model, an immigrant that isless likely to stay in the host country have less incentives to investin destination-country-specific skills such as education and languagesince such investments will not generate returns if the individual can-not stay in the host country. However, if working can increase theprobability to stay, as is the case in Sweden, a prediction is thatthose on temporary residence permits have greater incentives to work.Taken together, the model predicts that we expect to find that im-migrants with a permanent residence permit are more likely to investin education whereas immigrants with a temporary permit are morelikely to start working to a larger extent. However, it is importantto note that there are competing complementary theories and theo-

3.1. INTRODUCTION 119

ries that predict opposite effects. First, a permanent residence permiteliminates the fear of deportation and increases the incentive to in-vest in a long-lasting future in the receiving country which might alsoincrease the probability of work. Second, the uncertainty about the fu-ture might create stress and other health related problems which willcounteract the hypotheses of increase work incentives. Third, since apermanent residence permit implies a more secure situation in termsof the likelihood of staying in the host country, this might reduce in-centives for a faster integration. A permanent residence permit wouldthen imply less work and education compared to a temporary permit.

Using population register data including the immigrant popula-tion for the years 2012-2017, which is compiled by Statistics Swedenand the Swedish Integration Board (the database is called STATIV),we have information on all the application and grant dates of residencepermits in addition to information on several demographic variablessuch as age and education and on various income types. The mainoutcomes are work, participating in Swedish language training, reg-ular education and validating education.7 The use of education andlanguage skills as outcome variables is motivated based on the ob-servation that these are key factors in labor market integration (e.g.,Carnevale et al. 2001; Dustmann and Fabbri 2003; Bleakley and Chin2004). The data are constructed so that we can follow the refugeesover time.

Our main results show that a temporary residence permit in-creases the probability of working, starting an education and vali-dating an education from the source country. These results suggestthat refugees granted a temporary instead of a permanent residencepermit are in general more likely to integrate on the labor marketin terms of work and education. We also find interesting results ofcaseworker behavior. The policy reform also implied that if a decision

7Language training for individuals with residence permits is provided by theSwedish municipalities through a special language program called Swedish forimmigrants (SFI).

120 CHAPTER 3

was made by the immigration board before July 20, 2016, an individ-ual should still be granted a permanent residence permit. Using thisdate as a cut-off in a Regression discontinuity design we show thatgranting caseworkers granted a substantial larger fraction of asylumseekers residence permits before July 20. Results also show that malesand older were more likely to be granted permanent residence permitsbecause of this discretionary behavior of granting caseworkers.

The major contribution of this paper is that it provides the firstcausal evidence of how of a permanent versus a temporary residencepermit affects language training and labor market integration. Ourpaper contributes more broadly to different strands of the literature.First, this work is closely related to a small body of literature thatstudies how different asylum policies affect the integration process.Hainmueller et al. (2016a) study the labor market consequences of alengthier asylum process. By exploiting variations in wait times andapplying panel data covering asylum seekers who applied for asylumin Switzerland between 1994-2004, the authors find that an increase inthe waiting time for a decision reduces subsequent employment rates.Kilström et al. (2018) investigate a Danish reform that extended theperiod from three to seven years before asylum seekers are eligible toapply for permanent residence. In general, the authors find limitedeffects on labor market outcomes for the asylum seekers. Hainmuelleret al. (2015; 2016b) exploit referendums in Swiss municipalities thatgranted citizenship to immigrant applicants in order to investigatelabor market effects of receiving citizenship. The authors find thatreceiving Swiss citizenship strongly improved long-term political andsocial integration. The effect of citizenship has also been studied byGathmann and Keller (2014), who exploit discontinuities in the eligi-bility rules for immigration reforms in Germany that changed the res-idency requirements for citizenship. In general, the authors find smalleffects on labor market integration. Kuka et al. (2018) show that thehigh school and college attendance of undocumented immigrants both

3.1. INTRODUCTION 121

increase as a reaction to a policy that deferred deportation for highschool-educated youths.

Second, our paper is also related to a small body of literature thatanalyzes the effects of labor market programs targeted at immigrants.Åslund and Engdahl (2012) study whether performance bonuses inimmigrant language training affect average student achievement inSweden and find positive effects. Andersson Joona and Nekby (2012)study a Swedish program in which newcomers were provided extensivejob search counseling and coaching. The results suggest that inten-sive coaching significantly increased the share of immigrants in regularemployment. Sarvimäki and Hämäläinen (2016) evaluate the effect ofintegration plans where participation was determined based on thedate of entry into the population register system. The regression dis-continuity analyzes show that the integration plan had significanteffects on the labor earnings of the participants.

Third, our research is also related to a broader set of studies onthe effect of proficiency in the host country’s language on labor mar-ket integration. One of our major variables in this paper is languagelearning, which we assume works as an intermediate labor marketoutcome. According to the literature, there seems to be little doubtthat proficiency in the language of the host country is crucial for suc-cessful integration. For example, Ferrer et al. (2006) find that literacydifferences between immigrants and natives explain a significant partof earnings differences. Claussen et al. (2009) find a large positiveeffect of language courses on employment (for a recent survey, seeHangartner and Sarvimäki 2017).

The paper is organized as follows. Section 3.2 describes theSwedish context for immigrants. Section 3.3 describes the change inthe asylum regulation. Section 3.4 builds our data and empiricalstrategy. Sections 3.5, 3.6 and 3.7 provide the estimation results,and Section 3.8 concludes.

122 CHAPTER 3

3.2 The Swedish Context

3.2.1 The Asylum Process in Sweden in Brief

There are two main reasons to apply for asylum in Sweden.8 One isif the asylum seeker, in accordance with the UN Convention, is a vic-tim of persecution or at risk of persecution or subject to inhumanetreatment in the person’s home country due to race, nationality, re-ligious or political beliefs, gender, sexual orientation, or affiliation toa particular social group.9 If the asylum seeker obtains refugee sta-tus according to the UN convention, a temporary residence permitthat last for three years is granted. The other main reason, based onSwedish and EU regulations, is when the asylum seeker needs sub-sidiary protection. This is for example, when people are at risk ofbeing sentenced to death or tortured or face a serious risk of beinginjured because of an armed conflict.10 Residence permits for the sub-sidiary protection reason last 13 months (which is the most commonreason in our study since they constitute 69 percent of our study pop-ulation). When the temporary residence permit expires, an individualcan apply for renewal. The permit may be renewed if the person stillneeds shelter. A temporary residence permit gives a person the rightwork.

The Swedish Migration Agency is responsible for the asylum pro-cess and examines each asylum application individually. In order toapply for asylum, the seeker must be in Sweden or at the Swedishborder.11 An important part of the Swedish legislation is that immi-

8For a detailed description of the rules regarding asylum in Sweden, see theSwedish Migration Agency.

9See the UN Refugee Agency.10In addition to the two main reasons for residence permit, there are exceptional

reasons, such as extraordinary circumstances directly related to their personalsituation, such as serious health reasons or human trafficking.

11The exception is for quota refugees who can apply from another country. Aquota refugee is a person who has been selected by UNHCR to move to anothercountry which is called resettlement.

3.2. THE SWEDISH CONTEXT 123

grants with a temporary residence permits can receive a permanentresidence permit if the individual can make a living through employ-ment and where conditions regarding the level of salary, insurancecoverage and other employment conditions are at least in accordancewhat is stipulated by the collective agreements.12 Subsidized employ-ment should not be a basis for permanent residence permit (see Prop.2015/16:174). The possibility to receive a permanent residence permitalso holds for someone who can make a living through business ac-tivities. An individual granted a permanent residence permit has theright to live and work in Sweden on the same terms as everyone elsewho resides here. The permanent residence permit can be withdrawnif the persons leave Sweden without notifying the Swedish MigrationAgency. A person can go abroad for up to two years without thepermit being affected.

Given that a permanent residence permit is granted, the individ-ual’s family can also apply for residence permits so that they can jointheir relative in Sweden. This holds for a husband, wife, registeredpartner or cohabiting partner, or children under the age of 18. Bothspouses within the couple must be at least 21 years old and musthave lived together before one of them moved to Sweden (exemptionsfrom the age requirement can be made if the couple have childrentogether). For the family to be granted residence permits, the asy-lum seeker must be able to support the family and have a suitableaccommodation in terms of size and standard where the family canlive together.

3.2.2 The Establishment Programme

Once a person has been granted a residence permit, he or she is enti-tled to the establishment program which is operated by the Swedish

12See 5 kap. 17 /§ of the legislation: "Lag (2016:752) om tillfälliga begränsningarav möjligheten att få uppehållstillstånd i Sverige".

124 CHAPTER 3

Employment Service.13 The establishment program is a support in-cluding activities and education for newly arrived immigrants. Theaim of the program is that newcomers should learn Swedish, find ajob, and become self-sufficient as quickly as possible. The programconsists of several activities that are supposed to facilitate labor mar-ket integration, such as language training, courses in social orien-tation, courses developing skills and work experience, support whensearching for jobs, help and guidance when starting an own business.An important component of the establishment program is to validatethe education that the immigrant has from the host country. In somecases, immigrants might need to complement with education in Swe-den in order for the education they have from their host country tobe valid in Sweden. In other cases, it might be relevant to invest in anew education to meet the demand from the Swedish labor market.

The establishment program is normally full-time and last maxi-mum 24 months. Individuals aged 20-64 and who participate full-timein the establishment program receive an introduction benefit of ap-proximately e30 per day (for those aged 18-20, compensation is paidonly if they do not have parents in Sweden). This compensation canbe compared to the average daily wage in Sweden, which amountsto approximately e160 (see Statistics Sweden). In addition to the in-troduction benefit, individuals can receive housing allowances and/ormaintenance support. These two types of benefits are means testedand vary depending on the costs of living that the individual faces.14

To receive the introduction benefit, it is required that the individualfollows the plan and takes part in the activities that has been agreedupon. The individual has to submit an activity report every month.

One major component of the establishment program is languagetraining program called Swedish for immigrants (SFI). Swedish mu-

13The Swedish Employment Office have a detailed description of the program.14In Sweden, the government calculates a national standard amount that should

be available to everyone. This calculation considers reasonable costs for housing,household appliances, electricity, home insurance, etc.

3.2. THE SWEDISH CONTEXT 125

nicipalities are by law required to offer such a language training pro-gram. The purpose of this program is to provide adult newcomerswith basic knowledge of the Swedish language. All immigrants with-out such skills and who are older than 16 are eligible for the program.SFI is in principle mandatory in order to receive any type of gov-ernment transfers. The program consists of language courses at fourlevels, namely, A, B, C and D. Highly educated students with highlearning skills start directly with course C. Students who lack read-ing and writing skills in their mother tongue or who have very shortschool background (up to approximately 4-6 years) will start withcourse A. The courses are graded on a scale from A to F, where Fmeans fail. For courses B-D, national tests called SFI exams are is-sued by the Swedish National Agency for Education. An individualis supposed to take part in the establishment program until he orshe starts working or studying full-time (other reasons are full-timeparental leave or absenteeism due to illness). In other words, onecannot have an employment, either with or without support, in theestablishment program. During employment, the participant is writ-ten out from the establishment program with the same scope as theemployment. Part-time work thus leads to discharge from the estab-lishment program on part-time and full-time employment means thatyou cannot participate.

An individual that has not found a job after 24 months withinthe establishment program can then take part in regular unemploy-ment programs operated by the Employment Service.15 Eligible un-employed individuals then receive a benefit called activity support.The benefits are income-related. Those without any previous laborearnings receive a basic income. Since most newcomers don’t haveany previous earnings in Sweden, they often have to rely on the basicincome. Individuals aged at least 25 receive activity support at thebasic income amount (approximately e22 per day). A person under

15See the Swedish Employment Office.

126 CHAPTER 3

the age of 25 will receive a development allowance instead of approx-imately e14 per day. From January 1, 2018, activity support, devel-opment allowance and introduction benefits will be governed by thesame regulation. Individuals registered as unemployed at the Employ-ment service and receive activity support are supposed to participatein different activities provided by the authority. The activities includelabor market programs, employment training, work preparatory ac-tivities, support for start of business activities etc.

The ultimate goal of the establishment program is to find work forthe new immigrants. Often the initial job consist of a wage subsidyto the employer. There are many types of wage subsidies but theyall share the feature that they offer a wage subsidy to the employer.Minimum wages in Sweden are set by collective agreements betweenthe employer and the unions. Approximately 90 percent of Swedishworkers are covered by collective agreements. In general, Swedish min-imum wages are considered to be relatively high in an internationalcomparison (see, for example, Skedinger 2016). High minimum wagesimply that it could be difficult for newcomers to receive a job with-out a wage subsidy, which covers the discrepancy between the marketwage level and the productivity level of the worker.

3.2.3 Immigrants and Asylum Seekers in Sweden

In 2018, Sweden has a population of around 10.2 million people. Nine-teen percent is born abroad, which corresponds to just over 1.96 mil-lion people. Approximately half of the immigrants originate froma European country, and Syrians represent the largest immigrantgroup. The second-largest group of immigrants is composed of peoplefrom Finland, followed by Iraq.16 Together with the other EuropeanUnion members, Sweden has recently experienced the largest inflowof refugees since World War II.

16See Statistics Sweden.

3.2. THE SWEDISH CONTEXT 127

Figure 3.1: Number of asylum seekers (in thousands) in Sweden during2000-2017 by gender and child versus adult

050

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150

200

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um s

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rs in

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All asylum seekers Men/boysWomen/girls Children <age of 18

Source: https://www.migrationsverket.se/

The number of individuals who applied for asylum in Sweden dur-ing the period 2000-2017 is shown in Figure 3.1. As is shown, 2015was an extreme year in which more than 160,000 applied for asylum.More men than women apply for asylum, and there are more individ-uals above the age of 18 than below. Figure 3.2 presents the numberof asylum seekers by country of origin using the largest immigrantgroups during the recent years. As revealed by the figure, Syrians,Afghans and Iraqis are the most common asylum seekers during thepast few years.

128 CHAPTER 3

Figure 3.2: Number of asylum seekers (in thousands) in Sweden during2000-2017 by most common countries of origin

010

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4050

Asyl

um s

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2001 2003 2005 2007 2009 2011 2013 2015 2017

Syria IraqAfghanistan SomaliaEritrea

Source: https://www.migrationsverket.se/

3.3 The Reform and Theoretical Predictions

3.3.1 The Change of the Asylum Regulation

During the period before the refugee crisis in 2015, asylum seekerswere granted permanent residence permits as default. On Novem-ber 24, 2015, the Swedish government announced that it would startto work on a new law proposal that would limit the possibility forrefugees and people with protection status to get permanent residencepermits.17 Two weeks prior, on November 12, the Swedish governmentalso implemented stricter border controls. Together with the stricterborder controls in other EU countries, the inflow of refugees was re-duced from 39,000 in October 2015 to 14,000 in December 2015.

On June 21, 2016, the parliament passed a proposed legislation

17This information can be found on the home pages of the Swedish MigrationAgency, which is the source guiding this section.

3.3. THE REFORM AND THEORETICAL PREDICTIONS 129

that establishes the norm of granting temporary rather than perma-nent residence permits to asylum seekers (in addition, the rules forfamily reunification were affected for some groups). The law cameinto force a month later on July 20, 2016. The new law was in starkcontrast to the old law. According to the old law, which was valid un-til the 19th of July, any person with the right to asylum was granteda permanent residence permit with the right to family reunificationwithout having to provide economic support for the newcomer. Withthe new law, the norm is to grant temporary residence permits whenasylum decisions are taken by the Swedish Migration Agency on July20, 2016, or after.

For the empirical design of this paper, there are exceptions. Animportant exception is when the application was registered beforeNovember 25, 2015, and if the applicant is below the age of 18 or ifthe applying family has a child below 18 at the time of the decision. Insuch a case, the old rules apply, implying that a permanent residencepermit is granted. Hence, the application date of November 25, 2015is an important date that determines the status of residence permits.In addition, the age of the youngest family member at the time ofdecision (above or below 18) determines treatment. This means thatif the youngest family member is below 18 when the decision is taken,even after July 20, a permanent residence permit is granted.

Taken together, there are three thresholds that determine whethera refugee or a person who needs subsidiary protection receives a per-manent rather than a temporary residence permit: (i) the decisionabout the type of residence permit is made by the Swedish MigrationAgency before July, 20, 2016; (ii) the application is registered beforeNovember 25, 2015; and (iii) the applicant or the youngest child inthe applicant family is below the age of 18. Table 3.1 summarizes thedifferent treatments based on these threshold

In theory, these thresholds give us the opportunity to use threedifferent regression discontinuity designs (RDD). However, as the key

130 CHAPTER 3

identification assumption of RDD is that there is no perfect manip-ulation or sorting, it is important to indicate that the three designsdiffer in terms of sorting possibilities. The July 20 threshold and theage 18 cut-off are based on the decisions of the granting officers atthe Swedish Migration Agency. Thus, sorting is feasible if bureau-cracies adjust their behavior because of the new law and since theyhave the potential to perfectly observe the assignment variables. Thissetting is in stark contrast to that for the application date thresholdof November 25 for two reasons. First, it is impossible for the asy-lum seeker to exactly control when they arrive in Sweden and hencehave the possibility of applying. Second, and most importantly, asthe threshold was postulated in retrospective, the asylum seekers didnot know about the rules when they applied for a residence permit.For this reason, using application dates around the threshold date ofNovember 25, 2015, will be our main strategy.

3.3. THE REFORM AND THEORETICAL PREDICTIONS 131T

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132 CHAPTER 3

3.3.2 Theoretical Predictions of the Reform

One major decision facing a refugee is to what extent he or she shouldinvest in education or start working. Work and education are our ma-jor outcomes when analyzing differences in labor market behaviorbetween refugees with temporary versus permanent residence permit.To support our empirical analyzes we discuss theoretical predictionsof differences in labor market behavior between the two groups. Thestarting point is the investment-in-human-capital model as proposedby Duleep and Regets (1999).18 Our discussion is facilitated by thefact that the assignment to temporary and permanent residence per-mits are as good as random due to our empirical strategy. Hence, theonly difference between our two groups, in a statistical sense, is thedifferent type of residence permits.

In previous literature, the comparison is often between natives andimmigrants where the two-period human capital investment modelcan help to explain how education and work decisions differ betweenthese two groups. One important parameter of the model is the possi-bility to transfer education from the source country to the destinationcountry. This skill-transfer parameter implies, given the same initiallevel of education, that investment in education can be higher forimmigrants since the alternative cost of education is lower due to alower market return from education. For our purpose, the interestingcomparison is between immigrants with different types of residencepermits but who are statistically equal in all respects. As such, wecan simplify and leave out the skill-transfer parameter in our versionof the model, since this parameter is equal across the two immigrantgroups.

A permanent residence permit implies that the individual will beable to stay in the destination country with a high degree of certainty.

18This model has also been the starting point in several empirical papers. Seee.g. Akresh (2007), Duleep and Regets (2002), Duleep, Liu and Regets (2014), andVan Tubergen and De Werfhorst (2007).

3.3. THE REFORM AND THEORETICAL PREDICTIONS 133

We can therefore characterize the investment in human capital for animmigrant with a permanent residence permit in the same way asfor natives but with the exception that the initial education level isobtained in the source country. A simplified version of the investmentin human capital model for immigrants with permanent residencepermit is formulated in the following way:

maxθ

wHs(1 − θ) + w[Hs + γf(Hs, θ)], (3.1)

where w is the market wage rate, Hs is the immigrant’s initial stockof human capital produced in the source country, θ is the fraction ofthe market value of the initial human-capital invested, and γf(Hs, θ)is the human capital production function with a human capital pro-ductivity coefficient, γ. The optimal investment of education in thefirst period, θ∗ maximizes total earnings over the two periods. Thegreater returns to human capital in period two, the higher investmentin education will take place in period one. This is illustrated by thefirst order condition

wγdf

dθ= wHs, (3.2)

where the left-hand side is the marginal benefit of investing in ed-ucation and the right-hand side is the marginal cost, i.e., forgoneearnings.

For immigrants with a temporary residence permit we in additionallow for the probability of staying in the host country, ρ (which isassumed to equal one for those with permanent permits). A majorcomponent of the Swedish legislation is that an immigrant with atemporary residence permit can receive a permanent residence permitby working. This means that ρ is a function of θ, since 1 − θ is theprobability of working and dρ

dθ < 0. The investment in human capitalmodel for immigrants with a temporary residence permits can be

134 CHAPTER 3

formulated as

maxθ

wHs(1 − θ) + wρ(θ)[Hs + γf(Hs, θ)]. (3.3)

For immigrants with a temporary residence permit, the first ordercondition is

wdρ(θ)dθ

[Hs + γf(Hs, θ)] + wρ(θ)γ dfdθ

= wHs. (3.4)

Comparing the benefits of investing in education between immigrantswith permanent versus temporary residence permits, the first orderconditions for the two groups show that the marginal benefits of edu-cation is larger for someone with a permanent residence permit thanfor someone with a temporary residence permit. The reason is thatthe marginal benefit for immigrants with a temporary residence per-mit has a negative component represented by the first term on theleft-hand side of the first order condition in Equation (4). The secondcomponent of the first order condition is positive but weakly smallerthan the corresponding component for immigrants with permanentresidence permits (since ρ ≤ 1).

In other words, an immigrant with a temporary residence permitwill have less incentives to invest in destination-country-specific skillssuch as education and language. The reason is that there is no guar-antee that the human capital investment will generate a return if theindividual will not be allowed to stay in the host country. Since thealternative to education in the model is work, the model predicts thatimmigrants with a temporary permit are more likely to work.

There are alternative theories that predict opposite effects as thosesketched above. First, one factor is psychological stress. Theoretically,stress can arise if immigrants face threats to their resources and in-vestments (Hobfoll 2001). A temporary residence permit might createmore stress than a permanent one, which would make labor market

3.4. DATA AND EMPIRICAL SETTING 135

integration more difficult. This could for example imply that immi-grants with a temporary residence permit are less likely to be able towork. Second, employers might be more willing to hire someone whoseresidence is secured, rather than investing in someone who might haveto leave the country. If this is the case, labor market integration be-comes more difficult with a temporary residence permit. Third, sincea permanent residence permit implies a more secure situation in termsof the likelihood of staying in the host country, this might reduce in-centives for a faster integration. A permanent residence permit wouldthen imply less work and education compared to a temporary permit.It is possible that the design of the Swedish asylum policy where workcan make an individual qualified for a permanent residence permit,reinforces work and education incentives for those with a temporarypermit. Especially when employment opportunities are limited, whichis often the case for new arrivals in Sweden, education can be an al-ternative to work for immigrants with temporary permits in order toincrease the chance of finding a job in the near future.

3.4 Data and empirical setting

3.4.1 Data

Our data come from the STATIV database, which is compiled byStatistics Sweden. STATIV is a collection of registers that includes allindividuals who at some point have been granted a residence permitin Sweden (individuals who applied for but never received a residencepermit are not included). Data only includes information of type ofresidence permit, i.e., temporary or permanent residence permits, forthose individuals who have been assigned a host municipality whichis true for the majority of the refugees. Since we need information ontype of residence permits for those who have not been assigned a hostmunicipality, we complement with register information from StatisticsSweden on type of residence permit for all asylum seekers granted a

136 CHAPTER 3

permit, including those who have not been assigned a host municipal-ity (this register is called the Migration- and asylum register, MOAin Swedish).

STATIV also includes several register data sources, allowing usaccess to a rich set of individual characteristics such as age, educa-tion level, and different types of income variables. Data also includesinformation which allows use to construct several main labor marketoutcome variables. Our main outcome variables, as suggested by thetheoretical predictions outlined in the previous section, are: (i) work-ing or not defined a as having non-zero annual labor earnings, (ii)having started any Swedish regular education (regular education isdefined as educations that are not part of the labor market programsprovided by the Employment Office), (iii) having started the Swedishlanguage training program or not, and (iv) the probability of validat-ing an education. We will also comment on the results when usingother alternative definitions of these variables. For example, we willalso define working as having annual labor earnings above one BasicAmount.19 Regarding Swedish language training, we will also use thetotal number of hours that the refugee has participated in the SFIprogram. Later in the analyzes we will also investigate effects on al-ternative outcome measures such as housing allowance, introductionbenefit, and maintenance support. We will motivate these outcomesin the additional results section.

Our main sample constitutes all individuals aged 25-65 with atleast one child below the age of 18, and who applied for asylum duringmonths around November 24, 2015. These restrictions are made forindividuals where we have information on the outcome variables inNovember 2016 and 2017. The reason for the age restriction is thatbefore the age of 25, individuals were affected by the specific rulesregarding the possibility to study at high school. The reason why we

19The Basic Amount is set (and annually revised) by the Government to bench-mark welfare benefits.

3.4. DATA AND EMPIRICAL SETTING 137

Table 3.2: Summary statistics

Mean Sd Min Max(1) (2) (3) (4)

Panel A: First stageTemporary residence 0.22 0.41 0 1

Panel B: Outcome variablesSwedish for immigrants 0.65 0.48 0 1Hours completed, Swedish for immigrants 176 206 0 1,476Enrolled in regular education 2016 or 2017 0.11 0.31 0 1Housing allowance (100 SEK) 3.91 31.20 0 468Introduction benefit (100 SEK) 354 285 0 936Maintanence support (100 SEK) 172 230 0 5,850Unemployment (in days) 300 99 1 365Positive earnings 2016 or 2017 0.12 0.32 0 1

Panel C: Pre-treatment variablesRefugee 0.28 0.45 0 1Year of birth 1980 8 1950 1993Female 0.52 0.50 0 1Afghanistan 0.09 0.29 0 1Eritrea 0.02 0.13 0 1Iraq 0.08 0.28 0 1Somalia 0.01 0.11 0 1Syria 0.71 0.46 0 1Observations 12,089

Notes: Summary statistics on refugees 25-65 years old (at arrival) that arrivedwithin a 100 days time-window of November 24th 2015.

focus on parents with at least one children below the age of 18 is thatit is for this population where the date, November 24, determines thetype of residence permit.20 Table 3.2 reports summary statistics ofour main variables.

20We have also performed the same analyzes on sample where we also includeasylum seekers without children. This creates a weaker first stage but results arerobust to this augmented sample definition. These results will be commented onin the results section.

138 CHAPTER 3

3.4.2 Empirical Strategy

The strategy we are using in this paper is the Regression disconti-nuity design. As discussed in Section 3.2, three treatment variablesdetermine the probability of receiving a temporary permit if a par-ticular threshold is surpassed. There has been a recent debate onwhether time can be used as the running variable without invalidatingthe standard regression discontinuity design (Hausman and Rapson2017). If we can use small time windows around the threshold, for ex-ample, using daily data, the treatment is not ex ante inevitable, andthe data generating process cannot be perfectly manipulated, or an-ticipated, as when the rules are retroactively implemented, then, wecan employ standard regression discontinuity techniques (see, e.g.,Hausman and Rapson 2017 and Lee and Lemieux 2010). Our maindesign, which uses the application date as the running variable, fitsinto this description. Moreover, there is no reason to believe that thereis perfect control over this variable. Below, we will focus on describingour main design.

We argue that our RD approach is a fuzzy design in which theprobability of granting a temporary permit is affected if the thresholdis exceeded.21 Thus, we will estimate standard RD specifications ofthe form

Yi = α+ τDi + f(Xi − c) + εi, (3.5)

where Yi is a labor market integration outcome, such as languagetraining, educational or labor market success, for individual i. f(Xi−c) represents a continuous function of the normalized running vari-able, which is defined as the distance in days from the threshold dateof November 24, and Di is an indicator with a value of one if a tem-porary permit is granted and zero if a permanent is granted. Thus, τ

21As we will show, we can rule out the possibility that refugee/subsidiary statusin our main design is affected by the new rules. Moreover, family reunification rulesare only marginally affected and only for some subgroups.

3.4. DATA AND EMPIRICAL SETTING 139

represents the treatment effect of being assigned a temporary insteadof a permanent permit and is the parameter of interest. As Di is gen-erally endogenous, we will use the threshold as an instrument. Forexample, we will use the eligibility rule Zi = 1[X ≥ November24] asan instrument for treatment status Di (e.g., Hahn et al. 2001, Imbensand Lemieux 2008). We will recover our causal effect by estimatinga first-stage equation (Equation (6)) and a reduced-form outcomeequation (Equation (7)), which are described in the following way:

Di = φ0 + φ1Zi + f(Xi − c) + vi (3.6)

Yi = α0 + α1Zi + f(Xi − c) + ui (3.7)

where the estimated treatment effect τ is the ratio between the es-timates of α1 and φ1. Equation (5) is estimated by non-parametriclocal linear regressions (LLR), as suggested by Hahn et al. (2001) andPorter (2003), and we follow the suggestion of Imbens and Lemieux(2008) and Lee and Lemieux (2010) to use a uniform kernel. Thebandwidth is selected by optimal bandwidth selector in Calonico etal. (2014a, 2014b), but we always display a number of bandwidths.In particular, we follow the advice in Lee and Lemieux (2010) andgraphically present the estimates over a large range of bandwidths.We cluster the standard errors on the forcing variable because it isdiscrete (Card and Lee 2008).

Following the recommendations of McCrary (2008) and Cattaneoet al. (2017), the validity of the RDD is evaluated by analyzing thedensity of the running variable (i.e., the registered application dateor the decision date). Here, we test the null hypothesis of continu-ity around the cut-off value of the dates determining type of resi-dence permit in which a discontinuity suggest violations of the no-manipulation assumption. Since a density discontinuity is not conclu-sive evidence of violations of the RDD assumptions, we also display

140 CHAPTER 3

examples of covariates that should be continuous around the cut-offif manipulation and sorting are not problems. Then, if sorting is notfound, we can continue and analyze outcome measures, presentingboth first-stage, reduced-form, and treatment estimations.

Test of the Validity of the RD Design

The RD design relies on the key identifying assumption that indi-viduals are as good as randomized around the cut-off. An advantagewith the method is that this assumption offers some testable pre-dictions. In our case this means that there shouldn’t be any sortingof individuals around the application date of November 24, 2015. Italso predicts that individual background characteristics should evolvesmoothly around this application cut-off date. Otherwise, it would bea sign that individuals of certain types have managed to sort on oneside of the cut-off, potentially in order to benefit from a permanentresidence permits (note that such sorting could also be a consequenceof migration caseworkers having preferences for type of residence per-mits).

In panel a of Figure 3.3, we show the mean number of daily ap-plications in three-day bins. There is no sign of discontinuity in thenumber of applications around date of November 24, 2015, which isnormalized to zero in the figure. The null hypothesis of no disconti-nuity cannot be rejected at any conventional significance level. Thus,this result supports the hypothesis that there is no systemic sortingof asylum seekers around the date that determines whether a tempo-rary or permanent residence permit is granted. The underlying RDDresults with optimal bandwidth are reported in Column 1 of TableA1 in the Appendix.

Moving to the balance test of background characteristics such asage and the share of females among asylum seekers, results show thatthese characteristics are balanced around the threshold (see panels b

3.4. DATA AND EMPIRICAL SETTING 141

Figure 3.3: Balance test0

5010

015

020

0

Num

ber o

f obs

erva

tions

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(a) Number of observations01

jan1

975

01ja

n197

801

jan1

981

01ja

n198

4

Birth

day

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(b) Birthday

.45

.5.5

5.6

.65

.7

Shar

e w

omen

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(c) Share women

.6.7

.8.9

1

Prob

abilit

y of

dec

isio

n af

ter J

uly

20 2

016

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(d) Prob. of dec. after July 2016

Notes: In Panels a-d the Stata routine rdrobust has been used where plotted pointsare conditional means with a binwidth of 3 (Calonico et al., 2017). The solid lineis the predicted values of a local linear estimation with a uniform kernel.

and c of Figure 3.3).22

As explained in Section 3.3.1, from July 20, 2016 and onwards thenorm is to grant temporary residence permits. Thus, it is only asylumseekers who get their application granted after this date that areaffected by the new rules. One way for migration officers to affect the

22In Figures A1 in the Appendix, we show the results of the balance testsfor a set of other pre-treatment characteristics of the asylum seekers, once againsupporting the hypothesis that pre-characteristics are balanced. The underlyingRDD results with optimal bandwidth are reported in Table A1 in the Appendix.

142 CHAPTER 3

share of applicants receiving permanent residency would be to front-load applications depending on date of arrival i.e., working only withthose arriving before or after November 24, depending on caseworkers’preferences for permanent permits. To examine the existence of suchbehavior by migrant caseworkers, we show the probability of receivinga decision after July 2016 in Panel d of Figure 3.3. According tothis figure, there is no such caseworker behavior as the probability ofreceiving a decision after the new law was implemented do not changediscontinuously around the cut-off.

Taken together, the above analysis supports our a priori reasoningthat it is not possible for either asylum seekers or granting officers tomanipulate the running variable (i.e., the registered application date).Therefore, using the date of registered application as the runningvariable within an RDD framework, we can study the causal effectsof receiving a temporary residence permits instead of a permanentpermit.

3.5 Main Results

In this Section we present the main results. First, we report how thechange in the asylum legislation affects the fraction of asylum seekersthat receive temporary residence permits (i.e., the first stage effect).Second, we analyze how a temporary residence permit affects ourmain outcomes which are the probability of working, taking part inthe Swedish language training program and regular education.

3.5.1 First Stage Effects

In Figure 3.4 we report the graphical representation of the first stageeffect, i.e., the fraction of individuals who receive a temporary resi-dence permit, by dates. According to Figure 3.4, the share receivinga temporary residence permit increases by approximately 70 percent-age points at the threshold date, November 24, 2015, when the new

3.5. MAIN RESULTS 143

Figure 3.4: The share of individuals receiving a temporary residence per-mit, by application dates (first stage relationship)

0.2

.4.6

.81

Prob

abilit

y ge

tting

tem

pora

ry re

side

ncy

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

Notes: The plotted points are conditional means with a binwidth of 3 using Stataroutine rdrobust (Calonico et al., 2017). The solid line is the predicted values of alocal linear estimation with a uniform kernel.

legislation made temporary residence permit the default.In Table 3.3, we present the corresponding coefficient estimates of

the first stage effect, based on local linear regressions (see Equation(6)) using optimal bandwidths (see Calonico et al. (2017)). Estimatesreported in the first Column of Table 3.3 use a linear specification ofthe forcing variables without controlling for additional control vari-ables. In Column 2, control variables are added to the specificationand in Column 3 a second order polynomial specification of the forcingvariables is used with control variables. In Figure A2 in the Appendixwe show that the first-stage effect is robust to a large number of differ-ent bandwidths (both with and without controls and with a linear aswell as quadratic specification of the local linear regression). Accord-ing to Table 3.3, the probability of receiving a temporary residencepermit increases is 69-72 percentage points higher due to the changeof the asylum regulation.

144 CHAPTER 3

Table 3.3: First Stage

(1) (2) (3)

First stage 0.72∗∗∗ 0.73∗∗∗ 0.69∗∗∗

(0.029) (0.030) (0.037)Obs 8,292 7,771 8,893Bandwidth 58 54 64Polynomial 1 1 2Controls X X

Notes: Standard errors in parentheses. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.Bandwidths are selected using the optimal bandwidth selector in Calonicoet al. (2017). All predicted values are estimated with a uniform kernel.

The reason why the probability of receiving a temporary resi-dence permit does not go from zero to one between the periods be-fore and after the cut-off, i.e., November 24, is that when decisionsabout residence permits were taken before July 20, 2016, individualswere granted permanent residence permits. Decisions were made be-fore this date for individuals who applied both before November 24,as well as after.

As described in Section 3.3 and presented in Table 3.1, there aretwo reasons to apply for asylum, either in order to obtain refugeestatus or to obtain subsidiary protected status. Although the rules(i.e., the UN convention) did not change at the same time, we cannotex ante rule out that the interpretation of the rules could have changedat the cut-off date. As refugee and subsidiary protected status mattersfor treatment, for example affecting the length of the residence permit,a change in the interpretation of the rules could violate the exclusionrestriction. It is therefore important to rule out that the interpretationof the type of asylum reason rule changed on November 24, 2015. Toinvestigate this, we estimated the RD effect on the probability ofbeing classified as a refugee instead of obtaining subsidiary protected

3.5. MAIN RESULTS 145

status. Reassuringly, Panel a in Figure A1, in the Appendix shows noevidence of a jump.

3.5.2 Main outcome effects

In Figure 3.5 we report the graphical evidence of the reduced-formeffects of temporary residence permits on our main labor market out-comes: (a) the probability of working (i.e., work shares), (b) probabil-ity of starting education (except language training), (c), the probabil-ity of starting language training, and (d) the probability of validatingan education.

Consistent with the theoretical prediction outlined in Section3.3.2, panel a in Figure 3.5 shows that after the cut-off date,temporary residence permits increase the probability of workingcompared to permanent permits. In contrast to the theoreticalprediction it seems that a temporary residence permit also increasesthe probability of starting an education (see panel b of Figure 3.5).The same conclusion holds for the probability of entering languagetraining and the probability of having the education validated (seepanels c and d).

Table 3.4 reports the RD estimates of the reduced-form effectsof temporary residence permits on the main outcome variables usingthe optimal bandwidths. For each outcome variable we report resultsbased on three specifications, a linear specification of the local lin-ear regression without control variables, a linear specification withcontrol variables and finally a second order specification with controlvariables. Panel A report results from reduced form estimations andPanel B report the treatment effect based on IV-estimates.23

The graphical results are confirmed by the results from RD re-gressions. The probability of working are 2-6 percentage points higherfor those with temporary residence permits compared to permanent

23Results using different bandwidths for the three types on polynomial specifi-cations, respectively, are reported in Figure A3-A5 in the Appendix

146 CHAPTER 3

Figure 3.5: Work and education outcomes0

.02

.04

.06

.08

.1.1

2.1

4.1

6.1

8

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(a) Prob. having worked 2016 or2017

0.1

.2.3

Enro

lled

in a

ny e

duca

tion

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(b) Prob. starting educ.

.4.5

.6.7

.8

Prob

abilit

y st

artin

g Sw

edis

h tra

inin

g

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(c) Prob. starting SFI

0.0

3.0

6.0

9.1

2.1

5

Hav

e a

valid

ated

edu

catio

n in

Sta

tistic

Sw

eden

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(d) Prob. validating educ.

Notes: This Figure reports the graphical evidence of the reduced-form effects oftemporary residence permits on (a) the probability of having worked during 2016-2017 (i.e., work shares), (b) probability of starting education (except languagetraining), (c), the probability of starting language training, and (d) the probabilityof validating an education. In Panels a-d the Stata routine rdrobust has been usedwhere plotted points are conditional means with a binwidth of 3 (Calonico et al.,2017). The solid line is the predicted values of a local linear estimation with auniform kernel.

permits, depending on the underlying specification (see IV results inPanel and Columns 1-3 in Table 3.4). With a work share of 15 per-cent for those with a permanent residence permit, these effects implythat the work share for an individual with a temporary residencepermit are approximately 15-40 percent higher than for those with

3.5. MAIN RESULTS 147

permanent residence permits (note that the effect is only statisticallysignificant for the second order polynomial specification reported inColumn 3).

Table 3.4 also shows that the effect of temporary permits on theprobability of starting an education is significantly positive, regard-less of specification (see panel B, Columns 4-6). The differences rangebetween 4-8 percentage points. These are quite large effects since theshare who have starting an education among individuals with a per-manent permit is 7.5 percent, implying between 50 and 100 percenthigher probabilities of starting an education for those with tempo-rary permits. Regarding the probability of starting language trainingthere are no significant differences between temporary and permanentpermits (results are reported in Columns 7-9 in Table 3.4).

In the last three columns of Table 3.4 we report results for theprobability of validating an education from the home country. Also,for validating education, the shares are significantly higher for tempo-rary permits (except for the second order polynomial specification).The differences are around 4 percentage points implying effects interms of percent of around 80 percent.

The finding that temporary residence permits increase the prob-ability of working is consistent with the theoretical prediction of thehuman capital investment model outlined in Section 3.3.2. However,the effect of a temporary permit on the probability of starting aneducation goes against the theoretical prediction of the model. In-centives to work when receiving a temporary residence permit arestrong within the Swedish design of the asylum policy. However, theprobability of finding a job is in general low for individuals who re-cently immigrated to Sweden. The work shares for our study groupsis around 10 percent. If labor market opportunities are low for theimmigrant group under study, incentives to start an education mightbe higher for those who have less chances to stay in the country. Onechannel to increase the possibility to find a job and ultimately receive

148 CHAPTER 3

a permanent residence permit, is through education. This might alsoexplain why those with temporary permits are more likely to startan education and validate their education, which both might increasethe likelihood of finding a job.

Taken together, results suggest that refugees granted a temporaryinstead of a permanent residence permit are in general more likelyintegrate on the labor market in terms of increased propensities inworking and taking part in education.

3.5.3 Placebo effects

One way to check the validity of our research design is to study agroup who is unaffected by the change in the new asylum regulation.For such a group we should not find any effects on the work and edu-cation outcomes. One such group is asylum seekers without childrenbelow the age of 18. Regardless of when they applied for asylum, i.e.,before or after November 24, 2015, they should all receive a tempo-rary residence permit unless the decision were taken before July 20,2016.

The first stage for this group is presented in Figure A6 in theappendix. The figure clearly shows that there is no difference in theshares temporary residence permits around the cut-off. The fractionof temporary permits is not equal to one, neither before nor afterNovember 24, 2015. The reason is that some immigrants who appliedfor asylum around the cut-off, decision about residence permits weretaken before July 20, 2016, and they were granted permanent resi-dence permits. The absence of any first stage effects for the sampleof asylum seekers without children below 18 is confirmed by the cor-responding RDD estimates presented in Table A2.

The hypothesis that there should be no effect of temporary resi-dence permits on the outcome variables is supported by Figure A7 inthe Appendix, showing the RDD graphs, and by Table A3 showing thecorresponding RDD estimates. For work, starting an education and

3.5. MAIN RESULTS 149

language learning there are no signs of any effect at this threshold.We have also performed a number of placebo estimations for our

main outcome variables, defining November 24, 2014 as a placebothreshold date. Importantly, there are no signs of any effect at thisthreshold (results are available from the author).

150 CHAPTER 3

Tab

le3.

4:Workan

deducationou

tcom

es

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

(11)

(12)

Pan

elA:Red

uced

form

outcom

es

Proba

bilityworking

Proba

bilityed

ucation

Proba

bilitySF

IProba

bilityvalid

ating

RD

Estim

ate

0.02

∗0.03

∗∗0.01

0.03

∗∗0.03

∗∗0.03

∗∗0.00

0.00

0.02

0.03

∗∗0.03

∗∗0.03

∗

(0.014)

(0.013)

(0.017)

(0.011)

(0.011)

(0.013)

(0.031)

(0.028)

(0.029)

(0.016)

(0.015)

(0.017

)Obs

11,242

11,427

13,132

9,208

9,208

12,587

7,206

7,530

12,121

6,631

6,724

11,695

Ban

dwidth

8890

128

6565

112

4953

102

4547

94Pan

elB:Treatmenteff

ects

Proba

bilityworking

Proba

bilityed

ucation

Proba

bilitySF

IProba

bilityvalid

ating

RD

Estim

ate

0.02

0.03

0.06

∗0.04

∗∗0.05

∗∗∗

0.08

∗∗∗

0.02

0.00

-0.02

0.04

∗0.04

∗∗0.03

(0.021)

(0.022)

(0.033)

(0.015)

(0.017)

(0.024)

(0.047)

(0.044)

(0.055)

(0.023)

(0.020)

(0.027)

First

0.73

0.72

0.66

0.72

0.73

0.68

0.69

0.69

0.66

0.69

0.72

0.68

Obs

9,734

8,054

8,180

8,720

7,460

8,479

5,863

5,863

8,180

5,863

8,054

9,208

Ban

dwidth

7056

5863

5260

3939

5739

5666

Polyno

mial

11

21

12

11

21

12

Con

trols

XX

XX

XX

XX

Notes:S

tand

arderrors

inpa

renthe

ses.

∗p<

0.10,∗∗

p<

0.05,∗∗

∗p<

0.01.B

andw

idthsa

reselected

usingtheop

timal

band

width

selector

inCalon

icoet

al.(2017).

Allpred

ictedvalues

areestim

ated

with

aun

iform

kernel.P

roba

bilityworking

isadu

mmyforha

ving

positiv

eearnings

in2016

or2017.P

roba

bilityed

ucationis

adu

mmyforha

ving

startedsomeed

ucation(other

than

SFI)

inthefallof

2016

or2017.P

roba

bilityof

SFIisadu

mmyforha

ving

startedlang

uage

training

in2016

or2017.P

roba

bilityvalid

atingis

adu

mmyforha

ving

valid

ated

one’sed

ucation.

3.6. ADDITIONAL ANALYZES 151

Figure 3.6: Welfare outcomes0

.51

1.5

2

Hou

sing

allo

wan

ce 2

017

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(a) Housing20

022

024

026

028

030

0

Intro

duct

ion

bene

fit 2

017

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(b) Introduction benefit

120

140

160

180

200

220

Mai

nten

ance

sup

port

2017

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(c) Maintenance support

Notes: In Panels a-c the Stata routine rdrobust has been used where plotted pointsare conditional means with a binwidth of 3 (Calonico et al., 2017). The solid lineis the predicted values of a local linear estimation with a uniform kernel.

3.6 Additional analyzes

3.6.1 Alternative outcomes

We have also analyzed the effects of temporary residence permits ona number of outcomes representing welfare benefits such as housingallowances, introduction benefits and maintenance support. Resultsare reported in Figure 3.6 and reveal no significant effects.

152 CHAPTER 3

3.7 RD using decision date or age

In this section, we analyze the effect of temporary residence permitsusing the date of decision made by the Swedish Migration Agency,as well as the age at decision. Decisions made before July 20 shouldimply permanent permits, while those made after July 20 imply atemporary residence permit. Figure 3.7 shows the number of observa-tions around the threshold based on the decision date. In Panel a ofFigure 3.7 we can clearly reject the null hypothesis of no discontinuity.Apparently, caseworkers made more decisions before July 20. The sizeof the case load increased dramatically in order to finalize decisionsbefore the expiration of the old law. This behavior is consistent withthe goal of maximizing the total number of permanent permits, whichwould decrease future workloads since officers don’t have to deal withrenewed applications from the refugees. As there was a boom in thenumber of cases around this time, there is a debate as to whether themanagers at the Swedish Migration Agency encouraged the officers tohandle as many cases as possible. One natural strategy in this respectis to maximize the number of permanent residence permits since thesecases would not return after 13 months or 3 years.

The above finding is less of a problem if caseworkers front-loadedthe workload with no respect to underlying characteristics. Then,groups across the threshold would still be balanced. However, as de-picted in Panel c and e, significantly older people and more malesare chosen prior to July 20, implying that males and older are givenpermanent residence permits to a larger extent. Thus, it seems thatcase rationing behavior of caseworkers took place, i.e., picking thesubjects that have the most to lose (older) from the stricter polices.But also that favors men. The last finding is not consistent with min-imizing future reoccurring applications and thus something else wasmaximized by the migration authorities.

Turning to panels b, d and f in Figure 3.7, we use age of theyoungest family member at decision as a cut-off. Being just below

3.7. RD USING DECISION DATE OR AGE 153

Figure 3.7: Test of density continuity and balance when the forcing vari-able depends on the date of the decision

020

040

060

080

0

-21 -14 -7 0 7 14 21Normalized day of decision (0=20th July)

Panel A: No. of observations

-200

020

040

060

0-21 -14 -7 0 7 14 21

Normalized age at decision day (0=18 year)

Panel B: No. of observations

01ju

n198

701

jun1

991

01ju

n199

5

-21 -14 -7 0 7 14 21Normalized day of decision (0=20th July)

Panel C: Birthday

01ju

n199

630

nov1

997

01ju

n199

9

-21 -14 -7 0 7 14 21Normalized age at decision day (0=18 year)

Panel D: Birthday

.25

.3.3

5.4

.45

.5

-21 -14 -7 0 7 14 21Normalized day of decision (0=20th July)

Panel E: Female

0.1

.2.3

.4.5

-21 -14 -7 0 7 14 21Normalized age at decision day (0=18 year)

Panel F: Female

Notes: In Panel A-F the Stata routine rdrobust has been used where plottedpoints are conditional means with a binwidth of 3 (Calonico et al., 2017). Thesolid line is the predicted values of a local linear estimation with a uniformkernel.

the age of 18 imply permanent permits, while being just above im-ply temporary permits. As in the previous case we see clear signs ofmanipulation around the cut-off. There is an increase in the number

154 CHAPTER 3

of observations just before the refugee turn 18 and then a decrease.Again, more males than females are picked before they turn 18, point-ing to the same conclusion as with the decision date cut-off.

3.8 Conclusion

This paper provides the first causal evidence of how of a temporaryresidence permit versus a permanent permit affects intermediate labormarket outcomes such as work, language training and education. Ouranalyzes are based on a 2016 Swedish reform that changed the normof which type of residence permits that should be granted to newcom-ers. The Swedish government decided that from July 20, 2016, asylumseekers would be granted temporary rather than permanent residencepermits. However, there are exceptions to this rule for asylum seek-ers who are granted temporary residence permits after this date. Themost important exception is when a residence permit application isregistered before or on November 24, 2015, which exogenously in-creased the probability of receiving a permanent residence permit.As the law was discussed and passed after the registration threshold,there could not be any sorting around this threshold. As such, thereform allows us to exploit the discontinuity on this date and applya regression discontinuity design.

Our short-term results show that a temporary residence permit in-creases the probability of working, starting an education and validat-ing an education from the source country. No differences in languagetraining are found. The policy reform also implied that if a decisionwas made by the immigration board before July 20, 2016, an indi-vidual should still be granted a permanent residence permit. Usingthis date as a cut-off, we show that granting caseworkers granted asubstantial larger fraction of asylum seekers residence permits beforeJuly 20. Results also show that males and older were more likely tobe granted permanent residence permits because of this discretionary

3.8. CONCLUSION 155

behavior of granting caseworkers.The conclusions we draw from the results in this report are as

follows. When we study labor market outcomes a few years after new-comers applied for asylum, it seems that temporary residence permitslead to a faster integration process. The combination of temporaryresidence permits with the possibility of being granted a permanentresidence at a later date, given that one can obtain a job, increasesthe labor supply. It also seems that a temporary residence permit,at least in the short-run, increases incentives to engage in education.One interpretation of this result is that education could be one step-ping stone for obtaining employment at a later date. This might beespecially true when labor market prospects are poor which often isthe case for individuals who recently immigrated to Sweden.

It remains to analyze how temporary and permanent residencepermits affect integration in the long term. We cannot exclude thepossibility that it takes time to find an adequate education and thatpermanent permits have educational effect in a longer perspective.Nor can we exclude that there may be health effects that may affectintegration in the long run. As mentioned in the introduction, theSwedish Red Cross has warned that temporary residence permits cancause stress, among other things. Long-term and health effects willbe investigated in future research.

A further conclusion we draw from our results is that caseworkersfront-loaded the decision-making process before July 20 and that menand the elderly benefited from this process, in terms of being grantedmore permanent residence permits. Hence, a consequence of the in-creased number of decisions taken before July 20 was case picking byofficers.

156 CHAPTER 3

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162 CHAPTER 3

3.A Appendix

Figure A1. Pre-characteristics

0.2

.4.6

.81

Ref

ugee

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(a) Refugee0

.2.4

.6.8

1

Syria

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(b) Syria

0.2

.4.6

.81

Afgh

anis

tan

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(c) Afghanistan

300

350

400

450

500

Day

s fro

m a

pplic

atio

n to

dec

isio

n

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(d) Waiting time in days

Notes: In Panels a-d the Stata routine rdrobust has been used where plotted pointsare conditional means with a binwidth of 3 (Calonico et al., 2017). The solid lineis the predicted values of a local linear estimation with a uniform kernel.

3.A. APPENDIX 163Tab

leA1.

Pre-cha

racteristics

byno

rmalized

applicationda

tes

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

(11)

(12)

Pan

elA:Red

uced

form

outcom

es

Observation

sAge

Female

Dec.after

Syria

Waiting

July

2016

time

RD

Estim

ate

-48∗

∗∗-21∗

-148

-206

-0.02

-0.04∗

-0.02

-0.02

-0.02

-0.02

5-8

(10)

(11)

(117)

(160)

(0.018)

(0.021)

(0.014)

(0.017)

(0.030)

(0.035)

(10)

(9)

Obs

6,692

8,678

9,841

11,566

6,599

10,832

5,624

7,299

7,497

10,212

7,497

12,313

Ban

dwidth

4762

7093

4583

3850

5273

53106

Pan

elB:Treatmenteff

ects

Observation

sAge

Female

Dec.after

Syria

Waiting

July

2016

time

RD

Estim

ate

-92∗

∗∗-44∗

∗∗-302

∗-277

-0.02

-0.04

-0.03

0.00

-0.03

0.01

-4-3

(12)

(15)

(176)

(239)

(0.030)

(0.030)

(0.019)

(0.024)

(0.042)

(0.051)

(14)

(15)

First

Obs

10,574

10,740

8,140

10,212

4,358

10,212

6,250

9,685

7,171

8,438

5,224

8,438

Ban

dwidth

7779

5774

3073

4269

4960

3661

Polyno

mial

11

21

12

11

21

12

Con

trols

XX

XX

XX

XX

Notes:Stan

dard

errors

inpa

renthe

ses.

∗p<

0.10,

∗∗p<

0.05,

∗∗∗p<

0.01.Ban

dwidthsareselected

usingtheop

timal

band

width

selector

inCalon

icoet

al.

(2017).A

llpred

ictedvalues

areestim

ated

with

aun

iform

kernel.A

gean

dwaitin

gtim

eareexpressedin

days.

164 CHAPTER 3

Figure A2. First stage effects at different bandwidths0

.1.2

.3.4

.5.6

.7.8

.91

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(a) Linear, no control

0.1

.2.3

.4.5

.6.7

.8.9

1

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(b) Linear, control

0.1

.2.3

.4.5

.6.7

.8.9

1

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(c) Quadratic, control

Notes: Panels a, b and c show first stage outcomes on the probability of receivinga temporary residence permit given arrival after November 24, 2015 for differentbandwidths. All regressions in panels a-c use the Stata routine rdrobust package(Calonico et al., 2017) with a uniform kernel. Panel a use a linear estimation andno control variables. Panel b use a linear trend and includes control variables.Panel c use a quadratic trend and include control variables.

3.A. APPENDIX 165

Figure A3. Main outcomes for different bandwidths

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(a) Prob. work 2016 or 2017 (<0earnings)

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(b) Prob. work 2016 or 2017(<base amount earnings)

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(c) Prob. work 2016 or 2017 (<0earnings)

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(d) Prob. work 2016 or 2017(<base amount earnings)

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(e) Prob. work 2016 or 2017 (<0earnings)

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(f) Prob. work 2016 or 2017(<base amount earnings)

Notes: This figure shows reduced form outcomes on arriving after November 24,2015 for different bandwidths. Panels a and b show outcomes for different band-widths with a linear regressor. Panels c and d show outcomes for different band-widths with a linear regressor including control variables. Panels e and f showoutcomes for different bandwidths with a quadratic regressor including controlvariables. All regressions in panels a-f use the Stata routine rdrobust package(Calonico et al., 2017) with a uniform kernel. The left-hand side panels show out-comes for work defined as positive earnings in either 2016 or 2017. The right-handside panels show outcomes for work defined as at least one base amount of earningsin either 2016 or 2017.

166 CHAPTER 3

Figure A4. Main outcomes for different bandwidths-.1

-.08

-.06

-.04

-.02

0.0

2.0

4.0

6.0

8.1

.12

.14

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(a) SFI, extensive

-20

020

4060

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(b) SFI, intensive

-.1-.0

8-.0

6-.0

4-.0

20

.02

.04

.06

.08

.1.1

2.1

4

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(c) SFI, extensive

-20

020

4060

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(d) SFI, intensive

-.1-.0

8-.0

6-.0

4-.0

20

.02

.04

.06

.08

.1.1

2.1

4

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(e) SFI, extensive

-20

020

4060

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(f) SFI, intensive

Notes: This figure shows reduced form outcomes on arriving after November 24,2015 for different bandwidths. Panels a and b show outcomes for different band-widths with a linear regressor. Panels c and d show outcomes for different band-widths with a linear regressor including control variables. Panels e and f showoutcomes for different bandwidths with a quadratic regressor including controlvariables. All regressions in panels a-f use the Stata routine rdrobust package(Calonico et al., 2017) with a uniform kernel. The left-hand side panels show out-comes for the probability of having started SFI education. The right-hand sidepanels show outcomes for number of hours in SFI education, given enrollment.

3.A. APPENDIX 167

Figure A5. Main outcomes for different bandwidths

-.1-.0

8-.0

6-.0

4-.0

20

.02

.04

.06

.08

.1

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(a) Regular education-.0

20

.02

.04

.06

.08

.1.1

2

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(b) Validation

-.1-.0

8-.0

6-.0

4-.0

20

.02

.04

.06

.08

.1

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(c) Regular education

-.02

0.0

2.0

4.0

6.0

8.1

.12

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(d) Validation

-.1-.0

8-.0

6-.0

4-.0

20

.02

.04

.06

.08

.1

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(e) Regular education

-.02

0.0

2.0

4.0

6.0

8.1

.12

14 17 21 24 28 31 35 38 42 45 49 52 56 59 63 66 70Different bandwidths, in days

(f) Validation

Notes: This figure shows reduced form outcomes on arriving after November 24,2015 for different bandwidths. Panels a and b show outcomes for different band-widths with a linear regressor. Panels c and d show outcomes for different band-widths with a linear regressor including control variables. Panels e and f showoutcomes for different bandwidths with a quadratic regressor including controlvariables. All regressions in panels a-f use the Stata routine rdrobust package(Calonico et al., 2017) with a uniform kernel. The left-hand panels show outcomesfor having enrolled in any regular education in 2016 or 2017. The right-hand panelsshow outcomes for having validated ones education.

168 CHAPTER 3

Figure A6. First stage - Adults without children

0.2

.4.6

.81

Prob

abilit

y ge

tting

tem

pora

ry re

side

ncy

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

Notes: The plotted points are conditional means with a binwidth of 3 using Stataroutine rdrobust (Calonico et al., 2017). The solid line is the predicted values of alocal linear estimation with a uniform kernel.

3.A. APPENDIX 169

Figure A7. Work and education outcomes - Adults withoutchildren

0.0

5.1

.15

.2.2

5.3

.35

.4

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(a) Prob. having worked 2016 or2017

0.1

.2.3

Enro

lled

in a

ny e

duca

tion

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(b) Prob. starting educ.

.4.5

.6.7

.8

Prob

abilit

y st

artin

g Sw

edis

h tra

inin

g

-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(c) Prob. starting SFI

0.0

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2.1

5

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e a

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ated

edu

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n in

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tistic

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-21 -14 -7 0 7 14 21Normalized application day (0=24th Nov.)

(d) Prob. validating educ.

Notes: This Figure reports the graphical evidence of the reduced-form effects oftemporary residence permits on (a) the probability of having worked during 2016-2017 (i.e., work shares), (b) probability of starting education (except languagetraining), (c), the probability of starting language training, and (d) the probabilityof validating an education. In Panels a-d the Stata routine rdrobust has been usedwhere plotted points are conditional means with a binwidth of 3 (Calonico et al.,2017). The solid line is the predicted values of a local linear estimation with auniform kernel.

170 CHAPTER 3Tab

leA2.

First

Stage-Adu

ltswitho

utchild

ren

(1)

(2)

(3)

Firststage

0.01

0.01

0.04

∗

(0.017)

(0.016)

(0.023)

Obs

4,302

5,581

4,162

Ban

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lyno

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2Con

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XX

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es:S

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Red

uced

form

outcom

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(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

(11)

(12)

Proba

bilityworking

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Estim

ate

0.01

0.03

0.02

0.00

0.01

-0.00

-0.06

-0.05

-0.03

0.01

0.02

0.03

∗

(0.023)

(0.021)

(0.027)

(0.020)

(0.017)

(0.023)

(0.038)

(0.034)

(0.036)

(0.018)

(0.017)

(0.018)

Obs

9,419

9,119

11,453

9,268

10,564

11,742

5,231

5,231

10,109

5,231

5,403

9,73

1Ban

dwidth

9086

130

88108

138

5050

101

5151

96Po

lyno

mial

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21

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11

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Con

trols

XX

XX

XX

XX

Notes:S

tand

arderrors

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renthe

ses.

∗p<

0.10,∗∗

p<

0.05,∗∗

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0.01.B

andw

idthsa

reselected

usingtheop

timal

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ated

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iform

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2016

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ving

valid

ated

ones

education.

Chapter 4

Mom and Dad Got JobsNatural Resources, Economic Activity, and InfantHealth∗

∗This chapter was co-authored by Andreas Madestam, Emilia Simeonova, andBjörn Tyrefors. We thank Lisa Laun and Jon Olofsson for valuable comments. Weare grateful for funding from Jan Wallanders and Hedelius stiftelse and Marianneand Marcus Wallenberg Foundation. All errors are our own.

172 CHAPTER 4

4.1 Introduction

The traditional "enclave" view, suggested by Hirschman (1958), arguesthat natural resource extraction has few or no "backward linkages" tothe local community. Recent research has challenged this view, espe-cially the growing body of work on hydraulic fracking in the UnitedStates. The effects are not uniformly positive, with perhaps the moststriking trade-offs appearing between labor market gains and health(and in particular infant health) losses (Bartik et al, 2019; Currie,Greenstone and Meckel, 2017; Hill, 2018; Feyrer, Mansur and Sacer-dote, 2017). Though fracking has received a lot of attention in theliterature, other types of natural resource extraction likely have sim-ilar effects on local economies. As discussed by Cust and Poelhekke(2015), local economic gains from natural resource extraction are com-mon, although the effects are modest.

Most extraction projects, including hydraulic fracking, undergoseveral phases, from initial discovery to final extraction, where eachphase can have distinct consequences on the locality.1 By ignoring theimpact of the stages leading up to the actual extraction phase, thereis a risk of understating the true direct gains, and conversely under-stating the true direct losses, related to the opening and exploitationof a natural resource. In this paper, we make progress on this ques-tion by examining the local economic impact of resource exploitationrights. Specifically, combining differences in the timing and locationof Swedish mineral exploitation permits in a difference-in-differencesdesign, we estimate the causal effect of the initial preparatory stagesof mine extraction on the local economy.

The effects we uncover are nontrivial and speak directly to theimportance of accounting for activities that occur before the activephase of natural resource extraction begins. Using highly disaggre-

1For example, introductory texts on the direct impact of mining highlight thedifferent phases of mine development (see, e.g., https://www.elaw.org/mining-eia-guidebook).

4.1. INTRODUCTION 173

gated data, we estimate a significant positive impact of mineral ex-ploitation permits on employment and wages for both women andmen and a negative effect on housing prices. We also show that chil-dren’s early-life health outcomes are negatively affected. As we studythe phase before the mines de facto open, we argue that the health ef-fects cannot be due to pollution and other dis-amenities caused by theactual resource exploitation, and are thus more likely due to increasedlocal economic activity and related changes in family structure. More-over, using individual-level data and detailed residential informationwe document intention-to-treat effects, showing that our findings arenot purely driven by compositional effects due to selective migration.

Our study is closely related to recent evaluations of resource ex-traction using quasi-experimental methods and highly disaggregatedwithin-country data, such as the work on the shale energy boom in theUS which typically shows positive effects on the local economy andnegative effects on infant health (Hill, 2018; Currie et al, 2017). Weber(2012) finds small positive effects on wages, employment, and house-hold income when comparing boom and nonboom natural gas countiesacross time. In a similar setting, Jacobsen (2019) also finds increasesin wages (for all occupations) and in housing values. Gopalakrishnanand Klaiber (2014), on the other hand, show that homes that rely onwell water located within 0.75 miles of the drilling site see a valuereduction of 21.7%. Studying property values closer to and fartheraway from drilling sites in Pennsylvania, Muehlenbachs et al. (2015)find that groundwater-dependent homes are negatively affected whilepiped water homes receive small benefits. Using a similar methodolog-ical approach, Bartik et al. (2019) show not only gains in total income,employment, and wages but also an increase in violent crimes. Fred-eriksen and Kadenic (2020) use municipality-level data from Nordiccountries and show that mine openings increase employment and pop-ulation in affected municipalities. Following the coal boom and bustin the US, Black et al. (2005) find some pro-cyclical employment ef-

174 CHAPTER 4

fects in the locally traded goods sectors. Aragon et al. (2018) studythe flip side of mine openings by estimating the effect of the collapseof the UK coal industry. They uncover an increase in manufacturingemployment for men and a decrease for women, potentially pointingto women being crowded out by men who have lost their employmentin the coal industry. Finally, another related study is Currie et al.(2015), who analyze 1,600 toxic plant openings and closings. Theyfind that housing prices decreased by 11% while the incidence of lowbirth weight increased by 3% as an effect of the plant openings. Inwhat follows, we mimic the empirical design of Currie et al. (2015).

The next section reviews the setting and the data while Section4.3 presents the methodology. Section 4.4 quantifies the effects of theextraction permits, Section 4.5 discusses possible mechanisms, andSection 4.6 concludes.

4.2 Institutional Setting and Data

4.2.1 The process before a mine opening

The right to open mines in Sweden is regulated by the Swedish Min-eral Act (1991:451).2 The process starts with the Chief Mining In-spector granting an exploration permit, giving a company the exclu-sive right to explore whether a certain area is economically viable formining. The Chief Mining Inspector is the head of the Mining Inspec-torate, which is part of the Geological Survey of Sweden (SGU). Inorder to investigate the quality of the finding experimental excava-tion could take place in this phase with a separate permit needed. If acompany with an exploration permit finds mining to be economicallyviable, it applies for an exploitation concession permit.3 If that per-

2This section is based on SGU(2016).3Based on the numbers from 2016-2018, 100-200 exploration permits are

granted each year. However, only about 5 exploitation permits are given eachyear.

4.2. INSTITUTIONAL SETTING AND DATA 175

mit is granted (again by the Chief Mining Inspector), the companyobtains the right to exploit the mineral deposit. An exploitation per-mit is only granted if the Chief Mining Inspector agrees that miningis economically viable. After an exploitation permit is granted, thereis still a need for an environmental permit. The environmental appli-cation is granted by the Land and Environmental Court.4 The finalstep is getting a land- and building permit. That decision is madein collaboration with the county and/or the local municipality, po-tential landowners and other stakeholders. After the final permit isissued, the mine can be opened. However, already after the exploita-tion permit is granted, the local economy is affected. For example,the environmental permit application is thorough and should amongother things contain technical descriptions of the spot, output andproduction technology, hydrogeological investigations to ensure thequality of the fresh water in locality. Moreover, the localization andconstructions prints on dams, buildings and roads including alter-native locations must be included. Clearly, these investigations takeboth central and local resources into account.

Maybe most importantly, there is often a large scale second phaseof experimental excavation (a experimental excavation permit is againneeded) in this phase in order to get further information to plan theproduction process. For example in 2008 the spot "Fäboliden" got allthe permits to start a gold mine. But finance surged and the minedid not open. Eventually the company owning the exploitation rightwent into bankruptcy. The right is now owned by another miningcompany which wants to investigate the quality of the gold ore morebefore sinking a pit. Thus, the company is now applying a large scaleexperimental excavation of over 100 000 tons of to be extracted andanalyzed. Experimental excavation has direct local impacts as the siteneeds to be prepared and infrastructure needs to be put in place.

4While the process of issuing an environmental permit in theory could over-turn the decision to grant an exploitation permit, in practice it rarely does (seePettersson et al, 2015 for more details).

176 CHAPTER 4

4.2.2 Data

We link an individual to each exploitation permit using the longitudeand latitude of the centroid of the exploitation permit and the lon-gitude and latitude for the residence of each individual (and year)provided to us by Statistics Sweden. The sample includes the totalpopulation within the designated areas. For each individual, we es-timate the distance to all 150 exploitation permits granted in theperiod 1994 to 2014.5 Similar to Currie et al. (2015), we include in-dividuals within certain distance bins from each exploitation permit.Specifically, we construct distance bins of 0–30, 0–40, and 0–50 km,which serve as different treatment groups, and a group that resides50–70 km from the permit, as our control group in the baseline analy-sis.6 Thus, for each exploitation permit, we have several yearly paneldatasets including each individual living within the appropriate dis-tance. We then collapse the individual variables into distance-by-yearbins. This implies that some individuals will be included in more thanone "exploitation permit"-distance bin if several exploitation permitsare granted close to where they reside. It also means that if individualsmove, they will be part of the aggregation in other distance-by-yearbins after the move, although in the robustness section, we also esti-mate the intention-to-treat based on the place of residence one yearbefore the permit was granted.

Turning to our data specifically, we present the summary statis-tics in Table 1. Panel A of Table 1 shows summary statistics on meanoutcome variables for different distance bins the year before an ex-ploitation permit was granted. Earnings are 144–149 thousand SEK

5See figure 4.5 in Appendix 4.A for a map over where the granted permits aresituated.

6In order to verify our different definitions of a reasonable treatment area, weuse a government analysis of commuting zones (2013). It shows that 70-90% ofworkers have a <30 km commuting distance. Thus, it is reasonable to begin ouranalysis by defining the treatment group as those living 0-30 km from the centerof the resource.

4.2. INSTITUTIONAL SETTING AND DATA 177

(around 15,000 USD) on average and are stable across columns. Theshare of individuals employed in the ages 18-64 for each distance groupis approximately 88% and is similar across distance bins, including thecontrol distance bin of 50–70 km in the last column. Housing valuesare, unfortunately, not measured at the individual level. Instead, theyare calculated using the average price in the municipality where theperson is located. Again, in particular when relating to the size ofthe standard deviation, the mean of housing prices is approximately370,000 SEK (or 39,000 USD) and is stable across distance bins. Ourlast set of outcomes is motivated by Currie et al. (2015) and measuresearly-life health. In Panel B, we observe the share of children bornwith low birth weight, defined as below 2,500 grams. The share is sta-ble across the columns, at approximately 3%. The same conclusionholds for the other two measures, the share of premature birth (bornbefore week 37) and neonatal deaths (infants dying within 28 days ofbirth).

Last, in Panel C, we show the means and standard deviationsfor sociodemographic variables across distance bins. In general, thedemographic variables are balanced. It is worthwhile noting thatthe number of exploratory permits, capturing the stage precedingthe granting of the exploitation permit, is almost identical acrossall bins implying that the underlying geological features are fairlysimilar across the different treatment groups. Finally, the populationcount is monotonically increasing in columns 1 to 3 to 5 as the areasize increases from 706 to 1,256 to 1,962 square kilometers. Thesize of the control bin is 1,884 square kilometers, and the pop-ulation lies between the population sizes reported in columns 3 and 5.

[Table 1 about here]

178 CHAPTER 4

4.3 Methodology

We follow a difference-in-differences design, similar to the one em-ployed by Currie et al. (2015), to estimate the effect of mineral ex-ploitation permits on a wide range of outcomes as follows:

Yjdt = β0 + β11[Exploitation permit]jt + β21[Near]jd+ β31[Exploitation permit]jt ∗ 1[Near]jd + ηj

+ τt + β4Xjd ∗ Tt + εjdt, (4.1)

where Yjdt denotes the average value of an outcome of interest (em-ployment, wages, housing prices, or health) near exploitation permitj, within distance group d, in year t. There are two observations foreach exploitation permit and year. One observation of the averageoutcome for the distance group d within 30, 40, or 50 km, which isnear the site of exploitation and hence the treated area, and denotedNear. The counterfactual or control group area is the second obser-vation, and is captured within 50–70 km of an exploitation permit.1[Exploitation permit]jt is an indicator variable equal to one for bothdistance groups if an exploitation permit j is granted in t and zerootherwise. 1[Near]jd is an indicator variable equal to one for all yearsand groups in the near category. The parameter β3 of the interactionterm 1[Exploitation permit]jt ∗ 1[Near]jd is the variable of interest,which measures the effect of receiving an exploitation permit on thelocal economy for areas close to the permit compared to areas furtheraway. We also include "exploitation permit"-by-distance fixed effectsηjd, and Xjd ∗ Tt, where the latter denotes demographic controls Xjd

from the year before an exploitation permit was granted interactedwith a quadratic time-trend in Tt.7 Unlike 1[Near]jd the "exploitation

7The number of previous exploration permits provided the year before theexploitation permit was granted are interacted with the quadratic time trend aswell. Just as housing value, exploration permits are calculated on the municipality

4.4. RESULTS 179

permit"-by-distance fixed effects ηjd, separately accounts for each ex-ploitation permit (the treatment and counterfactual groups). Finally,our time fixed effects, τt, are either county-by-year or permit-by-yearfixed effects as in Currie et al. (2015).8 The results shown in themain text will be based on regression weighting by the group-levelcell population size similar to Currie et al. (2015), but we also showunweighted result in Appendix for completeness. We report standarderrors clustered at the relevant exploitation permit level.

The validity of the identification strategy relies on satisfying theparallel trend assumption: areas near and further away from the ex-ploitation permits should have experienced the same trends in ourvariables of interest in the absence of the permit being granted. Toverify this assumption, we present standard event-study graphs thatdisplay the separate difference-in-differences estimates 5 years beforeand after the granting of the mineral exploitation permit (discussedin the next section).

4.4 Results

The event study graphs are depicted in Figures 1 and 2 and are basedon the estimation of two versions of equation (1). In Figure 1 (2), weshow an event study using county-by-year (permit-by-year) fixed ef-fects. The graphs plot annual effects of the exploitation permit, bothbefore it was granted (placebo) and after, with 95 percent confidenceintervals, based on clustered standard errors on the relevant distancegroup. The year before the permit was granted serves as the bench-mark omitted category. The coefficients represent the time profile β3within 0–40 km from the center of the exploitation permit, relativeto 50–70 km from the exploitation permit centroid, conditional on

level.8A county is the equivalent of a US state. Sweden has 24 counties in total.

Permit-by-year is the equivalent of plant-by-year in Currie et al. (2015).

180 CHAPTER 4

permit-by-distance and permit-by-year fixed effects.9In Figure 1, subfigures A and B, we first study local labor mar-

ket outcomes. We see no signs of different pre-trends, and there is animmediate direct positive effect on earnings and employment on theevent date, supporting a causal interpretation. The effect of the per-mit on employment is approximately 0.1–0.2 percentage points, andfor earnings, the effect size is approximately 0.5–1%. Turning to thetemporal effects on housing prices (subfigure C), we find again thatthe validity of the difference-in-differences design seems likely to holdas there is no sign of a violation of parallel trend assumption beforethe permit has been granted. After the exploitation permit is in place,however, housing prices decrease, and the average effect seems to beapproximately 3–5%, although it decreases dynamically.

Following previous work studying the effects of local resourceextraction we next turn to early-life health outcomes. A priori, itis not clear whether there are any adverse effects on health-relatedmeasures before a mine actually opens since the potentialenvironmental damage to ground water or air quality is likely tobe appear once the mineral extraction starts.10 However, there isa literature relating economic activity to health outcomes. Thus,while the effects of pollution might be weaker in the preparationphase, people’s health could be affected through increasedeconomic activity via various channels including increased alcoholconsumption, smoking and job-related stress. However, there is noconsensus on the sign of the effects of increased economic activityon health. Previous studies of the effects of economic shocks onhealth have come to very different conclusions.11 Following Currie

9In Appendix Figure A1, we show the equivalent event study graphs generatedusing unweighted regressions. The patterns are similar. For house prices, our dataare based on average prices for the municipality where the individual is located.

10For the adverse environmental impact of gold mining, see, for example,Aragon and Rud (2016).

11For example, studies pointing to a positive relationship include Ruhm

4.4. RESULTS 181

et al. (2015), we look at the proportion of children born with lowbirth weight, as well as premature births and neonatal deaths. Ascan be seen in subfigures D, E, and F, there seems to exist adversehealth effects after the permit is granted, although the pre-trendsfor premature births suggest that locations about to be granted apermit experience a downward trend in the years leading up to thepermit.

[Figure 1 about here]

Figure 2 displays the other main specification usingpermit-by-year fixed effects and shows that the effects before thepermit is granted are statistically insignificant. Moreover, the effectsizes are similar for earnings, housing prices, low birth weight,and premature birth while the impact is somewhat dampened foremployment and neonatal deaths.

[Figure 2 about here]

Table 2 reports the corresponding main estimates of β3 basedon estimating equation 1. Again, we present the results for our sixoutcomes across Panels A–F. In all regressions, the comparison groupis localities situated 50–70 km from the center of the exploitation,whereas the definition of Near changes across regressions, asshown in the column headings. The odd-numbered columns reportestimates from specifications that include county-by-year fixedeffects, and the even-numbered columns report estimates fromspecifications that use permit-by-year fixed effects. All specifications

and Black (2002), Dehejia and Lleras-Muney (2004), DiTella et al. (2003) andGerdtham and Ruhm (2006). Examples of studies pointing at a negative relation-ship are Dee (2001), Sullivan and von Wachter (2009), Eliason and Storrie (2009),Cotti et al. (2015), Hollingsworth et al. (2017), and Ruhm (2000).

182 CHAPTER 4

include permit-by-distance fixed effects and demographic covariatesinteracted with a quadratic time trend. All results are populationweighted. Table A1 in the Appendix shows that the unweightedregression results are quite similar.

Starting with the employment effects in Panel A, we estimate val-ues ranging from 0.1 to 0.3 percentage points. Interpreting the resultsin column 4, Panel A: if a locality is situated at a maximum distanceof 40 km from the center of the location of the mineral resource thatreceives a permit, then employment increases by 0.3 percentage points(or 0.3% at a mean of 0.88) relative to the control group that is lo-cated 50–70 km away. The point estimates decrease in general whenincreasing the size of the treatment zone in columns 3–6, suggestingthat the effects of the mineral exploitation permit on employmentfade with distance (which is evidence of a dose response). In columns7 and 8, we compare the 0–40 km treatment zone to the same controlarea as before but restrict the sample to a narrower time window.Compared with columns 3 and 4, we see that estimates are smaller,indicating dynamically growing effects over time, consistent with theevent-study graphs depicted in Figure 1. Analyzing the outcome of theregression on annual earnings in Panel B also shows a positive effectof the permit, as earnings increase by 0.6–0.9%, decreasing with thesize of the treatment zone and indicating a dose response. Again, thenarrower time window yields smaller effects in columns 7–8. The pos-itive effects are in line with and similar in magnitude to the findingsin, for example, Jacobsen (2019) and Bartik et al. (2019).

In Panel C, we see a sharp decrease of approximately 2–5% inhousing prices, with similar patterns when we increase the treatmentzone/decrease the time window as before. That housing prices de-crease is consistent with the findings of Currie et al. (2015), Gopalakr-ishnan and Klaiber (2014) and Muehlenbachs et al. (2015). Note alsothat the decrease in housing prices will measure both immediate disu-tility and future discounted utility flows of the final mining activity.

4.5. MECHANISM AND ROBUSTNESS 183

Finally, Panels D to F show the effects on the early-life healthoutcomes. There is clear evidence of negative health effects as theshare of newborns with low birth weight, premature births, andneonatal deaths increases after the mineral exploitation permit hasbeen granted. The estimate for low birth weight in column 3 can beinterpreted as follows: if a locality within 0–40 km of the mineraldeposit experiences the consequences of the exploitation permit,then the share of babies born with low birth weight (less than 2,500grams) increases by 0.1 percentage points compared to the controlzone located further away (50–70 km). Given a mean of 0.029, theincrease is about 3.4% overall.12

[Table 2 about here]

4.5 Mechanism and Robustness

4.5.1 Intention-to-treat estimates

When using repeated cross-sectional data, attrition could pose athreat to the validity of the research design employed in the paper.Specifically, if an individual migrates in or out of the treatmentzone because of the treatment, then all or part of the treatmenteffect we capture could be caused by compositional changes inthe underlying characteristics of the population of interest. Forexample, skilled workers may move to the treatment areas to takeup high-paid jobs. In this case, the treatment causes the movementof skilled workers but not necessarily higher wages because the

12In Appendix Table A1, we also show the same outcomes for the unweightedregressions. The point estimates are similar in magnitude and statistically signif-icant for the labor market outcomes, housing prices and the of share prematuredeaths. For the share of low birth weight babies, the estimates are impreciselymeasured, and for the share of neonatal deaths, the results are not robust to theunweighted regressions.

184 CHAPTER 4

increase in wages is due to high skilled workers who would have hadhigh wages regardless. We note that there is one striking patternin our results that speaks against our estimates on earning andemployment being upward-biased. If highly skilled people movedinto the treated areas, then it is unlikely that house prices wouldfall. Of course, it is possible that house prices would have fallen evenmore if highly skilled people would not have moved. Regardless,since we have annual information on the residential location ofthe entire population, we can estimate the treatment effect basedon where people resided one year before the exploitation permitwas granted via an intention-to-treat (ITT) exercise. By definition,the ITT cannot suffer from compositional bias. However, if peoplemove in and out of an area randomly, that is, without causinga compositional bias, our ITT estimate will be smaller thanthe group-level estimate. Thus, if compositional bias is of littleimportance, we expect the ITT estimates to survive, althoughpotentially attenuated. Table 3 presents the results. The effectsare similar though somewhat smaller compared to those showedin Table 2, suggesting that the results are unlikely to suffer fromcompositional bias.

[Table 3 about here]

4.5.2 Female and male outcomes

Table 4 shows the results on the labor market outcomes brokendown by gender; Panels A and B for women and Panels C and D formen. There are no statistically significant differences between thetwo groups. Although much of the activity during the pre-miningphase involves the construction of infrastructure, where maleworkers tend to be in majority, we also know from studies on mineopenings that the service sector is affected. For example, Kotsadam

4.5. MECHANISM AND ROBUSTNESS 185

and Tolonen (2016) study the effects of mine openings and findevidence of increased female employment and evidence for womenshifting into the service sector.

[Table 4 about here]

Also related to the question of gender-specific effects is whetherthe increased economic activity affects the timing of birth. For exam-ple, improved economic circumstances may affect households’ deci-sions on fertility, which could affect the health of the child. However,when evaluating the effects on the age of the mothers in Table A2in the Appendix, there is no significant relationship between grantingthe exploitation permit and the age of mothers.

4.5.3 Robustness

There are other important robustness checks, and for brevity, we com-ment on them here but refer to the results in the Appendix. First,we have chosen an arbitrary control group 50–70 km away from thecentroid of the permit. Tables A3 and A4 use 50–80 km and 60–80km, respectively. As can be seen, the estimates are not very differ-ent, alleviating concerns that the choice of control group drive thefindings.

Although the event-study graphs typically show an immediate im-pact at time of granting the mineral exploitation permit, we arguethat the exploitation phase has a distinct and meaningful effect onthe local economy. Therefore, it is of interest to exclude those permitareas where mines eventually opened within our sample period. In Ta-ble A5, we estimate our main model excluding those localities wherea mine eventually opened (n=7). The results are very similar, and weconclude that exploitation itself directly affects the local economy.

186 CHAPTER 4

4.6 Conclusion

The phase before actual resource extraction begins directly affects thelocal economy. Credible estimates on the direct impact of these activ-ities are scarce. Using highly disaggregated within-country data fromSweden, we estimate significant causal effects of mineral exploitationpermits on employment, housing prices, earnings, and early-life healthoutcomes. Moreover, we show that the local economic effects are notdriven by compositional bias. Not accounting for the pre-extractionphase could potentially lead to flaws in standard evaluations of theeffects of local resource extraction on the local economy and could beone explanation for why the effects found in the literature are modest.

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190 CHAPTER 4

4.7

Tab

les

Tab

le4.

1:Su

mmarystatistic

s

0-30

km0-40

km0-50

km50

-70km

Mean

SDMean

SDMean

SDMean

SD(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA:Econo

mic

variab

les

Ann

uale

arning

s14

734

148

3314

933

144

31Employ

ment

0.87

70.01

70.87

80.01

50.87

80.01

50.87

40.02

2Hou

sing

value

357

140

365

145

377

149

375

142

Pan

elB:Healthvariab

les

Sharelow

birthweigh

t0.03

00.03

10.02

90.01

80.03

10.01

60.03

40.03

3Sh

areprem

aturebirths

0.04

90.03

20.04

80.02

30.04

90.02

00.05

40.03

3Sh

arene

onatal

deaths

0.00

280.01

440.00

160.00

530.00

180.00

490.00

170.00

82

Pan

elC:Dem

ograph

icvariab

les

Age

422

422

422

423

Sharebo

rnin

Swed

en0.94

0.03

0.94

0.03

0.94

0.03

0.94

0.03

Sharefemale

0.49

0.01

0.49

0.01

0.50

0.01

0.49

0.02

Elementary

0.32

0.06

0.31

0.05

0.30

0.05

0.30

0.05

Second

ary

0.52

0.03

0.51

0.03

0.51

0.03

0.51

0.03

College

0.17

0.05

0.18

0.05

0.19

0.05

0.18

0.04

Exp

loratory

perm

its10

1110

1110

119

9Po

pulatio

n29

,517

44,907

47,648

69,247

77,741

112,24

364

,487

90,373

N(E

xploita

tionpe

rmits

)15

015

015

015

015

015

015

015

0

Notes:A

llsummarystatistic

saremeasuredon

eyear

before

anexploitatio

npe

rmitbe

cameactiv

e.Ann

uale

arning

san

dHou

sing

values

in10

00’s

ofSE

K.A

nnua

learning

san

dEmploymentmeasuredforthepo

pulatio

nag

ed18

-64yearsold.

Low

birthweigh

tisde

fined

asweigh

ingless

than

2,50

0gram

s.Prematurebirthisde

fined

asbe

ingbo

rnbe

fore

week37

.Neona

tald

eath

isdefin

edas

thechild

dyingwith

in28

days

ofbe

ingbo

rn.

4.7. TABLES 191T

able

4.2:

Mainou

tcom

es

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA

:E

mp

loy

men

t

1[Exp

loitationpermit]

×Near

0.003∗

∗∗

0.002

0.003∗

∗∗

0.002∗

0.001∗

∗0.001

0.001∗

∗∗

0.001∗

∗∗

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.000)

(0.000)

Pan

elB

:L

og

earn

ing

s

1[Exp

loitationpermit]

×Near

0.009∗

∗∗

0.006∗

∗∗

0.009∗

∗∗

0.006∗

∗0.005∗

∗∗

0.004∗

∗0.004∗

∗∗

0.004∗

∗∗

(0.002)

(0.002)

(0.002)

(0.002)

(0.002)

(0.002)

(0.001)

(0.001)

Pan

elC

:L

og

ho

usi

ng

valu

e

1[Exp

loitationpermit]

×Near

-0.050

∗∗

∗-0.054

∗∗

∗-0.043

∗∗

∗-0.050

∗∗

∗-0.031

∗∗

∗-0.035

∗∗

∗-0.022

∗∗

∗-0.020

∗∗

∗

(0.012)

(0.012)

(0.010)

(0.011)

(0.009)

(0.010)

(0.007)

(0.007)

Pan

elD

:L

owb

irth

wei

gh

t

1[Exp

loitationpermit]

×Near

0.00087∗

∗0.00087∗

∗0.00103∗

∗∗

0.00104∗

∗0.00106∗

∗∗

0.00130∗

∗∗

0.00174∗

∗0.00158∗

∗

(0.00042)

(0.00044)

(0.00038)

(0.00044)

(0.00037)

(0.00040)

(0.00070)

(0.00073)

Pan

elE

:P

rem

atu

reb

irth

1[Exp

loitationpermit]

×Near

0.00198∗

∗∗

0.00185∗

∗∗

0.00197∗

∗∗

0.00200∗

∗∗

0.00114∗

∗0.00118∗

∗∗

0.00385∗

∗∗

0.00322∗

∗∗

(0.00049)

(0.00051)

(0.00048)

(0.00049)

(0.00045)

(0.00040)

(0.00113)

(0.00108)

Pan

elF

:N

eon

atal

dea

th

1[Exp

loitationpermit]

×Near

0.00036∗

∗∗

0.00033∗

∗∗

0.00036∗

∗∗

0.00030∗

∗∗

0.00024∗

∗∗

0.00021∗

∗∗

0.00063∗

∗0.00063∗

∗

(0.00013)

(0.00012)

(0.00009)

(0.00010)

(0.00008)

(0.00008)

(0.00024)

(0.00027)

Observation

s8,930

8,980

8,938

8,996

8,917

8,996

1,418

1,466

Cou

nty×

YearFE

XX

XX

Permit

×YearFE

XX

XX

Not

es:Thistablereports

regression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicator

variab

le"N

ear"

correspon

dto

amineconcession

within30

km,in

columns

3an

d4,

"Near"

correspon

dsto

aconcession

within40

kman

din

columns

5an

d6,

"Near"

correspon

dsto

aconcession

within50

km.In

columns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbeforean

dafter

amineconcession

permit

becom

esactive.The

compa

risongrou

psarealway

s50-70km

away

from

amineconcession

.The

data

have

beenaggregated

topermit-by-distan

ce-by-year

cellsan

dtheregression

sareweigh

tedby

pop

ulationcellsize.Dem

ograph

iccharacteristicsof

each

distan

cebintheyear

beforeexploitation

permission

isinteracted

withaqu

adratictimetrend.

Stan

dard

errors,clusteredat

theexploitation

permit

level,in

parentheses.

∗

p<

0.10,

∗∗

p<

0.05,

∗∗

∗p

<0.

01

192 CHAPTER 4

Tab

le4.

3:Intention-to-treat

estim

ates

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA

:E

mp

loy

men

t

1[Exp

loitationpermit]

×Near

0.001

0.000

0.001∗

∗0.001

0.002∗

∗∗

0.001∗

∗0.001∗

0.001

(0.001)

(0.001)

(0.001)

(0.001)

(0.000)

(0.001)

(0.000)

(0.000)

Pan

elB

:L

og

earn

ing

s

1[Exp

loitationpermit]

×Near

0.003∗

0.002

0.005∗

0.004

0.005∗

∗0.004∗

0.003∗

∗0.003∗

∗

(0.002)

(0.002)

(0.003)

(0.003)

(0.002)

(0.002)

(0.001)

(0.001)

Pan

elC

:L

og

ho

usi

ng

valu

e

1[Exp

loitationpermit]

×Near

-0.042

∗∗

∗-0.037

∗∗

∗-0.038

∗∗

∗-0.037

∗∗

∗-0.031

∗∗

∗-0.028

∗∗

∗-0.019

∗∗

∗-0.016

∗∗

(0.009)

(0.009)

(0.008)

(0.008)

(0.007)

(0.007)

(0.007)

(0.007)

Pan

elD

:L

owb

irth

wei

gh

t

1[Exp

loitationpermit]

×Near

0.00075∗

0.00063

0.00089∗

∗0.00080∗

∗0.00080∗

∗0.00085∗

∗∗

0.00124∗

0.00081

(0.00039)

(0.00041)

(0.00039)

(0.00037)

(0.00031

)(0.00030)

(0.00072)

(0.00073)

Pan

elE

:P

rem

atu

reb

irth

1[Exp

loitationpermit]

×Near

0.00078∗

0.00064

0.00083∗

0.00074

-0.00000

0.00011

0.00352∗

∗∗

0.00304∗

∗∗

(0.00045)

(0.00050)

(0.00046)

(0.00046)

(0.00043

)(0.00041)

(0.00111)

(0.00108)

Pan

elF

:N

eon

atal

dea

th

1[Exp

loitationpermit]

×Near

0.00021∗

0.00012

0.00027∗

∗∗

0.00021∗

∗0.00006

0.00001

0.00031

0.00034

(0.00011)

(0.00011)

(0.00008)

(0.00009)

(0.00006

)(0.00007)

(0.00024)

(0.00026)

Observation

s8,930

8,980

8,938

8,996

8,917

8,996

1,418

1,466

Cou

nty×

YearFE

XX

XX

Permit

×YearFE

XX

XX

Not

es:Thistablereports

regression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicator

variab

le"N

ear"

correspon

dto

amineconcession

within30

km,in

columns

3an

d4,

"Near"

correspon

dsto

aconcession

within40

kman

din

columns

5an

d6,

"Near"

correspon

dsto

aconcession

within50

km.In

columns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbeforean

daftera

mineconcession

permit

becom

esactive.The

compa

risongrou

psarealways50-70km

away

from

amineconcession

.The

data

have

beenaggregated

topermit-by-distan

ce-by-year

cellsan

dtheregression

sareweigh

tedby

pop

ulationcellsize.Treatmentis

decidedon

eyear

beforean

exploitation

permit.

Dem

ograph

iccharacteristicsof

each

distan

cebintheyear

beforeexploitation

permission

isinteracted

withaqu

adratictimetrend.

Stan

dard

errors,

clusteredat

theexploitation

permit

level,in

parentheses.

∗p

<0.

10,

∗∗

p<

0.05

,∗

∗∗

p<

0.01

4.7. TABLES 193T

able

4.4:

Mainem

ploymentou

tcom

es,b

ygend

er

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA:Fe

maleem

ployment

1[Exp

loita

tionpe

rmit]

×Near

0.003∗∗

∗0.002∗

0.004∗∗

∗0.002∗∗

0.003∗∗

∗0.002∗∗

∗0.001

0.001∗∗

∗

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.000)

(0.000)

Pan

elB:Fe

malelogearnings

1[Exp

loita

tionpe

rmit]

×Near

0.012∗∗

∗0.010∗∗

∗0.013∗∗

∗0.009∗∗

∗0.013∗∗

∗0.011∗∗

∗0.002∗∗

0.003∗∗

∗

(0.002)

(0.002)

(0.003)

(0.003)

(0.002)

(0.002)

(0.001)

(0.001)

Pan

elC:Maleem

ployment

1[Exp

loita

tionpe

rmit]

×Near

0.003∗∗

∗0.002

0.004∗∗

∗0.002

0.002∗∗

0.001

0.002∗∗

0.001∗

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

Pan

elD:Malelogearnings

1[Exp

loita

tionpe

rmit]

×Near

0.013∗∗

∗0.005∗

0.015∗∗

∗0.006∗∗

0.012∗∗

∗0.004

0.005∗∗

∗0.004∗∗

∗

(0.002)

(0.003)

(0.003)

(0.003)

(0.003)

(0.003)

(0.001)

(0.001)

Observatio

ns8,930

8,980

8,938

8,996

8,917

8,996

1,418

1,466

Cou

nty×

Year

FEX

XX

XPe

rmit×

Year

FEX

XX

X

Notes:T

histablerepo

rtsregression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicatorvaria

ble"N

ear"

correspo

ndto

amineconcession

with

in30

km,incolumns

3an

d4,

"Near"

correspo

ndsto

aconcession

with

in40

kman

din

columns

5an

d6,

"Near"

correspo

ndsto

aconcession

with

in50

km.I

ncolumns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbe

fore

andafteramineconcession

perm

itbe

comes

activ

e.The

compa

rison

grou

psarealways50-70km

away

from

amineconcession

.The

data

have

been

aggregated

tope

rmit-by

-distance-by

-yearcells

andtheregression

sareweigh

tedby

popu

latio

ncellsize.T

reatment

isde

cide

don

eyear

before

anexploitatio

npe

rmit.

Dem

ograph

iccharacteris

ticsof

each

distan

cebin

theyear

before

exploitatio

npe

rmission

isinteracted

with

aqu

adratic

timetren

d.Stan

dard

errors,c

lustered

attheexploitatio

npe

rmit

level,in

parenthe

ses.

∗p<

0.10,∗∗

p<

0.05,∗∗

∗p<

0.01

194 CHAPTER 4

4.8

Figures

Fig

ure

4.1:

Event-stud

yestim

ates,c

ounty-by-yearfix

edeff

ects

-.0010.001.002.003.004

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(a)Em

ployment

-.0050.005.01.015

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(b)Lo

gearnings

-.08-.06-.04-.020.02

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(c)Hou

sing

value

-.0020.002.004

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(d)Lo

wbirthwe

ight

-.0020.002.004.006

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(e)Pr

ematurebirth

-.00050.0005.001.0015

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(f)Neona

tald

eath

Notes:T

hese

areeventstud

yplotscreatedby

regressing

theou

tcom

evaria

bleof

interest

inequa

tion(1)on

afullset

oflead

san

dlags

forape

rmit-by

-distance-by

-yearcellwith

the"N

ear"

indicator.

Treatm

entgrou

psareareas0-40

kman

dcontrola

reas

50-70km

from

thespecificexploitatio

npe

rmit.

The

regression

sareweigh

tedby

popu

latio

ncellsize.

The

seregression

specificatio

nsinclud

ecoun

ty×year

FE.S

tand

arderrors

areclusteredat

theexploitatio

npe

rmitlevel.

4.8. FIGURES 195F

igur

e4.

2:Ev

ent-stud

yestim

ates,p

ermit-by-yearfix

edeff

ects

-.002-.0010.001.002

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(a)Em

ployment

-.0050.005.01

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(b)Lo

gearnings

-.08-.06-.04-.020.02

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(c)Hou

sing

value

-.004-.0020.002.004.006

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(d)Lo

wbirthwe

ight

-.0050.005.01

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(e)Pr

ematurebirth

-.002-.0010.001.002

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(f)Neona

tald

eath

Notes:T

hese

areeventstud

yplotscreatedby

regressing

theou

tcom

evaria

bleof

interest

forape

rmit-by

-distance-by

-year

cellon

afullsetof

lead

san

dlags

interacted

with

the"N

ear"

indicator.

Treatm

entgrou

psareareas0-40

kmfrom

thespecificexploitatio

npe

rmit.

Con

trol

grou

psareareas50-70km

from

thespecificexploitatio

npe

rmit.

Dem

ograph

iccharacteris

ticsof

each

distan

cebintheyear

before

exploitatio

npe

rmission

isinteracted

with

aqu

adratic

timetren

d.The

data

have

been

aggregated

tope

rmit-by

-distance-by

-yearcells

andtheregression

sareweigh

tedby

popu

latio

ncell

size.T

hese

regression

specificatio

nsinclud

epe

rmit×

year

FE.S

tand

arderrors

areclusteredat

theexploitatio

npe

rmit

level.

196 CHAPTER 4

4.A

App

endix

Tab

le4.

5:Mainou

tcom

es,u

nweighted

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA

:E

mp

loy

men

t1[Exp

loitationpermit]

×Near

0.003∗

∗0.004∗

∗∗

0.003∗

∗∗

0.003∗

∗∗

0.003∗

∗∗

0.003∗

∗∗

0.002∗

∗0.001∗

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

Pan

elB

:L

og

earn

ing

s11[Exp

loitationpermit]

×Near

0.006∗

0.011∗

∗∗

0.011∗

∗∗

0.010∗

∗∗

0.010∗

∗∗

0.008∗

∗∗

0.005∗

∗∗

0.002∗

(0.004)

(0.003)

(0.002)

(0.002)

(0.002)

(0.002)

(0.002)

(0.001)

Pan

elC

:L

og

ho

usi

ng

valu

e1[Exp

loitationpermit]

×Near

-0.043

∗∗

∗-0.033

∗∗

∗-0.041

∗∗

∗-0.034

∗∗

∗-0.029

∗∗

∗-0.021

∗∗

-0.013

∗∗

-0.007

(0.011)

(0.010)

(0.009)

(0.010)

(0.008)

(0.008)

(0.006)

(0.006)

Pan

elD

:L

owb

irth

wei

gh

t1[Exp

loitationpermit]

×Near

0.00080

0.00143

0.00081

0.00077

0.00052

0.00078

0.00556∗

∗0.00400∗

(0.00126)

(0.00121)

(0.00099)

(0.00092)

(0.00090)

(0.00086)

(0.00237)

(0.00218)

Pan

elE

:P

rem

atu

reb

irth

1[Exp

loitationpermit]

×Near

0.00218

0.00332∗

∗∗

0.00246∗

∗0.00297∗

∗0.00192∗

0.00282∗

∗0.00749∗

∗0.00644∗

∗

(0.00135)

(0.00127)

(0.00122)

(0.00120)

(0.00112)

(0.00110)

(0.00305)

(0.00290)

Pan

elF

:N

eon

atal

dea

th1[Exp

loitationpermit]

×Near

0.00006

0.00022

-0.00012

0.00007

-0.00012

0.00008

0.00080

0.00100∗

(0.00030)

(0.00031)

(0.00018)

(0.00021)

(0.00017)

(0.00018)

(0.00056)

(0.00058)

Observation

s8,930

8,98

08,938

8,996

8,917

8,996

1,418

1,46

6

Cou

nty×

YearFE

XX

XX

Permit

×YearFE

XX

XX

Not

es:Thistablereports

regression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicator

variab

le"N

ear"

correspon

dto

amineconcession

within30

km,in

columns

3an

d4,

"Near"

correspon

dsto

aconcession

within40

kman

din

columns

5an

d6,

"Near"

correspon

dsto

aconcession

within50

km.In

columns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbeforean

dafter

amineconcession

permit

becom

esactive.The

compa

risongrou

psarealway

s50-70km

away

from

amineconcession

.The

data

have

beenaggregated

topermit-by-distan

ce-by-year

cells.

Stan

dard

errors,clusteredat

theexploitation

permit

level,in

parentheses.

∗p

<0.

10,

∗∗

p<

0.05

,∗

∗∗

p<

0.01

4.A. APPENDIX 197T

able

4.6:

Effecton

ageof

mother

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA:Age

ofmothe

rs(pop

ulationweigh

tedregression

s)

1[Exp

loita

tionpe

rmit]

×Near

-0.033

-0.027

-0.019

-0.029

-0.031

-0.024

0.015

0.001

(0.030)

(0.029)

(0.024)

(0.023)

(0.020)

(0.021)

(0.037)

(0.037)

Pan

elB:Age

ofmothe

rs(unw

eigh

tedregression

s)

1[Exp

loita

tionpe

rmit]

×Near

0.001

-0.055

-0.075

-0.056

-0.080

-0.045

-0.088

-0.054

(0.063)

(0.053)

(0.055)

(0.055)

(0.051)

(0.049)

(0.086)

(0.079)

Observatio

ns8,930

8,980

8,938

8,996

8,917

8,996

1,418

1,466

Cou

nty×

Year

FEX

XX

XGruvid×

Year

FEX

XX

X

Notes:T

histablerepo

rtsregression

coeffi

cients

from

18sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicatorvaria

ble"N

ear"

correspo

ndto

amineconcession

with

in30

km,incolumns

3an

d4,

"Near"

correspo

ndsto

aconcession

with

in40

kman

din

columns

5an

d6,

"Near"

correspo

ndsto

aconcession

with

in50

km.I

ncolumns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbe

fore

andafteramineconcession

perm

itbe

comes

activ

e.The

compa

rison

grou

psarealways50-70km

away

from

amineconcession

.The

data

have

been

aggregated

tope

rmit-by

-distance-by

-yearcells

andtheregression

sareweigh

tedby

popu

latio

ncellsize.Dem

ograph

iccharacteris

ticsof

each

distan

cebintheyear

before

exploitatio

npe

rmission

isinteracted

with

aqu

adratic

timetren

d.Stan

dard

errors,c

lustered

attheexploitatio

npe

rmitlevel,in

parenthe

ses.

∗p<

0.10,∗∗

p<

0.05,∗∗

∗p<

0.01

198 CHAPTER 4

Tab

le4.

7:Mainou

tcom

es,c

ontrol

grou

p50-80km

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA

:E

mp

loy

men

t

1[Exp

loitationpermit]

×Near

0.002∗

∗∗

0.001∗

∗0.002∗

∗∗

0.001

0.000

0.001∗

0.001∗

∗0.000

(0.001)

(0.001)

(0.000)

(0.001)

(0.000)

(0.000)

(0.000

)(0.000)

Pan

elB

:L

og

earn

ing

s

1[Exp

loitationpermit]

×Near

0.008∗

∗∗

0.006∗

∗∗

0.008∗

∗∗

0.006∗

∗∗

0.004∗

∗∗

0.005∗

∗∗

0.004∗

∗∗

0.003∗

∗∗

(0.001)

(0.002)

(0.002)

(0.002)

(0.001)

(0.002)

(0.001

)(0.001)

Pan

elC

:L

og

ho

usi

ng

valu

e

1[Exp

loitationpermit]

×Near

-0.055

∗∗

∗-0.055

∗∗

∗-0.045

∗∗

∗-0.045

∗∗

∗-0.028

∗∗

∗-0.037

∗∗

∗-0.023

∗∗

∗-0.018

∗∗

(0.013)

(0.012)

(0.010)

(0.010)

(0.009)

(0.010)

(0.007

)(0.007)

Pan

elD

:L

owb

irth

wei

gh

t

1[Exp

loitationpermit]

×Near

0.00123∗

∗∗

0.00082∗

∗0.00134∗

∗∗

0.00098∗

∗0.00129∗

∗∗

0.00119∗

∗∗

0.00138∗

∗0.00164∗

∗

(0.00040)

(0.00041)

(0.00037)

(0.00044)

(0.00035)

(0.00038)

(0.00068)

(0.00074)

Pan

elE

:P

rem

atu

reb

irth

1[Exp

loitationpermit]

×Near

0.00253∗

∗∗

0.00185∗

∗∗

0.00259∗

∗∗

0.00190∗

∗∗

0.00174∗

∗∗

0.00119∗

∗∗

0.00368∗

∗∗

0.00339∗

∗∗

(0.00053)

(0.00058)

(0.00041)

(0.00045)

(0.00037)

(0.00040)

(0.00102)

(0.00104)

Pan

elF

:N

eon

atal

dea

th

1[Exp

loitationpermit]

×Near

0.00034∗

∗∗

0.00026∗

∗∗

0.00037∗

∗∗

0.00034∗

∗∗

0.00024∗

∗∗

0.00022∗

∗∗

0.00063∗

∗0.00072∗

∗∗

(0.00012)

(0.00010)

(0.00009)

(0.00009)

(0.00007)

(0.00006)

(0.00025)

(0.00027)

Observation

s8,937

8,984

8,945

9,000

8,924

9,000

1,390

1,466

Cou

nty×

YearFE

XX

XX

Permit

×YearFE

XX

XX

Not

es:Thistablereports

regression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicator

variab

le"N

ear"

correspon

dto

amineconcession

within30

km,in

columns

3an

d4,

"Near"

correspon

dsto

aconcession

within40

kman

din

columns

5an

d6,

"Near"

correspon

dsto

aconcession

within50

km.In

columns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbeforean

dafter

amineconcession

permit

becom

esactive.The

compa

risongrou

psarealway

s50-80km

away

from

amineconcession

.The

data

have

beenaggregated

topermit-by-distan

ce-by-year

cellsan

dtheregression

sareweigh

tedby

pop

ulationcellsize.Dem

ograph

iccharacteristicsof

each

distan

cebintheyear

beforeexploitation

permission

isinteracted

withaqu

adratictimetrend.

Stan

dard

errors,clusteredat

theexploitation

permit

level,in

parentheses.

∗

p<

0.10,

∗∗

p<

0.05,

∗∗

∗p

<0.

01

4.A. APPENDIX 199T

able

4.8:

Mainou

tcom

es,c

ontrol

grou

p60-80km

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA

:E

mp

loy

men

t

1[Exp

loitationpermit]

×Near

0.000

-0.000

0.001

-0.001

-0.000

-0.000

0.001

0.000

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.000)

(0.000)

Pan

elB

:L

og

earn

ing

s

1[Exp

loitationpermit]

×Near

0.005∗

∗∗

0.002∗

0.006∗

∗∗

0.003∗

0.002

0.004∗

∗∗

0.003∗

∗∗

0.003∗

∗∗

(0.002)

(0.001)

(0.002)

(0.002)

(0.002)

(0.001)

(0.001)

(0.001)

Pan

elC

:L

og

ho

usi

ng

valu

e

1[Exp

loitationpermit]

×Near

-0.054

∗∗

∗-0.058

∗∗

∗-0.047

∗∗

∗-0.056

∗∗

∗-0.031

∗∗

∗-0.046

∗∗

∗-0.022

∗∗

-0.020

∗∗

∗

(0.012)

(0.011)

(0.011)

(0.011)

(0.010)

(0.011)

(0.009)

(0.008)

Pan

elD

:L

owb

irth

wei

gh

t

1[Exp

loitationpermit]

×Near

0.00134∗

∗∗

0.00086∗

∗0.00135∗

∗∗

0.00077∗

0.00131∗

∗∗

0.00110∗

∗∗

0.00125

0.00154∗

∗

(0.00043)

(0.00037)

(0.00040)

(0.00045)

(0.00041)

(0.00042)

(0.00076)

(0.00077)

Pan

elE

:P

rem

atu

reb

irth

1[Exp

loitationpermit]

×Near

0.00277∗

∗∗

0.00174∗

∗∗

0.00267∗

∗∗

0.00180∗

∗∗

0.00160∗

∗∗

0.00116∗

∗∗

0.00331∗

∗∗

0.00327∗

∗∗

(0.00051)

(0.00046)

(0.00046

)(0.00050)

(0.00042)

(0.00043)

(0.00108)

(0.00103)

Pan

elF

:N

eon

atal

dea

th

1[Exp

loitationpermit]

×Near

0.00020∗

∗0.00010

0.00025∗

∗∗

0.00024∗

∗∗

0.00011∗

0.00014∗

∗0.00069∗

∗∗

0.00066∗

∗

(0.00010)

(0.00010)

(0.00007

)(0.00008)

(0.00006)

(0.00006)

(0.00026)

(0.00026)

Observation

s8,872

8,984

8,880

9,000

8,903

9,000

1,399

1,466

Cou

nty×

YearFE

XX

XX

Permit

×YearFE

XX

XX

Not

es:Thistablereports

regression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

150mineconcession

s.In

columns

1an

d2,

theindicator

variab

le"N

ear"

correspon

dto

amineconcession

within30

km,in

columns

3an

d4,

"Near"

correspon

dsto

aconcession

within40

kman

din

columns

5an

d6,

"Near"

correspon

dsto

aconcession

within50

km.In

columns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbeforean

dafter

amineconcession

permit

becom

esactive.The

compa

risongrou

psarealway

s60-80km

away

from

amineconcession

.The

data

have

beenaggregated

topermit-by-distan

ce-by-year

cellsan

dtheregression

sareweigh

tedby

pop

ulationcellsize.Dem

ograph

iccharacteristicsof

each

distan

cebintheyear

beforeexploitation

permission

isinteracted

withaqu

adratictimetrend.

Stan

dard

errors,clusteredat

theexploitation

permit

level,in

parentheses.

∗

p<

0.10,

∗∗

p<

0.05,

∗∗

∗p

<0.

01

200 CHAPTER 4

Tab

le4.

9:Mainou

tcom

es,e

xcluding

future

mineopenings

0-40

km0-30

km0-40

km0-50

km+/-

2years

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

Pan

elA

:E

mp

loy

men

t

1[Exp

loitationpermit]

×Near

0.003∗

∗∗

0.002

0.003∗

∗∗

0.002∗

0.001∗

∗0.001

0.002∗

∗∗

0.001∗

∗∗

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.001)

(0.000

)(0.000)

Pan

elB

:L

og

earn

ing

s

1[Exp

loitationpermit]

×Near

0.010∗

∗∗

0.006∗

∗∗

0.010∗

∗∗

0.006∗

∗0.005∗

∗∗

0.004∗

∗0.005∗

∗∗

0.004∗

∗∗

(0.002)

(0.002)

(0.002)

(0.002)

(0.002)

(0.002)

(0.001

)(0.001)

Pan

elC

:L

og

ho

usi

ng

valu

e

1[Exp

loitationpermit]

×Near

-0.050

∗∗

∗-0.054

∗∗

∗-0.045

∗∗

∗-0.050

∗∗

∗-0.033

∗∗

∗-0.035

∗∗

∗-0.023

∗∗

∗-0.021

∗∗

∗

(0.012)

(0.012)

(0.010)

(0.012)

(0.009)

(0.010)

(0.007

)(0.007)

Pan

elD

:L

owb

irth

wei

gh

t

1[Exp

loitationpermit]

×Near

0.00095∗

∗0.00088∗

∗0.00126∗

∗∗

0.00111∗

∗0.00130∗

∗∗

0.00148∗

∗∗

0.00185∗

∗∗

0.00151∗

∗

(0.00042)

(0.00044)

(0.00038)

(0.00045)

(0.00036)

(0.00041)

(0.00068)

(0.00071)

Pan

elE

:P

rem

atu

reb

irth

1[Exp

loitationpermit]

×Near

0.00220∗

∗∗

0.00186∗

∗∗

0.00225∗

∗∗

0.00206∗

∗∗

0.00136∗

∗∗

0.00131∗

∗∗

0.00406∗

∗∗

0.00344∗

∗∗

(0.00051)

(0.00052)

(0.00048)

(0.00050)

(0.00045)

(0.00042)

(0.00115)

(0.00109)

Pan

elF

:N

eon

atal

dea

th

1[Exp

loitationpermit]

×Near

0.00038∗

∗∗

0.00035∗

∗∗

0.00040∗

∗∗

0.00032∗

∗∗

0.00028∗

∗∗

0.00024∗

∗∗

0.00066∗

∗∗

0.00069∗

∗

(0.00013)

(0.00012)

(0.00010)

(0.00010)

(0.00008)

(0.00008)

(0.00025)

(0.00027)

Observation

s8460

8520

8460

8520

8437

8520

1338

1386

Cou

nty×

YearFE

XX

XX

Permit

×YearFE

XX

XX

Not

es:Thistablereports

regression

coeffi

cients

from

48sepa

rate

regression

s,from

asampleof

143mineconcession

s.In

columns

1an

d2,

theindicator

variab

le"N

ear"

correspon

dto

amineconcession

within30

km,in

columns

3an

d4,

"Near"

correspon

dsto

aconcession

within40

kman

din

columns

5an

d6,

"Near"

correspon

dsto

aconcession

within50

km.In

columns

7an

d8,

thesampleremoves

observations

morethan

twoyearsbeforean

dafter

amineconcession

permit

becom

esactive.The

compa

risongrou

psarealway

s50-70km

away

from

amineconcession

.The

data

have

beenaggregated

topermit-by-distan

ce-by-year

cellsan

dtheregression

sareweigh

tedby

pop

ulationcellsize.Dem

ograph

iccharacteristicsof

each

distan

cebintheyear

beforeexploitation

permission

isinteracted

withaqu

adratictimetrend.

Stan

dard

errors,clusteredat

theexploitation

permit

level,in

parentheses.

∗

p<

0.10,

∗∗

p<

0.05,

∗∗

∗p

<0.

01

4.A. APPENDIX 201F

igur

e4.

3:Ev

ent-stud

yestim

ates,c

ounty-by-yearfix

edeff

ects

usingun

weighted

regression

s

-.004-.0020.002

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(a)Em

ployment

-.015-.01-.0050.005.01

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(b)Lo

gearnings

-.06-.04-.020.02

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(c)Hou

sing

value

-.0050.005.01.015

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(d)Lo

wbirthwe

ight

-.0050.005.01.015

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(e)Pr

ematurebirth

-.0010.001.002.003

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(f)Neona

tald

eath

Notes:T

hese

areeventstud

yplotscreatedby

regressing

theou

tcom

evaria

bleof

interest

forape

rmit-by

-distance-by

-year

cellon

afullsetof

lead

san

dlags

interacted

with

the"N

ear"

indicator.

Treatm

entgrou

psareareas0-40

kmfrom

thespecificexploitatio

npe

rmit.

Con

trol

grou

psareareas50-70km

from

thespecificexploitatio

npe

rmit.

Dem

ograph

iccharacteris

ticsof

each

distan

cebintheyear

before

exploitatio

npe

rmission

isinteracted

with

aqu

adratic

timetren

d.The

data

have

been

aggregated

tope

rmit-by

-distance-by

-yearcells.T

hese

regression

specificatio

nsinclud

ecoun

ty×year

FE.S

tand

arderrors

areclusteredat

theexploitatio

npe

rmitlevel.

202 CHAPTER 4

Fig

ure

4.4:

Event-stud

yestim

ates,p

ermit-by-yearfix

edeff

ects

usingun

weighted

regression

s

-.0020.002.004.006

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(a)Em

ployment

-.01-.0050.005.01.015

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(b)Lo

gearnings

-.06-.04-.020.02

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(c)Hou

sing

value

-.010.01.02

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(d)Lo

wbirthwe

ight

-.010.01.02.03

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(e)Pr

ematurebirth

-.006-.004-.0020.002.004

-5-4

-3-2

-10

12

34

5Ye

ars

to/fr

om e

xplo

itatio

n pe

rmit

(f)Neona

tald

eath

Notes:T

hese

areeventstud

yplotscreatedby

regressing

theou

tcom

evaria

bleof

interest

forape

rmit-by

-distance-by

-year

cellon

afullsetof

lead

san

dlags

interacted

with

the"N

ear"

indicator.

Treatm

entgrou

psareareas0-40

kmfrom

thespecificexploitatio

npe

rmit.

Con

trol

grou

psareareas50-70km

from

thespecificexploitatio

npe

rmit.

Dem

ograph

iccharacteris

ticsof

each

distan

cebintheyear

before

exploitatio

npe

rmission

isinteracted

with

aqu

adratic

timetren

d.The

data

have

been

aggregated

tope

rmit-by

-distance-by

-yearcells.T

hese

regression

specificatio

nsinclud

epe

rmit×

year

FE.S

tand

arderrors

areclusteredat

theexploitatio

npe

rmitlevel.

4.A. APPENDIX 203

Figure 4.5: Map over exploration permits 1994-2014

Active permits 1994-2014

Notes: This map shows the geographical placement of exploration permits grantedby The Chief Mining Inspector 1994-2014.

204 SWEDISH SUMMARY

Sammanfattning

Staten har en omfattande påverkan på sysselsättning, löner och ar-betstid. För det första är den offentliga sektorn arbetsgivare med endirekt påverkan på vissa arbetares löner, arbetstid, och arbetsvillkor.I Sverige är detta ett viktigt sätt genom vilket det offentliga kanpåverka anställningsvillkoren, eftersom en tredjedel av alla arbetare äranställda inom den offentliga sektorn. För det andra beskattar statensina medborgare. Skatter påverkar indirekt sysselsättningen och valetav antalet arbetade timmar. För det tredje beslutar staten, förutomom skatter, om de institutioner som påverkar val och möjligheter påarbetsmarknaden för medborgarna. Denna avhandling består av fyrafristående kapitel som vart och ett fokuserar på några av de olika sättsom det offentliga kan påverka sysselsättning, löner, och arbetstid.

Det första kapitlet i denna avhandling, "Right to Work Full-time" Policies and Involuntary Part-time Employment, tar sigan den offentliga sektorn som arbetsgivare. I detta kapitel studerarjag effekten av en policyförändring som genomförts i svenska kom-muner. Under 2000-talet beslutade svenska kommuner att införa "rätttill heltid" för sina anställda. Denna policy gav kommunalt anställdaomvårdnadsarbetare rätten att, inom vissa gränser, välja hur mångatimmar de ville arbeta. Denna policy utvärderas med hjälp av endifference-in-differences-strategi. Resultaten från utvärderingen visaratt tio procent av de deltidsanställda väljer att gå upp till heltid närde får möjligheten. Studien visar också att förändringarna i avtalade

205

206 SWEDISH SUMMARY

timmar främst kommer från att arbetare med kontrakt på <75 %av ett heltidskontrakt beslutade att öka sina avtalade timmar. Efteratt kommunerna beslutade att införa "rätt till heltid" för omvård-nadsarbetare minskade personalomsättningen i sektorn medan tjän-stgöringstiden ökade, vilket tyder på att policyn var populär.

Det faktum att offentliga omvårdnadsarbetare ändrade sina av-talade arbetstimmar när de fick möjlighet visar att en betydandeminoritet av dem tidigare inte kunnat arbeta så mycket som de ön-skat. Detta indikerar i sin tur att kommunala arbetsgivare inom denoffentliga omvårdnadsssektorn i viss mån kan agera som monopson-istiska arbetsgivare. I Sverige är nästan 18 procent av alla arbetareanställda i den offentliga sektorn på kommunnivå, och av dessa är38 procent offentliga omvårdnadsarbetare. Således kan en betydandedel av arbetsmarknaden karakteriseras som monopsonistisk (i vidmening).

Det har funnits en oro bland politiker på lokal nivå att omvårdnad-sarbete inom kommunen inte är tillräckligt attraktivt för att möta denlångsiktiga efterfrågan på arbetskraft. Detta kapitel visar att dennaoro till viss del kan vara berättigad. Eftersom arbetsgivare inom of-fentlig omsorg kan agera som monopsonister kan det leda till billi-gare anställningslösningar på kort sikt och brist på arbetstagare pålång sikt. Detta kapitel visar att eftersom personalomsättningen min-skade och tjänstgöringstiden ökade på grund av införandet av "rätt tillheltid" är det möjligt för lokala myndigheter att ändra politik på ettsådant sätt att offentliga anställningar blir mer attraktiva. En sistapunkt, vilken leder fram till nästa kapitel i avhandlingen; dessa resul-tat tyder på att vissa arbetare är begränsade i sina val av arbetadetimmar.

Det andra kapitlet i denna avhandling, Hours Constraints andTax Elasticity Estimates – Evidence from Swedish PublicCare Workers, fokuserar på hur vi mäter skatteelasticiteter. Skattbehövs för att det offentliga ska kunna utföra sina uppgifter. Sam-

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tidigt finns ett problem med att skatter riskerar att påverka arbet-skraftsutbudet negativt. För att skattepolitiken ska kunna hjälpastaten att nå sina mål är det viktigt att förstå hur, och hur mycket,skatter påverkar arbetskraftsutbudet. Empiriska uppskattningar avskattelasticiteten är därför avgörande att studera och förstå för attkunna bestämma den optimala skattenivån. En viktig pusselbit för attkunna beräkna skatteelasticiteter är att förstå om, och hur mycket,optimeringsfriktioner påverkar empiriska uppskattningar av skattee-lasticiteten. Det finns en oro att empiriskt uppskattade skatteelas-ticiteter innehåller beräkningsfel på grund av optimeringsfriktionersom arbetare möter på arbetsmarknaden. Hittills finns det begränsadkunskap om vad dessa optimeringsfriktioner består av. Detta kapi-tel ger insikt i en del av optimeringsfriktionens svarta låda, nämligenarbetstidsrestriktioner.

Med hjälp av föregående kapitels "rätt till heltid"-policys, vilkalyfte restriktioner i val av arbetade timmar, beräknar jag skillnadeni skatteelasticiteter mellan offentliga omvårdnadsarbetare som är be-gränsade i sitt val av arbetade timmar jämfört med de som inte ärbegränsade. Arbetare som inte är lika begränsade i sitt val av ar-betade timmar borde ha större uppskattade skattelasticiteter än ar-betare som inte fritt kan välja arbetade timmar. Anledningen tilldetta är att de som är begränsade i sina val inte bör kunna rea-gera på skatter genom att förändra sitt arbetsutbud på kort sikt,medan de som fritt kan välja antalet arbetade timmar kan justerasitt arbetsutbud. Om arbetstidsrestriktioner leder till stora mätfel iempiriskt beräknade skatteelasticiteter bör offentliga omvårdnadsar-betare i "rätt till heltids"-kommuner uppvisa högre skatteelasticiteterän deras motsvarighet i kommuner som inte infört "rätt till heltid".

Att någon typ av optimeringsfriktion påverkar empiriska uppskat-tningar av skattelasticiteten är etablerat i litteraturen. Frågan är vaddessa optimeringsfriktioner består av. Arbetstidsrestriktioner är enkandidat, och brist på information eller förståelse för skattesystemet

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är en annan. Det är viktigt att kunna skilja mellan dessa två op-timeringsfriktioner, eftersom de kan leda till olika långsiktiga kon-sekvenser. Arbetstidsrestriktioner är en kortvarig friktion som kom-mer att leda till underskattning av skatteelasticiteten, då arbetarefortfarande kommer att reagera fullt ut på skatter på lång sikt. Bristpå information eller förståelse för skattesystemet kan å andra sidanpåverka hur arbetare reagerar på skatter både på kort och lång sikt.Om arbetare inte håller sig uppdaterade på skattesystemet på korteller lång sikt kommer de inte heller att reagera på skatter, vilketger låga empiriska skatteelasticiteter. Så länge informationsbristen ärbeständig kommer den låga empiriska skatteelasticiteten vara en kor-rekt uppskattning av hur mycket arbetsutbudet påverkas av skatter.Då dessa olika optimeringsfriktioner leder till olika slutsatser om po-tentiella mätfel i den empiriska skattelitteraturen så är det viktigtatt kunna separera olika optimeringsfriktioner, som arbetstidsrestrik-tioner och informationsbrist.

Med hjälp av bunchingmetoden, och en stor marginalskatteförän-dring i det svenska skattesystemet, visar jag att det inte finns någonmätbar skillnad i hur offentliga omvårdnadsarbetare med olika arbet-stidsrestriktioner reagerar på skatter. Nollresultatet pekar mot slut-satsen att arbetstidsrestriktioner inte påverkar empiriska beräkningarav skattelasticiteten för denna grupp av arbetare.

Det tredje och fjärde kapitlet i denna avhandling går in på tvåspecifika institutioner och policys som kan påverka arbetsutbud ocharbetsvillkor. Det tredje kapitlet, Restricting Residence Permits– Short-run Evidence from a Swedish Reform, skrivettillsammans med Peter Skogman Thoursie och Björn Tyrefors,utvärderar en viktig del av den svenska integrationspolitikensom bestämmer om tillfälliga eller permanenta uppehållstillståndska beviljas till asylsökande. Integrationsfrågan har fått storuppmärksamhet i och med ökningen av flyktingar som anländetill EU under det senaste decenniet. Med klimatförändringar kan

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vi dessutom räkna med att denna fråga kommer att bli ännuviktigare i framtiden. Detta kapitel besvarar frågan om hur två olikatyper av uppehållstillstånd, tillfälliga och permanenta, påverkarintegrationen för flyktingar. Eftersom det är omöjligt att beviljaasyl till en flykting utan att ge någon typ av uppehållstillstånd,kommer det politiska valet att bevilja tillfälliga eller permanentauppehållstillstånd påverka alla flyktingar och hur det i sin turpåverkar integrationen blir därför viktigt att studera.

Med hjälp av en policyförändring i juni 2016, där Sveriges riksdagbeslutade att begränsa beviljandet av permanenta uppehållstillståndför asylsökande i Sverige, använder detta kapitel en regression dis-continuity design där vi följer flyktingarna under de första åren efterankomst. Denna första studie analyserar effekten på flyktingar som är25-65 år gamla och finner positiva effekter på utbildning och sysselsät-tning av att få ett tillfälligt istället för permanent uppehållstillstånd.En möjlig förklaring till detta resultat är att den svenska lagstiftnin-gen ger arbetsincitament för asylsökande med tillfälligt uppehållstill-stånd. En viktig del av den svenska lagstiftningen är att flyktingarmed tillfälligt uppehållstillstånd kan få ett permanent uppehållstill-stånd genom att arbeta. Vi har ännu inte genomfört en studie påyngre individer, eftersom alltför få har hunnit få betyg från grund-skolan för att göra det. Vidare kommer vi i framtiden att undersökahälsoeffekterna för individer som får tillfälligt istället för permanentuppehållstillstånd. Detta återstår att göra. Utan denna informationär det för tidigt att använda denna studie för att ge policyrekom-mendationer, eller dra säkra slutsatser om effekten av olika typer avuppehållstillstånd. Det är också viktigt att notera att tillfälligt up-pehållstillstånd kan ha andra effekter. Ett exempel är att det kanminska antalet asylsökande som anländer till ett specifikt land, vilketkan vara en preferens för landet ifråga.

Det fjärde kapitlet i denna avhandling, Mom and Dad GotJobs: Natural Resources, Economic Activity, and Infant

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Health, skriven tillsammans med Andreas Madestam, EmiliaSimeonova och Björn Tyrefors, studerar en annan institutionellmiljö som kan vara av betydelse för sysselsättning, löner, och hälsa.Vi gräver djupare i gruv- och frackinglitteraturen och de lokalaeffekterna på ekonomi och hälsa av att utvinna naturresurser.Effekterna av lokala ekonomiska chocker, som upptäckten ochutnyttjandet av naturresurser, på arbetsmarknad och hälsa är inteklarlagd. Både positiva och negativa effekter har dokumenteratsi litteraturen. Detta kapitel visar att fasen innan utvinning avnaturresurser inleds påverkar den lokala ekonomin. Vi använderdata från Sverige i kombination med skillnader i tidpunkt och platsför gruvtillstånd i en difference-in-differences-metod. Resultatenvisar en positiv effekt på sysselsättning och inkomst och en negativeffekt på bostadspriserna. Barns hälsa påverkas också negativt, eneffekt som sannolikt drivs av ökad lokal ekonomisk aktivitet snarareän gruvrelaterade externa effekter. Tidigare studier har vanligtvisbaserat sina resultat på att jämföra skillnader före och efter denaktiva fasen av utvinning börjar. Våra resultat tyder på att dessatidigare uppskattningar kan ha underskattat den verkliga effektenav utvinning av naturresurser på ekonomi och hälsa. Sammantagetpekar resultaten på vikten av att inkludera alla faser relateradetill utvinning av naturresurser för att korrekt bedöma den totalapåverkan på lokal ekonomi och hälsa.

Essays on Labor Economics The Role of Government in Labor Supply Choices

 Niklas Blomqvist

Niklas Blom

qvist    Essays on Labor Econ

omics

Dissertations in Economics 2020:1

Doctoral Thesis in Economics at Stockholm University, Sweden 2020

Department of Economics

ISBN 978-91-7911-142-7ISSN 1404-3491

Niklas BlomqvistNiklas holds a B.Sc. and an M.Sc. inEconomics from StockholmUniversity