Essays in Applied Econometrics

Submitted by Ivan Zili´cˇ

Submitted at Department of Economics

Supervisor and First Examiner Dr. Rudolf Winter- Ebmer

Second Examiner Dr. Ren´eB¨oheim Essays in Applied September 2017 Econometrics

Doctoral Thesis to obtain the academic degree of Doctor of Philosophy in the PhD Program (Doktoratsstudium) in Economics

JOHANNES KEPLER UNIVERSITY LINZ Altenbergerstraße 69 4040 Linz, Osterreich¨ www.jku.at DVR 0093696 Statutory declaration

I hereby declare that the thesis submitted is my own unaided work, that I have not used other than the sources indicated, and that all direct and indirect sources are acknowledged as references. This printed thesis is identical with the electronic version submitted.

Ivan Žilic´

signature

place and date

2 ...zahvali Tajnom za sva dobroˇcinstva.

Tin Ujevi´c

3 4 Acknowledgments

This thesis is a result of a ﬁve-year eﬀort and I would like to acknowledge all people who helped me along the way.

First and foremost, I would like to thank my advisor Rudolf Winter-Ebmer as I beneﬁted greatly from his knowledge, experience, and patience. His comments, guidance and support were of invaluable importance, not only for the thesis, but also for my professional development. I thank René Böheim, my co-advisor, whose sharp and constructive comments on early versions of papers presented in this thesis substantially improved their quality. I also thank Gerald Pruckner, a third member of my thesis comettee, who gave a beneﬁcial input on this thesis, especially to the third chapter. I thank all the members of JKU Department of Economics, especially Katrin and Alex, for making the research process an enjoyable experience.

I thank The Institute of Economics, Zagreb where I was employed as a research assistant throughout my PhD studies. Their ﬁnancial support and excellent working environment enabled me to fully devote my time to research. There I also met people who helped me during my studies, especially in the beginnings. I thank all of them, especially Marina, Iva and Rubil, for their friendship and help.

As I did my coursework in Madrid, I thank all the people I met there. To single out a few of them would not be justly, as we had a spectacular time as a group; thank you for everything. I also thank my Zagreb friends—Selma, Rafo, Cupiˇ c,´ Bruno, Vedran, Prebeg, Tiric,´ Vlado, Suljo and Maric—as´ they provided just enough distractions to keep me focused.

I thank my mom, dad, sister and her family for all the sacriﬁces, for always having my back and for being a true inspiration.

And ﬁnally, I thank Marina, for everything. For the help, patience, sacriﬁces, and support. Thank you for your love.

5 Summary

This thesis consists of three chapters. In ChapterI, Effect of forced displacement on health, I analyze health consequences of forced civilian displacement that occurred during the war in Croatia 1991-1995 which accompanied the demise of Yugoslavia. Dur- ing the Serbo-Croatian conflict a quarter of Croatian territory was ceded, 22,000 people were killed, and more than 500,000 individuals were displaced. Using the Croatian Adult Health Survey 2003 I identify the causal effect of forced migration on various dimensions of measured and self-assessed health. In order to circumvent the self-selection into displacement, I adopt an instrumental variable approach where civilian casualties per county are used as an instrument for displacement. I find robust adverse effects on probability of suffering hypertension, tachycardia as well as on self-assessed health and Short Form Health Survey (SF-36) health dimensions. Comparing OLS to IV estimates yields a conclusion of a positive selection into displacement with respect to latent health. Given the likely violation of the exclusion restriction, I use a method which allows the instrument to affect health outcomes directly and conclude that, even with substantial departures from the exclusion restriction, displacement still adversely affects health.

ChapterII, General versus Vocational Education: Lessons from a Quasi-experiment in Croatia, presents a research which identifies the causal effect of an educational reform implemented in Croatia in 1975/76 and 1977/78 on educational and labor market outcomes. High-school education was split into two phases which resulted in reduced tracking, extended general curriculum for pupils attending vocational training and attaching vocational context to general high-school programs. Exploiting the rules on elementary school entry and timing of the reform, I use a regression discontinuity design and pooled Labor Force Surveys 2000–2012 to analyze the effect of the reform on educational attainment and labor market outcomes. We find that the reform, on average, reduced the probability of having university education, which I contribute to attaching professional context

6 to once purely academic and general high-school programs. I also observe heterogeneity of the effects across gender, as for males we find that the probability of completing high school decreased, while for the females we do not observe any adverse effects, only an increase in the probability of having some university education. We explain this heterogeneity with different selection into schooling for males and females. The reform did not positively affect individuals’ labor market prospects; therefore, we conclude that the observed general-vocational wage differential is mainly driven by self-selection into the type of high school.

Do physicians respond to financial incentives is the research question tackeled in Chap- ter III named Do Financial Incentives Alter Physician Prescription Behavior? Evidence from Random Patient-GP Allocations. With co-author Alexander Ahammer I address this question by analyzing the prescription behavior of physicians who are allowed to dispense drugs by themselves through onsite pharmacies. Our identification strategy rests on multiple pillars. First, we use an extensive array of covariates along with multi-dimensional fixed effects which account for patient and GP-level heterogeneity as well as sorting of GPs into onsite pharmacies. Second, we use a novel approach that allows us to restrict our sample to randomly allocated patient-GP matches which rules out endogenous sorting as well as principal-agent bargaining over prescriptions between patients and GPs. Using administrative data from Austria, we find evidence that onsite pharmacies have a small negative effect on prescriptions. Although self-dispensing GPs seem to prescribe slightly more expensive medication, this effect is absorbed by a much smaller likelihood to prescribe something at all in the first place, causing the overall effect to be negative.

7 Contents

List of Figures 11

List of Tables 12

IEﬀect of forced displacement on health 13

I.1 Introduction...... 13

I.2 War and displacement in Croatia...... 16

I.3 Data...... 17

I.4 Empirical strategy...... 22

I.4.1 Identiﬁcation...... 25

I.5 Results...... 28

I.5.1 Sensitivity analysis...... 31

I.6 Conclusions...... 35

I.7 Appendix...... 37

II General versus Vocational Education: Lessons from a Quasi-experiment in Croatia 39

II.1 Introduction...... 39

II.2 Educational reform in Croatia...... 43

II.3 Methodology and data...... 46

II.3.1 Methodology...... 46

II.3.2 Data...... 48

8 II.3.3 Identiﬁcation...... 50

II.4 Results...... 53

II.4.1 Reduced tracking and educational outcomes...... 53

II.4.2 Heterogeneous eﬀects...... 54

II.4.3 Robustness...... 60

II.4.4 Extended general curriculum and labor market outcomes..... 62

II.5 Conclusions...... 64

III Do Financial Incentives Alter Physician Prescription Behavior? Evidence from Random Patient-GP Allocations (with Alexander Ahammer) 67

III.1 Introduction...... 67

III.2 Related literature and our contributions...... 70

III.3 Institutional setting...... 72

III.3.1 Country doctors and onsite pharmacies...... 73

III.3.2 Weekend prescriptions...... 74

III.4 Data...... 75

III.5 Methodology...... 79

III.5.1 Outcome variables...... 79

III.5.2 Identiﬁcation...... 81

III.6 Results...... 84

III.6.1 Heterogeneous eﬀects...... 92

III.7 Conclusions...... 93

9 IV Bibliography 96

10 List of Figures

1 Civilian casualties by county...... 21

2 Violation of exclusion restriction...... 34

3 Changes in high-school education in Croatia during the 1975/76 and 1977/78 reform...... 45

4 Discontinuity in the reform inclusion...... 47

5 Histogram of date of birth...... 52

6 Regression discontinuity graphs for the highest educational attainment.. 55

7 Distribution of education by gender in 2011 for 15+ individuals..... 60

8 Educational outcomes...... 61

9 Years of work...... 64

10 Heterogeneous eﬀects for diﬀerent patient age groups, weekend sample, extensive margin...... 89

11 Heterogeneous eﬀects for diﬀerent GP age groups, weekend sample, extensive margin...... 90

12 Heterogeneous eﬀects for diﬀerent patient education groups, weekend sample, extensive margin...... 91

11 List of Tables

1 Descriptive statistics of health outcomes...... 20

2 First stage and falsiﬁcation...... 26

3 War displacement eﬀects...... 29

4 Sensitivity analysis...... 35

5 Summary statistics...... 37

6 War displacement eﬀects excluding Vukovar-Syrmia County...... 38

7 Descriptive statistics...... 49

8 Eﬀect of the reform on predetermined variables...... 50

9 Results for the highest educational attainment—males...... 58

10 Results for the highest educational attainment—females...... 59

11 Labor market outcomes...... 63

12 Descriptive statistics...... 76

13 Average per patient per year drug expenses for GPs with and without onsite pharmacies...... 84

14 Estimations results for full sample...... 85

15 Estimation results for sample of weekend and holiday prescriptions, extensive margin...... 87

16 Estimation results for sample of weekend and holiday prescriptions, intensive margin...... 88

17 Heterogeneous eﬀects, weekend sample...... 92

12 I.E ffect of forced displacement on health

I.1.I ntroduction

Armed conflicts, along with other dreadful consequences, cause mass civilian displacement. Individuals are forced to leave their homes due to imminent life threatening situations that cause a series of challenges, life changes and losses. According to official UNHCR data, by the end of 2014 the number of forcefully displaced individuals was 59.5 million. In order to motivate a policy that mitigates challenges and adverse conditions that the displaced people face, it is necessary to evaluate the effects of displacement on individuals. Indeed, the literature on consequences of displacement, economic as well as medical, is gaining momentum as micro data sets become more available.

This paper contributes to this literature by analyzing health effects of civil displacement during the war in Croatia 1991-1995, which was a part of larger-scale conflicts in the 1990s that accompanied the break up of Yugoslavia. During the Serbo-Croatian conflict a quarter of Croatian territory was ceded, 22,000 people were killed, and more than 500,000 individuals were displaced, more than 10% of Croatia’s pre-war population.

While health consequences of this conﬂict are an important issue on its own, analyzing displacement caused by this conﬂict may provide broader implications. This war was set in a moderately developed country, very close to Central Europe. In particular, Croa- tia’s GDP per capita in 1990 was 8,123 international 1990 dollars - two thirds of Spain’s (Bolt and Zanden, 2014), while the distance from Croatia’s capital, Zagreb, to Vienna and Munich is less than 400 and 600 km, respectively.

Therefore, civilian displacement during the war in Croatia was diﬀerent than war-induced migration in a developing country. During displacement, most of the people in Croatia were settled to private accommodation (with their relatives or in state-provided hotel and apartment accommodation) and not in refugee camps (Global IDP Database, 2004), there-

13 fore the incidence of communicable diseases, neonatal health problems, and nutritional deficiencies, although increased, was not the most important cause of death (Toole and Waldman, 1997). Therefore, analyzing health consequences of mass civilian migration in a more affluent country, apart from estimating the lower bound of the displacement effect, can offer valuable information to other situations that create mass displacement, such as natural disasters, global warming and big infrastructure projects (Sarvimäki et al., 2009).

In this paper, using the Croatian Adult Health Survey collected in 2003, we identify the causal effect of war-migration on various dimensions of measured and self-assessed health for females. Due to the potential endogeneity of the displacement status, we adopt an IV approach. To the best of our knowledge, this is the first analysis of health effects of displacement that accounts for self-selection. Displacement, although to a great extent a forced action, is partly a result of a decision, and observed patterns of migration during the war in Croatia, in particular, partial flight of population from war-inflicted areas and displacement of individuals who lived far from conflict, validate this claim. Given that we have limited pre-war individual characteristics, we find the assumption that displaced individuals and stayers do not differ in observed and unobserved characteristics too restrictive. Instead, relying on the ethnic pattern of the conflict, which is orthogonal to pre-war health or health-related variables, we use civilian casualties across counties as an instrument for the displacement status, like in Kondylis(2010). As the instrument might affect health directly, we also advance the Kondylis(2010) IV approach by using union of confidence intervals from Conley et al.(2012) which enables us to make inference conclusions even if the exclusion restriction does not hold.

Results indicate that various health dimensions are adversely affected by displacement as 90% interval estimates exclude that there is no effect on the incidence of hypertension, self-assessed health, and both emotional and physical Short Form Health Survey (SF-36) dimensions. Comparing simple estimates and estimates that account for self-selection indicates positive self-selection into displacement with respect to latent health. These results hold for numerous robustness checks, including changing the definition of displacement,

14 changing the composition of control group as well as other sample restrictions.

While we claim that the instrument we use, civilian casualties across 21 counties in Croa- tia, is exogenously determined as the conflict distribution across counties was driven by ethnic structure, the exclusion restriction is very likely to be violated. In particular, civilian causalities, which approximate war intensity, affect health directly and not only through displacement. This concern is amplified by the existing literature, for example Kesternich et al.(2014), but also by unusually large IV estimates, which indicate that estimates are biased towards more adverse effects of displacement. In order to account for the likely violation of the exclusion restriction we use union of confidence interval method from Conley et al.(2012). Results of sensitivity analysis provide compelling evidence that forced displacement may have negative health consequences even with substantial departures from the exclusion restriction.

The literature on economics of forced migration is still in its early stage and it is gaining momentum as micro data sets on war-inflicted areas become available. Ruiz and Vargas-Silva(2013) provide an overview of the literature on the e ffect of displacement on migrating individuals as well as on hosting communities. Although numerous papers show that displacement impacts negatively the economic perspective of an individual,1 Sarvimäki et al.(2009) show that displacement might even induce higher mobility and consequently higher long-run incomes. In the health literature on displacement, there is a consensus that displacement adversely affects the health of individuals.2 For example, Porter and Haslam(2001) provide a meta analysis of papers that analyze psychological consequences of war displacement caused by the demise of former Yugoslavia, all of

1For example, Kondylis(2010), analyzing post-war Bosnia, shows that displaced males are more likely to be unemployed, while displaced females are more likely to drop out of labor force. Eder(2014), also using post-war Bosnia, shows that displaced individuals invest less in their children’s education. Bauer et al.(2013), analyzing the integration of Germans from Eastern Europe, conclude that the first generation of migrants has lower incomes and ownership rates. Fiala(2015), analyzing the displacement in Uganda, concludes that displaced households that returned had a significant drop in consumption and decline in assets. Abdel Rahim et al.(2013), studying displacement in Nuba Mountains in Sudan, conclude that displaced households hold fewer assets and are less involved in production. 2The exception being Abdel Rahim et al.(2013) who find that health status of displaced households in Nuba Mountains in Sudan actually improves due to the behavioral change (hygiene, use of mosquito nets and family planing).

15 which find mental health impairment of displaced and refugee persons. Similar results are also found on the displaced population in other war-inflicted areas, see Steel et al. (2002) and Kuwert et al.(2009). Thomas and Thomas(2004) analyzing key issues of displaced and refugee groups find that most common psychological consequences among those groups include Post Traumatic Stress Disorder (PTSD), depression, somatization and existential dilemmas.

The rest of the paper is organized as follows: section 2 provides background on war and displacement in Croatia, section 3 explains the data set used, section 4 presents the empirical strategy and discusses the identifying assumptions, section 5 gives results and relaxes the exclusion restriction while section 6 concludes the paper.

I.2.W ar and displacement in Croatia

War in Croatia 1991-1995 was part of a larger scale of conflicts on the territory of former Socialist Federative Republic of Yugoslavia (SFRY) in the 1990s. While the political tensions between Croatia and the leadership of SFRY were apparent already in the 1970s and 1980s, the large-scale armed conflict escalated after Croatia’s declaration of independence in June 1991. By the end of 1991 rebel Serbian forces, with the support of Yugoslav People’s Army (YPA), controlled by Serbia, declared the unified Republic of Srpska Kra- jina, taking a quarter of Croatian territory. In 1992 YPA had withdrawn and the United Nations Protective Force (UNPROFOR), as a part of peacekeeping mission, deployed the Serb held territories. In the mid-1995 Croatian army engaged in two large-scale military operations Storm and Flash and reclaimed most of its occupied territory excluding the Eastern part of Slavonia, Baranja and the Western Sirmium which was reintegrated in 1998 under the mandate of the UN Transitional Authority for Eastern Slavonia, Baranja and Western Sirmium (UNATES).

The aftermath of the war in Croatia is as follows: estimates of total casualties are around

16 22,000 individuals,3 while the estimates for the number of refugees and internally displaced persons of all nationalities is more than half a million individuals, which represents a signiﬁcant portion of Croatia’s 4.7 million population in 1991. For example, in March 1993 there were 237,000 individuals internally displaced, while 163,000 went to seek refugee (Repac-Roknic´, 1992). Ethnic Croats were displaced mostly during the 1991 and 1992 as Serbian forces progressed, while ethnic Serbs were displaced during 1995 as Croatian forces engaged in military operations to reclaim occupied territories.4 After the recovery of occupied territories in 1995 and 1998, internally displaced Croats begun their return to their homes. For example, in May 1995 there were 210,592 internally displaced individuals, while in April 2003, at the time when the Croatian Adult Health survey was collected, around 16,000 people in Croatia were still internally displaced (Global IDP Database, 2004).

I.3.D ata

Our main source of data is the Croatian Adult Health Survey 2003 (henceforth CAHS), collected by the Ministry of Health of the Republic of Croatia with consultancy of the Canadian Society for International Health. Sampling was stratiﬁed by six geographical regions in Croatia (North, South, East, West, Central and the capital Zagreb) from which 10,766 households were randomly picked for an interview. In total, 9,070 individuals older than 18 were interviewed, which implies that the response rate was 84.3 %. Individ- uals were interviewed from March to June 2003 with the assistance of 238 visiting nurses. The survey is representative on the national as well as on the regional level. CAHS contains information on measured health outcomes, Short Form Health Survey (SF-36), data on the use of health infrastructure, data on eating, smoking, drinking and exercising habits as well as basic demographics, migrations and labor activities (Vuletic´ and Kern, 2005).

3Živic´ and Pokos(2004) estimate that 22,192 individuals were killed: 8,147 Croatian soldiers, 6,605 Croatian civilians and 1,218 missing persons from Croatia as well as 6,222 Serbian casualties. 4Global IDP Database(2004) reports that total of 220,000 ethnic Croats were internally displaced at the beginning of the war, while 300,000 ethnic Serbs were displaced in 1995.

17 CAHS has three particularities which make it convenient for analyzing the effect of displacement in Croatia. The first one is the explicit identification of individuals that migrated during the 1991-1995 due to the war, a desirable feature in the analysis of forced displacement (Ruiz and Vargas-Silva, 2013).

In particular, forced migrants are identiﬁed using a question: "Did you change your place of living between 1991 and 1995?"; where the ﬁve answers are:

1. Yes, as a refugee/displaced person (8.35%);

2. Yes, for a job (0.21%);

3. Yes, to participate in a war (0.13%);

4. Yes, for some other reason (1.68%);

5. No (89.63%).

We identify displaced individuals as ones who reported being a refugee or displaced person in war period, while the control group is everyone else.5

Second, CAHS contains data on the county of residence just before the war (on March 31, 1991), which we use to construct an instrument in order to address the potential endogeneity of the displacement status. Therefore, we only include individuals who resided in Croatia in pre-war 1991, excluding individuals that lived in other parts of former Yu- goslavia or some other country in 1991. This also implies that the large inﬂux of individuals who came to Croatia ﬂeeing from the war in Bosnia and Herzegovina is not a part of the analysis.

Third, CAHS was collected in 2003, which coincides with the return of the majority of internally displaced individuals to their homes. In particular, out of 220,000 internally

5A disproportionately small number of veterans who reported war participation as migration (500 thousand individuals has veteran status) can be explained by two reasons. The ﬁrst one is the local place of war service, so individuals who served did not change residence, while the second is the fact that participating in the war was not perceived and reported as migration.

18 displaced Croatians during the war, in April 2003 around 16,000 individuals remained displaced (Global IDP Database, 2004), which is similar to the return pattern of displaced individuals in CAHS as in 2003 88.5% of the displaced individuals had the same county of residence as in 1991. Therefore, CAHS captures health dimensions of displaced individuals shortly after they have returned to their homes. Note that CAHS does not include individuals that stayed displaced outside Croatia until 2003.6 As we include only individuals who were living in Croatia in pre-war 1991 and at the time of the survey collection in 2003, thus excluding a large inﬂux of refugees from Bosnia during the 1992-1995 war in Bosnia, as well as the Serbian minority in Croatia that migrated when Croatia reclaimed its occupied territories in 1995, we speculate that we have run our analysis mostly on ethnic Croats (ethnicity is not recorded in the data set). While this may induce sample- selection concerns, we argue that the ethnic key on which the return of displaced has unfolded supports the view that sample-selection is random with respect to health. In particular, prior to the war, in ethnically mixed areas, both ethnicities shared the language, culture and lifestyle.

We restrict our analysis to females, due to the following reasons. First, CAHS does not provide information on the war-veteran status. Therefore, if an individual reported not being displaced and served in the war, (s)he would be included in the control group (non- displaced). As most of the individuals who served in the war are males, we exclude males to avoid including war veterans in the control group. Second, given male war mortality there might be non-random sampling of males into the survey.

CAHS is successful in recording post-displacement outcomes, also it provides limited, yet useful, information prior to displacement (the county of residence), but fails to provide any information during the displacement. In particular, we do not observe the duration of displacement, locus of displacement (whether a person was a refugee or an internally displaced person) nor the type of accommodation during the exile, all of which is relevant

6This includes ethnic Croats, as well as Serbs. In fact the Serbian population in Croatia decreased from 581 thousand in 1991 to 201 thousand in 2001 (Census of Population, 1991, 2001).

19 in explaining the severity of the displacement eﬀect (Porter and Haslam, 2001).

To construct the instrument for the displacement status we utilize information on pre-war county of residence to construct the approximation for war intensities across counties. As an instrument we use the portion of civilian casualties in county population obtained from Živic´(2001). 7 Figure1 shows the number of civilian casualties across counties per 1,000 inhabitants, which is the instrument we use.

To sum up, the treatment group is composed of displaced females, older than 25 at the beginning of the war, most likely ethnic Croats, who recently returned to their pre-war residence; while the control group is composed of their non-displaced counterparts. Table 7 presents the descriptive statistics of outcome variables for females across the displacement status.

Table 1 — Descriptive statistics of health outcomes

Displaced (N = 392) Non-displaced (N = 4,304) Diﬀerence Mean Std. dev. Mean Std. dev. Measured outcomes No hypertension 0.444 0.497 0.483 0.500 –0.039 No tachycardia 0.673 0.470 0.734 0.442 –0.060 No obesity 0.753 0.432 0.732 0.443 0.021 Self-assessed outcomes Healthy 0.355 0.479 0.422 0.494 –0.068∗∗ SF-36 physical –0.160 1.043 0.015 0.995 –0.175∗∗ SF-36 emotional –0.223 1.031 0.020 0.995 –0.243∗∗∗

Note: Column "Diﬀerence" represents a diﬀerence in mean of a given outcome between non-displaced and displaced individual. Details on outcomes can be found in the section below. ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

7Includes killed, exhumed, missing and civilians killed on freed territories during the presence of United Nations Protective Force and United Nations Conﬁdence Restoration Operation in Croatia.

20 Figure 1 — Civilian casualties by county

Civilian casualties by county (per 000) 15 10 5 0

21 I.4.E mpirical strategy

We estimate the eﬀect of displacement on health with a linear two-stage regression model:

0 0 healthi j = β displacedi j + δ xi + θ w j + i j (1) 0 0 displacedi j = λ civilian j + φ xi + ϕ w j + νi j

where healthi j represents a health outcome of a person i who before the war lived in a county j = 1, ..., 21. In particular, we deﬁne six diﬀerent health outcomes healthi j:

1. No hypertension: 1{systolici j < 140 mm Hg & diastolici j < 90 mm Hg}, i.e. an indicator taking the value one if a person i who lived in a county j has systolic and diastolic blood pressure below 140 and 90 mm Hg, respectively.

2. No tachycardia: 1{pulsei j < 100 bpm}, i.e. an indicator taking the value one if a person i who lived in a county j has pulse below 100 beats per minute.

3. No obesity: 1{bmii j < 30}, i.e. an indicator taking the value one if a person i who lived in a county j has Body Mass Index below 30.

4. Healthy: 1{excellenti j | very_goodi j | goodi j}, i.e. an indicator taking the value one if a person i who lived in a county j has reported of being in excellent, very good or good health.

5. SF-36 physical: subjective measure of physical health derived from Short Form (36) Health Survey questionnaire. Higher value indicates better health; standardized to have mean zero and variance one.

6. SF-36 emotional: subjective measure of emotional health derived from Short Form (36) Health Survey questionnaire. Higher value indicates better health; standardized to have mean zero and variance one.8

8More on SF-36 scoring can be found at http://www.rand.org/health/surveys_tools/mos/ 36-item-short-form/scoring.html.

22 The variable displacedi j takes the value one if a person i who before the war lived in a county j was displaced due to war in the 1991-1995 period. In particular, displacedi j takes value one if a person answered the question "Did you change your place of living between 1991 and 1995?" with "Yes, as a refugee/displaced person". xi denotes individual level controls such as age group dummies, education dummies and pre-war region of residence, while w j represents controls on pre-war county level: county GDP per capita and unemployment rate in 1990, county portion of Croatian and Serbian population in 1990 as well as portion of young population (below 20) and old population (above 60).9 Although a richer set of covariates is available—for example, post- displacement labor market outcomes—we avoid using covariates that could be affected by the displacement status. For example, Sarvimäki et al.(2009), Kondylis(2010) and Bauer et al.(2013) show that displacement is significant in explaining income and labor market outcomes in Finland, Bosnia and Herzegovina and Germany. Therefore using post-displacement income and labor market variables as controls would qualify as using bad controls (Angrist and Pischke, 2008). As education is affected by displacement (Eder, 2014), we circumvent this problem by excluding individuals that were younger than 25 at the beginning of the war in 1991. We do not include the present county of residence into estimation as 88.5% of displaced individuals has the same county of residence as before the war.

The variable civilian j, which serves as an instrument for the displacement status, represents civilian casualties during the 1991-1995 war in the individual’s i pre-war county of residence. The variable has 21 distinct values and is, in order to facilitate interpretation and sensitivity analysis, standardized to have mean zero and variance one.

We estimate (1) with 2SLS as OLS estimation of health outcomes on the displacement status might produce biased estimates of the coeﬃcient of interest β. As Czaika and Kis-Katos(2009) and Ibáñez and Vélez(2008) show, even when facing conﬂict and war

9As pre-war region of residence we use 2007-2012 versions of NUTS2 classiﬁcation which divides Croatia in three regions: Northwestern, Central and Eastern and Adriatic.

23 violence, economic conditions play an important role in displacement decisions. Self preservation is a dominant motive, but other motives are not completely suspended. Fol- lowing Ruiz and Vargas-Silva(2013), an individual i will choose displacement if her utility when going into displacement (D) is higher than the utility of staying (S ), i.e. if

UiD > UiS . Note that UiD = f (RiD, YiD, CiD, OiD, ViD), where RiD is the exposure to war violence, YiD are economic opportunities, CiD are costs of moving, OiD are other relevant factors and ViD are unobserved characteristics. Therefore, an individual might self-select into displacement based on latent health and other health related variables thus making the displacement an endogenous covariate and estimates biased.

Endogeneity concerns are amplified by observed war migration. First, there is no whole population flight from war-inflicted ares. For example, even in the most war-affected regions, the east part of Croatia (see Figure 1), we do not observe the displacement of the whole population. In particular, in March 1993, 25.6% of Vukovar-Syrmia county population was displaced. The reasons might be within county disparities of war intensity (not all of the county was occupied) or county ethnic mix (mainly ethnic Croats were displaced), but selection into displacement cannot be a priori discarded. Second, in CAHS there are individuals who reported being displaced even if they resided in the north-west part of Croatia, which was not inflicted by war. Hence, we observe migration that was war-related but not forced, i.e. there are individuals which were not directly exposed to violence, but mere proximity to conflict triggered the displacement decision.

Given that we observe only few pre-war characteristics (education and age) we cannot use any of the selection-on-the-observables methods, therefore, in order to circumvent the endogeneity of the displacement status, we use an instrumental variable approach, as in Kondylis(2010).

24 I.4.1 Identiﬁcation

In order to identify the local average treatment eﬀect (LATE) we need to discuss four assumptions: relevance and the exogeneity of the instrument, exclusion restriction and monotonicity (Angrist and Pischke, 2008).

First stage results presented in the first and second column of Table2 show that, although the instrument is based on 21 counties of pre-war residence, it is highly significant in explaining the displacement decision. In particular, an increase of one standard deviation of killed civilians in a county of residence leads to an increase of the probability of being displaced for 8.5 and 5.9 percentage points in the unconditional and conditional model, respectively. The F statistic on the excluded instrument is 20.94 and 29.37 (without and with covariates) so following Stock et al.(2002) we conclude that the correlation between civilian casualties per county and the displacement status for females is strong enough to exclude weak instrument issues. Third column in Table2 presents results on the displacement decision without the instrument—while other covariates we use do explain the displacement decision, including the instrument increases the total variation explained by the model. The fourth column of the Table2 presents the falsification test, i.e. we estimate the same model but on migration that occurred due to other reasons.10 Given that civilian causalities are not significant in explaining other types of migration implies that our instrument is not picking random variation which reinforces our identification strategy.

To argue the exogeneity of the instrument we need to support the claim that civilian casualties i.e., war intensity, are conditionally random across counties. Although we cannot directly test whether patterns of the conﬂict in Croatia are driven by pre-war health status in counties, inclusion of pre-war county GDP per capita, pre-war county unemployment rates, region dummies as well as pre-war county demographic structure (percentage of Serbian and Croatian population, percentage of young and old population) in 2SLS es-

10This migration is deﬁned if a person answered "Did you change your place of living between 1991 and 1995?" with "Yes, for some other reason".

25 Table 2 — First stage and falsiﬁcation

Displaced Other migration

(1) (2) (3) (4) Killed civilians 0.085∗∗∗ 0.059∗∗∗ −0.001 (0.019) (0.011) (0.002) Education Elementary −0.021 −0.019 0.012∗∗∗ (0.016) (0.017) (0.005) High school −0.010 −0.010 0.021∗∗ (0.023) (0.023) (0.009) College 0.006 0.005 0.018 (0.027) (0.027) (0.013) University −0.036 −0.039∗ 0.009 (0.023) (0.023) (0.007) Missing −0.120∗∗∗ −0.112∗∗∗ −0.012∗∗∗ (0.040) (0.039) (0.004) Age Age 31 – 35 0.018 0.017 −0.010 (0.012) (0.013) (0.010) Age 36 – 40 −0.003 −0.006 −0.022∗∗ (0.015) (0.015) (0.011) Age 41 – 45 −0.001 −0.006 −0.024∗∗ (0.014) (0.015) (0.010) Age 46 – 50 −0.021∗∗ −0.023∗∗ −0.026∗∗ (0.011) (0.011) (0.010) Age 51 – 35 −0.026 −0.026 −0.015 (0.016) (0.017) (0.015) Age 56 – 60 −0.025 −0.028∗ −0.012 (0.015) (0.016) (0.015) Age 61 – 65 0.0004 −0.001 −0.017 (0.020) (0.021) (0.014) Age 66 – 70 0.016 0.013 −0.009 (0.023) (0.023) (0.019) Age 71 + 0.019 0.014 −0.009 (0.031) (0.032) (0.019) Pre-war region of residence Central and Eastern 0.108∗∗ 0.108∗ 0.001 (0.054) (0.061) (0.014) Adriatic 0.043 −0.004 −0.013 (0.044) (0.053) (0.013) Constant 0.083∗∗∗ 0.205 0.091 −0.315 (0.018) (0.834) (1.062) (0.440) Pre-war county controls No Yes Yes Yes Observations 4,696 4,696 4,696 4,696 Adjusted R2 0.095 0.141 0.113 0.007 Note: Standard errors are clustered at the pre-war county of residence. Pre-war county controls include county GDP, unemployment rate, percentage of Serbian and Croatian population, percentage of population below 20 and above 60 years of age, all in pre-war 1990. ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

26 timation supports the conditional exogeneity of the instrument. In order to reinforce the claim that civilian casualties are orthogonal to pre-war health or health related variables, note that the war in Croatia started, and was the most intense, in areas where the ethnic structure was mixed. In particular, war was fought most intensely in the area of the Re- public of Srpska Krajina, which was proclaimed by rebel Serbian forces. Therefore as the local variation of war intensity is determined by ethnic structure, our instrument is as good as random with respect to pre-war health status and health related variables.

We devote our whole sensitivity analysis to address possible violations of the exclusion restriction. In fact, it seems plausible that the instrument, civilian casualties across counties, aﬀects health directly, and not only through displacement, thus producing biased estimates. In the sensitivity analysis section we present the results addressing this issue, using the method from Conley et al.(2012).

Monotonicity is satisfied if all individuals that changed the displacement decision due to war, changed it in the same direction, i.e., if there are no defiers. Intuitively, this implies no individuals should have decided to stay in the county of residence due to the war. Violation of monotonicity leads to biased estimates as IV does not necessarily estimate a weighted average of the underlying individual casual effect (Angrist and Pischke, 2008). Although self-preservation reasoning suggests that individuals would run away from war, monotonicity could be violated. In particular, there might be ethnic Serbs in Croatia that decided to stay in their county of residence just because Republic of Srpska Krajina was proclaimed, which induces a bias in the IV estimates Klein(2010). However, as in 1995, when occupied Croatian territory was reclaimed, a number of ethnic Serbs was displaced from Croatia, and as we are including only individuals that resided in Croatia in 1991 as well as in 2003, it seems unlikely that defiers are included in the analysis. Even if there are some defiers, as ? shows, if a subgroup of compliers accounts for the same percentage of population as defiers, 2SLS procedure estimates LATE for the remaining part of compliers. Intuitively, this weaker condition seems likely to hold in present setting as we expect more people fleeing from the war than staying in war-inflicted areas just

27 because of the war.

I.5.R esults

As pointed out by Sarvimäki et al.(2009) and Bauer et al.(2013), we cannot claim that the estimated effects are mean differences between health outcomes of displaced individuals and the outcomes in a counterfactual situation where displacement did not occur. Instead, due to the general equilibrium effects of war, we define the counterfactual states as (i) being displaced in war-inflicted Croatia and (ii) not being displaced in war-inflicted Croatia.

Results presented in Table3 reveal several insights on the e ffect of displacement on health outcomes. First, there is compelling evidence that displacement has an adverse effect on measured and self-assessed health outcomes. Displacement significantly increases the risk of hypertension and tachycardia and it also reduces self-assessed health and subjective SF-36 indicators. Incidence of obesity is not affected by displacement status.

Second, these effects are substantial in the magnitude, even to a fault. For example, column (2) in IV estimates indicates that displacement increases probability of suffering hypertension for 75.4 percentage points (90% confidence interval is from 60.1 to 90.7 percentage points), it increases the probability of suffering tachycardia for 40.3 percentage points (90% confidence interval is from 3.5 to 77.1 percentage points), decreases self- assessing health as good for 60.9 percentage points (90% confidence interval is from 33.8 to 88.1 percentage points). Likewise, displacement decreases SF-36 physical health for 0.676 standard deviations (90% confidence interval is from 0.349 to 1 standard deviations) and SF-36 emotional health for 0.812 standard deviations (90% confidence interval is from 0.641 to 0.983 standard deviations). The magnitude of these effects, especially compared to OLS estimates, casts a shadow on the IV estimation validity. We argue that a plausible violation of the exclusion restriction—civilian casualties which approximate the war intensity clearly affect health directly and not only through displacement—actually

28 biases the results towards a more adverse eﬀect of displacement. We devote the next section to address this plausible identiﬁcation threat.

Third, comparing the significance and magnitude of effects between estimators yields a conclusion that once we account for selection into displacement the adverse effect tends to increase. This implies that there was, in terms of latent health, a positive selection into displacement. Faced with armed conflict, individuals with better latent health, conditional on age and education level, were more prone to move. This positive selection into displacement pattern is present also in Kondylis(2010) who finds that more "able" individuals, in terms of labor market, were more likely to be displaced.

Table 3 — War displacement eﬀects

OLS estimates IV estimates Variable mean (1) (2) (1) (2) Measured outcomes No hypertension 0.480 −0.039 0.008 −0.457∗∗∗ −0.754∗∗∗ (0.049) (0.043) (0.048) (0.093) No tachycardia 0.729 −0.060 −0.037 −0.268∗∗∗ −0.403∗ (0.056) (0.053) (0.045) (0.224) No obesity 0.734 0.021 0.041∗ −0.087 0.050 (0.025) (0.024) (0.065) (0.095) Self-assessed outcomes Healthy 0.417 −0.068∗∗ −0.054∗∗ −0.371∗∗∗ −0.609∗∗∗ (0.028) (0.023) (0.106) (0.165) SF-36 physical 0.000 −0.175∗∗ −0.125 −0.664∗∗∗ −0.676∗∗∗ (0.086) (0.077) (0.175) (0.199) SF-36 emotional 0.000 −0.243∗∗∗ −0.190∗∗∗ −0.741∗∗∗ −0.812∗∗∗ (0.072) (0.063) (0.132) (0.104) F on excluded instrument — — — 20.938 29.368 Observations — 4,696 4,696 4,696 4,696

Note: Standard errors are clustered at the pre-war county of residence. Each coefficient is the effect of displacement on a different outcome variable. Model (1) is without covariates, while model (2) includes age- group and education controls, pre-war county of residence, pre-war county unemployment rate and GDP per capita as well as pre-war percentage of Serbian and Croatian population and percentage of population below 20 and above 60 years of age. For all the outcomes a negative coefficient represents an adverse effect. ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

In order to reinforce these ﬁndings we also provide results using additional estimates. First concern is that we limit the analysis on individuals who reported conﬂict as the rea-

29 son of their migration. This could induce bias in estimates as ex post rationalization of the migration decision might be influenced by realized outcomes. For example, more "able" individuals might have reported that the reason for migration was to find a job, while less "able" individuals might have reported that it was due to the conflict, which makes reporting a war as a trigger of migration decision an endogenous response. In order to circumvent this issue, we run the same analysis but broadening the definition of forced displacement on all movers. Results are very similar, both in magnitude and significance. Similarly, we re-run the estimations with different definition of control group, excluding the people who reported migration for other reasons, and results turn out almost identical. Given the potential sorting of displaced individuals into particular counties, we also estimate the models using only sample of individuals who have the same county of residence as prior to the war, and again, the results are similar both in magnitude and significance.

Next, we check the robustness of the results by excluding the most war-affected county (Vukovar-Syrmia county). As can be seen from Figure1, Vukovar-Syrmia County (east- ernmost county) is a clear outlier in terms of civilian casualties. After excluding this county, we are left with 4,487 observations (313 displaced and 4,174 controls). Results, shown in Table6, show that displacement has an adverse and significant e ffect on SF-36 physical and emotional health.

We also check we only include counties that were more severely hit by the war. In particular, we exclude counties that had lees than 0.05% civilian casualties, so we include 12 counties with, in total, 1,858 observations (359 displaced and 1,499 controls). Results reinforce the conclusions of the baseline speciﬁcation.12

As already noted, implausibly large magnitude of the eﬀects might come from a violation of the exclusion restriction, which we address in detail in the following section.

11Results are not presented due to brevity. 12Results of all robustness checks are not presented due to brevity.

30 I.5.1 Sensitivity analysis

In this section, we relax the exclusion restriction assumption needed for the identification of IV. The instrument, portion of civilian casualties per county, is reflecting war intensity across counties and there is substantial evidence that exposure to war directly affects long run health dimensions, for example Kesternich et al.(2014) and Akbulut-Yuksel(2014). During the war in Croatia more than 37,000 people were injured (Perkovic´ and Puljiz, 2001), which produces a long-term impact on health. Therefore it might be restrictive to claim that the instrument affects the health exclusively through displacement, especially given that the data set does not record disabilities. In order to address this potential violation of the exclusion restriction we use a method from Conley et al.(2012). Suppose we have one endogenous regressor x, and one instrument z:13

y = βx + γz + (2) x = λz + ν

p If γ = 0, the exclusion restriction holds, but if γ , 0, then βÎV → β + γ/λ. As the instrument might affect the health dimension in the same direction as the displacement, IV estimates are biased towards a more adverse effect of displacement. To account for the possibility of γ , 0 (in particular, for γ < 0) we apply union of confidence interval method from Conley et al.(2012).

In the union of conﬁdence intervals we need to specify the support of γ, G. If the true

γ is γ0 ∈ G, we can run IV estimation on (y − γ0z) = βx + . After obtaining βˆ(γ0) we construct (1 − α) confidence interval for this particular estimate. Repeating this procedure for different γ ∈ G and taking the union of confidence intervals gives us (1−α) confidence interval for the parameter of interest under the violation of the exclusion restriction:

13It is straightforward to accommodate the model for covariates, see the Appendix of the 2007 working paper version of Conley et al.(2012).

31 [ CIN(1 − α) = CIN(1 − α, γ0) (3)

γ0∈ G

For each of the health outcome we restrict γ ∈ [−0.05, 0], where the upper bound is 0 as we discard the possibility that exposure to war affects health in a positive way. In order to provide some insight regarding lower bound of the support of γ, we use a reduced-form estimate for a given health outcome. Note that the γ for which the IV point estimate is zero is actually a reduced-form estimate. Intuitively, if the entire reduced-form estimate is coming from the direct effect of instrument on an outcome—violation of exclusion restriction, i.e. γ—endogenous regressor (treatement) is not affecting the outcome. There- fore, benchmarking the magnitude of violation of exclusion restriction with reduced-form estimate provides insight how sensitive results to violation of exclusion restriction are.

Figure4 presents the results of the sensitivity analysis. X-axis represents γ i.e. degree of violation of the exclusion restriction, Y-axis presents the eﬀect of displacement on a given health outcome, gray area represents the 90% conﬁdence interval given the γ, while the solid black line presents the point estimate; to facilitate interpretation we also add a zero line (red line). Note that the γ for which the point estimate equals zero is actually a reduced-form estimate.

X-axis displays how strong does the violation of the exclusion restriction need to be in order for displacement to turn insignificant (upper bound of 90% confidence intervals hits zero). For example, in the case of variable No hypertension, the effect of displacement turns out to be insignificant when the effect of the instrument is -0.038. This translates to the following interpretation: displacement is insignificant in explaining hypertension if a one standard deviation increase of killed civilians increases hypertension incidence for 3.8 percentage points or more. As the reduced-form estimate for No hypertension is -0.045 we conclude that even with severe departures from exclusion restrictions the displacement still has significant and adverse effect on hypertension.

32 Table4 gives the same results in a more compact way. Column (1) displays reduced form estimates, column (2) shows how strong does the violation of exclusion restriction need to be in order for the displacement effect to turn insignificant, while column (3) shows point estimate of the displacement effect for a γ for which the effect turns insignificant.

Results provide compelling evidence that hypertension, self-assessed health as well as both SF-36 measures—even with severe departures from the exclusion restriction—are still adversely affected by displacement. As already mentioned, displacement is insignificant in explaining hypertension if a one standard deviation increase of killed civilians increases hypertension incidence for 3.8 percentage points or more, which is more than 84% of the magnitude of the reduced form effect. The same is true for self-assessed health and both SF-36 measures, where the γ needs to be 61%, 45% and 66% of the reduced- form estimate, respectively, in order for the effect turn insignificant. Also, looking at the third column of Table4, we see that, once we allow for the instrument to a ffect outcomes directly, the magnitude of the effect of displacement is not so implausible. However, it is hard to determine whether these effects are practically important after allowing for a violation of exclusion restriction.

33 Figure 2 — Violation of exclusion restriction

(a) No hypertension (b) No tachycardia

0.3

0.5 0.0

-0.3 0.0

-0.6 Effect ofdisplacement Effect ofdisplacement -0.5

-0.9

-0.05 -0.04 -0.03 -0.02 -0.01 0.00 -0.05 -0.04 -0.03 -0.02 -0.01 0.00 g g

0.5

0.8

0.0

0.4

-0.5 Effect ofdisplacement Effect ofdisplacement

0.0

-0.05 -0.04 -0.03 -0.02 -0.01 0.00 -0.05 -0.04 -0.03 -0.02 -0.01 0.00 g g

(e) SF-36 physical (f) SF-36 emotional

0.5

0.0

-0.5 -0.5 Effect ofdisplacement Effect ofdisplacement

-1.0 -1.0 -0.05 -0.04 -0.03 -0.02 -0.01 0.00 -0.05 -0.04 -0.03 -0.02 -0.01 0.00 g g

Note: Figure presents the effects of displacement allowing for the violation of the exclusion restriction using the Union of confidence interval, where γ represents the violation of the exclusion restriction in Equation (2). On both panels the black line presents the point estimate, while the gray surface presents the 90% confidence interval of the displacement effect under different degrees of violation of the exclusion restriction.

34 Table 4 — Sensitivity analysis

γ for which the effect Point estimate when the Reduced form estimates turns insignificant effect turns insignificant (1) (2) (3) Measured outcomes No hypertension –0.045∗∗∗ –0.038 –0.124 (0.005) No tachycardia –0.024∗ –0.002 –0.363 (0.012) No obesity 0.003 0 –0.050 (0.006) Self-assessed outcomes Healthy –0.036∗∗∗ –0.022 –0.241 (0.009) SF-36 physical –0.040∗∗ –0.018 –0.369 (0.016) SF-36 emotional –0.048∗∗∗ –0.032 –0.267 (0.012)

Note: Standard errors are clustered at the pre-war county of residence. Reduced form estimates includes all the controls as the column (2) in the IV specification in Table3. Second column shows γ for which the effect of displacement turns insignificant, while the third column shows point estimate for a such γ. ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

I.6.C onclusions

This paper provides an analysis of health consequences of war-related forced displacement that occurred in Croatia during 1991-1995 which accompanied the demise of Yu- goslavia. During the course of the war in Croatia more than half a million of individuals of all ethnicities were displaced, more than 10% of Croatia’s pre-war population. In order to analyze the health eﬀects of displacement, we use Croatian Adult Health Survey (CAHS) collected in 2003, when most of the internally displaced individuals returned to their homes. We take a stand that displacement, although to an extent a forced action, is a form of migration, and thus endogenous. In order to avoid the bias in estimates due to the self-selection into displacement, we adopt an instrumental variable approach. In particular, using a retrospective question on pre-war county of residence, we use civilian casualties per county as an instrument for displacement.

35 Results indicate that various health dimensions are adversely aﬀected by displacement as 90% interval estimates exclude that there is no eﬀect on the incidence of hypertension, self-assessed health, and both emotional and physical Short Form Health Survey (SF-36) dimensions. In addition, we found that IV estimates are quantitatively higher than OLS estimates which indicates positive selection into displacement. These baseline results are supported by numerous robustness checks.

In order to address a likely violation of the exclusion restriction, we also apply a method from Conley et al.(2012), that enable us to perform inference on the e ffect of displacement even if the instrument is directly affecting health outcomes. Results from the union of confidence interval indicate that even with sev ere departures from the exclusion restriction we still find significant adverse effects of displacement. In particular, the violation of exclusion restriction must be more than a half of the reduced-form effect in order for the effect of displacement to turn insignificant. While this indicates that our findings are robust, is hard to determine whether these effects are practically important after allowing for substantial violation of exclusion restriction. This research, enhancing the identification of causal effect of displacement, contributes to the growing literature of conflict consequences, which, unfortunately, will only be growing.

36 I.7.A ppendix

Table 5 — Summary statistics

Mean Std. dev. Min Max Measured outcomes No hypertension 0.480 0.500 0 1 No tachycardia 0.729 0.445 0 1 No obesity 0.734 0.442 0 1 Self-assessed outcomes Healthy 0.417 0.493 0 1 SF physical 0.000 1.000 -2.148 1.599 SF emotional 0.000 1.000 -2.465 1.592 Age Age 26 – 30 0.093 0.290 0 1 Age 31 – 35 0.111 0.315 0 1 Age 36 – 40 0.112 0.315 0 1 Age 41 – 45 0.120 0.325 0 1 Age 46 – 70 0.104 0.305 0 1 Age 51 – 55 0.121 0.326 0 1 Age 56 – 60 0.127 0.333 0 1 Age 61 – 65 0.109 0.312 0 1 Age 66 – 70 0.069 0.253 0 1 Age 71 + 0.033 0.180 0 1 Education No education 0.265 0.441 0 1 Elementary 0.283 0.451 0 1 High school 0.332 0.471 0 1 College 0.055 0.228 0 1 University 0.059 0.236 0 1 Missing 0.006 0.077 0 1 Pre-war region of residence Northwestern 0.394 0.489 0 1 Central and Eastern 0.297 0.457 0 1 Adriatic 0.309 0.462 0 1

37 Table 6 — War displacement eﬀects excluding Vukovar-Syrmia County

OLS estimates IV estimates Variable mean (1) (2) (1) (2) Measured outcomes No hypertension 0.486 −0.035 0.019 −0.453∗∗∗ −0.233 (0.059) (0.049) (0.144) (0.219) No tachycardia 0.733 −0.025 0.002 −0.232 −0.094 (0.055) (0.046) (0.171) (0.277) No obesity 0.735 0.014 0.034 −0.047 0.336∗∗ (0.029) (0.026) (0.140) (0.157) Self-assessed outcomes Healthy 0.423 −0.053∗ −0.046∗ −0.113 −0.068 (0.028) (0.026) (0.143) (0.202) SF-36 physical 0.010 −0.173∗ −0.130 −0.526∗ −0.659∗∗ (0.104) (0.093) (0.318) (0.299) SF-36 emotional 0.011 −0.242∗∗∗ −0.190∗∗∗ −0.677∗∗ −0.796∗∗ (0.086) (0.074) (0.302) (0.374) F on excluded instrument — — — 233.209 109.311 Observations — 4,487 4,487 4,487 4,487

38 II.G eneral versus Vocational Education:Lessons from a

Quasi-experiment in Croatia

II.1.I ntroduction

The debate on general versus vocational education has been an important part of policy makers’ and academics’ agenda. As both educational systems have their benefits, there exists a well-known general-vocational trade-off. In particular, skills acquired by vocational training may ease the transition into the labor market, but may become obsolete at a faster rate; while general education gives access to broader knowledge that can serve as a sound basis for subsequent learning and specialization (Hanushek et al., 2017). Verhaest and Baert(2015) characterize general versus vocational schooling as a trade-o ff between lower risk of bad match persistence later on, and higher employment chance and better match at the start of the career.

Some authors claim that general education is especially important for the fast-changing economy, as individuals can change occupations and adapt new technologies more quickly (Goldin, 2001; Hanushek et al., 2017). Adopting this view suggests that a more general education should pay a labor market premium in transition and post-transition countries. With the fall of socialism and the establishment of market-oriented economies in the 1990s, countries of the Eastern Bloc went through profound institutional and political changes. The economy was affected drastically as business activities turned to different sectors and technologies which translated into different sets of skills required on the labor market. Was a more general education beneficial for individuals in this changing age?

Answering these questions is not an easy task as educational choice suffers from self- selection—comparing labor market outcomes of individuals with general and vocational education would reflect unobserved differences across individuals making the estimates biased (Ryan, 2001).

39 To shed some light on this matter, in this paper we identify the causal eﬀect of a comprehensive high-school reform implemented in Croatia in 1975/76 and 1977/78. Prior to the reform, after completion of eight-year compulsory elementary school pupils, based on their grades and interests, could enroll academic (gymnasium), technical or vocational high school. The reform split high-school education into two phases—the ﬁrst phase, two years of general curriculum common to all students regardless of the school enrolled, and a second phase, which prepared students for a particular profession. This introduced three novelties. Firstly, an extra educational decision as to where to continue the second phase was introduced; therefore, the separation into vocational tracks was postponed, i.e. tracking was reduced. Secondly, individuals could not enter a vocational school directly after an eight-year compulsory elementary school—instead, they needed to attend two additional years of general education. Lastly, all programs, including once academic and general, were given vocational and paraprofessional context. Exploiting elementary school age entry rules and the timing of the implementation of the reform we are able to use regression discontinuity design on pooled Labor Force Surveys 2000–2012.

We test whether reduced tracking affected the highest educational attainment, years of schooling and the field of study. We also analyze if two extra years of general curriculum affected labor market prospects of nongymnasium high-school graduates (technical and vocational high-school graduates) in terms of wages, years of employment, probability of being unemployed as well as the probability of being inactive.

Results indicate that the reform, on average, reduced the probability of having university education. The estimated negative eﬀect is varying from 2.7 to 5.5 percentage points. We argue that this eﬀect came from attaching paraprofessional and vocational context to once general programs. In the old system, gymnasiums were perceived as a preparation for university education, while in the reformed system, gymnasiums de facto existed, but they were associated with some vocation, making graduates of general programs employable. This interpretation is supported by the drop in university enrollment rates.

40 We also observe different effects across gender. For male pupils we find that the probability of completing only elementary school increased, which indicates a high incidence of first-phase dropouts. The first phase was mostly general curriculum, which might have been a challenge for low-ability pupils who would otherwise be able to complete a three- year vocational school. As in the whole sample, we also observe a drop in the probability of having a university education for males.

On the other hand, we do not find any adverse effects for females. The only significant effect is an increase in the probability of attending some university education. We argue that this heterogeneity in the reform effects is driven by different selection into schooling across genders. While most of the males could go to school, a significantly lower portion of females enrolled secondary schooling, due to informal barriers, such as gender and family roles. We argue that these informal barriers selected more-able females into schooling who had no problems completing the first phase, and were actually motivated to continue education after high school. We also observe that a portion of females shifted from teacher education and services into social sciences.

Restricting our sample on nongymnasium high-school graduates, we find that the two additional years of general education did not positively affect individuals’ labor market prospects. This lack of premium on more general education is surprising, given the potential upward bias of the estimates. In particular, as the reform caused a drop in the probability of completing a university, the nongymnasium high school sample contains different ability distributions before and after the reform. We conclude that the observed general vocational wage differential is mainly driven by self-selection into the type of high school.

Although these results are speciﬁc for the socialist Yugoslavia, we believe they carry some external validity. Croatia, at that time a part of former Yugoslavia, had an economic system called “self-managment” where socially owned companies were proﬁt maximizing— labor actually employed capital. This hybrid system had some characteristics of market

41 economies. For example, in the 1960s interregional transfers were reduced and enterprise taxes were lowered in order to further push enterprises towards the market, and banks were established as financial intermediaries (Milenkovitch, 1977). Also, workers received wages in two parts: a fixed wage, based on job evaluation and labor market criteria, and a variable part based on the level of net profits of the enterprise (Wachtel, 1972), which gave profit- and utility-maximizing incentives to firms and individuals.

This paper contributes to the empirical literature on the nexus between additional years of general education and labor market outcomes. For example, Hanushek et al.(2017), using difference-in-differences approach and pooling individuals from 11 countries, provide results that support the general-vocational education trade-off as they find that individuals with general education do initially have worse employment outcomes, but their perspective improves as they get older. On the other hand, research that relies on quasi- experimental evidence contrast these results. Using the educational reform in the 1970s in Romania, Malamud and Pop-Eleches(2010) find that more years of general education did not affect labor market participation and earnings. Oosterbeek and Webbink(2007), analyzing the reform of the Dutch vocational schools, also find no evidence of premium on more general years of schooling. Analyzing a pilot scheme administrated in Sweden that introduced more comprehensive upper secondary education, Hall(2012) finds no e ffect of more general education on university enrollment and earnings, as well as no evidence that attending general education reduces unemployment risk during the 2008–2010 crisis (Hall, 2013).

The rest of the paper is organized as follows: section 2 explains the educational reform in Croatia, section 3 explains the methodology and data, section 4 presents the results, while section 5 the conclusion.

42 II.2.E ducational reform in Croatia

Prior to the reform in the 1970s, education in Yugoslavia, and hence Croatia, was reg- ulated at the federal level by the General Law on Education from 1958. Children enrolled an eight-year compulsory elementary school, on average, at the age of seven. Upon the completion of elementary school, depending on their performance and aptitude, they could continue in one of the following secondary schools: gymnasium, art school, technical school, trade or vocational school, teacher’s school or military secondary school. Duration of the secondary school depended on the type of the school, ranging from three years for trade or vocational schools for skilled workers to ﬁve years for teachers, but averaging around four years. After successfully completing high school and earning a diploma, pupils could enroll into a higher educational institution or enter the labor market (Georgeoﬀ, 1982).

On the tenth Congress of the League of Yugoslav Communists in 1974 the basis for the so-called “directed” education was established. The reform redesigned high-school education abolishing general secondary schooling (gymnasiums), making all secondary education vocation-oriented. In words of Stipe Šuvar, then Secretary of State for Education in Croatia, the educational system was flawed as: “Homo faber and homo sapiens are socially separated, alienated, opposed in the existence of different classes; and the primary purpose of education is to perpetuate these divisions it has, in fact, been developed as a specific ritual which selects a small proportion of the population for the social elites, and places them on a pedestal which is inaccessible to the vast majority of the population.” (Bacevic, 2016). Indeed, “Although any elemetary school graduate may enter gymnasium, in reality it is somewhat restricted by the realities of socio-economic life in Yugoslavia. ...we tend to find the children of the social and political elites in the gymnasium and the children of the general populace in the vocational and technical schools.” (Farmerie, 1972).

Therefore, the objectives of the reform were: (i) a more equal distribution of students from

43 various socio-economic backgrounds enrolled in secondary schools of various types; (ii) a greater emphasis on the development of speciﬁc occupational skills with the goal of easier school to work transition; (iii) a promotion of greater equality of access to education and employment opportunities; and (iv) a closer integration of the schooling system with the needs of the social system and self-management (Obradovic´, 1986).

Under the new educational system, the high school was split into two phases, both ad- ministered at the so-called school centers. The first phase, which lasted for two years, was common for all students irrespective of the type of the secondary school they enrolled. The majority of the first-phase curriculum was general (85% according Obradovic´ (1986)): official language, chemistry, biology, physics, geography, mathematics and history. Selection into the first phase was based on elementary school performance—pupils had to apply and were selected based on the grades form the last two grades of elementary school. Upon the completion of the first phase, students could enter the labor market or continue to the second phase. The second phase was designed to provide vocational preparation. In total, programs for 36 professions and more than 350 occupations were available (UNESCO, 1984), and programs lasted for one or two years. All students who completed the first-phase could apply for any of the second phase programs, but selection was based on the grades from the first phase. All high schools were renamed as school centers associated with some vocation. For example, a mathematical gymnasium was renamed the school center for mathematics and informatics, so programs for general education were still de facto available but were given a vocational or paraprofessional context. For example, upon completing the school center for mathematics and informatics a person would get a vocation titled “technician for mathematics and natural sciences”.

The ﬁrst phase of the new high-school system was implemented in all secondary education in Croatia in the school year 1975/76, for the high-school freshmen, while the second phase was implemented for the same cohort in the school year 1977/78 (UNESCO, 1977). Stylized representation of the reform is depicted in Figure3.

44 Figure 3 — Changes in high-school education in Croatia during the 1975/76 and 1977/78 reform

(a) Before the 1975/76 and 1977/78 reform

(b) After the 1975/76 and 1977/78 reform

Before highlighting the diﬀerences between the reformed and the old schooling, we stress the things that did not change. Firstly, elementary schools remained the only compulsory education. Secondly, selection procedure into the next phase of education remained the same—it was based on performance in the last two years of schooling. This implies that pupils in the ﬁrst phase, like in the prereform high schools, were homogeneous in ability. And lastly, all the educational resources, including teachers and buildings were the same as the new high schools were merely renamed school centers.

The reform did introduce a few important changes. Firstly, an additional educational decision was introduced into the schooling system—a decision of where to continue schooling after the first phase. Both phases could have been attended at the same school center, but pupils could also change the school center after the first phase. Since the first phase con-

45 sisted of a general curriculum, pupils were able to make their educational choice two years later, which implies later separation into vocational tracks. For example, an individual who set their mind on becoming a carpenter would, in a old educational system, make that decision after eight years of elementary school by enrolling a three-year vocational school. In the reformed system, an individual could decide to become a carpenter, enroll the ﬁrst phase, but could then, after being exposed to general subjects, change his/her mind and apply for a diﬀerent vocational program.

The second change was that the pupils were prevented from entering vocational training straight after elementary school. Instead, they needed to go through two additional years of general education before specializing for a particular vocation. This implied that, for example, an individual who would have enrolled a three-year vocational program before the reform, would have had eight years of general education, while the same person in the same vocational program after the reform would have had ten years of general education (the discontinuity in the years of general education is depicted in Figure4). Lastly, all programs, including once academic and general, were given vocational and paraprofessional context.

II.3.M ethodology and data

II.3.1 Methodology

To circumvent the self-selection nature of an educational choice (Bennell, 1996; Ryan, 2001; Malamud and Pop-Eleches, 2010), and hence bias ordinary least squares estimates, we exploit the high-school educational reform. The ﬁrst stage of the reform was implemented in the academic year 1975/76 for high-school freshmen. We combine the timing of the reform, the date of birth and rules for elementary school entry to construct an indicator if the person was included in the reform. In particular, we identify an individual born on January 1, 1961 as an individual who was marginally included in the reform. Figure4 depicts discontinuity in the reform inclusion. This framework enables us to

46 Figure 4 — Discontinuity in the reform inclusion

Individuals born before Individuals born after January 1, 1961 are not in the reform. January 1, 1961 are in the reform. High-school graduates have at least High-school graduates have at least eight years of general education. ten years of general education. They choose their profession They choose their profession after eight years of schooling. after ten years of schooling.

Jul 1958 May 1959 Mar 1960 Jan 1961 Nov 1961 Sep 1962 Jul 1963 use regression discontinuity design (RDD), introduced into the economics literature by Thistlethwaite and Campbell(1960), where the date of birth of each individual is used to construct an assignment variable that discontinuously determines the reform inclusion.

Suppose ci is the distance, in weeks, between individual’s i birth date and January 1, 1961, and let AFTERi = 1 [ci ≥ 0], i.e. an indicator taking value 1 if individual i was born after January 1, 1961. In order to estimate the eﬀects of the reform on educational attainment and labor market outcome yit of an individual i in time t, we estimate:

0 yit = δAFTERi + β Xi + f (ci) + ηt + νit (4)

where Xi is a vector of time-invariant controls (gender and nationality), f (ci) a function of the assignment variable and ηt is control for survey year.

We analyze the effects of the reform with two sets of outcome variables. First, by using all individuals born within a certain time frame, we analyze the effects of the reform on the highest educational attainment, years of schooling and field of education. We do so to explore whether the additional educational decision and hence the reduced tracking affected schooling outcomes.

47 Next, using only nongymnasium high-school graduates, we explore whether more years of general education provided a labor market premium in terms of wages, years of work, the probability of being employed and the probability of being inactive. We do so as the reform can be interpreted as an extension of the general part of curriculum in vocational schools.

In order to avoid misinterpreting nonlinearities around the cutoff as discontinuities, cau- tion regarding the functional form of f (ci) is advised (Angrist and Pischke, 2008). Fol- lowing Lee and Lemieux(2010), we estimate equation (4) semi-parametrically using different ad hoc bandwidths around the cutoff date and modeling f (ci) using polynomials of different order.

II.3.2 Data

Data are obtained by pooling 2000–2012 versions of the Croatian Labor Force Survey (LFS), which contains basic demographic characteristics, labor market outcomes, education variables, and, importantly, date of birth which we use to construct the assignment variable for the regression discontinuity design. We do not observe if an individual was actually included in the reform, so we cannot resort to instrumental variable estimation. We also do not capture information on the school center the individual attended and whether the individual changed the school center between the two phases.

Table7 presents descriptive statistics of pooled data. Note that we restrict the sample to individuals born within three years around the cutoﬀ date of January 1, 1961. We do so to restrict sample to cohorts that cope with similar labor market conditions upon completing education. The left panel of Table7 displays the prereform sample (individuals born between January 1, 1958 and January 1, 1961) while the right panel displays the postreform sample (individuals born between January 1, 1961 and January 1, 1964).

48 Table 7 — Descriptive statistics

Prereform sample (N=11,204) Postreform sample (N=11,170) Mean Std. dev. Mean Std. dev. Predetermined variables Female 0.458 0.498 0.463 0.499 Non-Croatian 0.082 0.274 0.080 0.272 Years of schooling 8 years or less 0.208 0.406 0.180 0.384 10, 11 or 12 years 0.596 0.491 0.615 0.487 16 years 0.090 0.287 0.087 0.282 More than 16 years 0.024 0.153 0.022 0.147 Education level No elementary 0.028 0.166 0.018 0.131 Elementary 0.185 0.388 0.175 0.380 High 0.607 0.488 0.621 0.485 Some university 0.068 0.252 0.081 0.273 University and more 0.111 0.314 0.106 0.307 Field of education* General programs 0.258 0.438 0.206 0.405 Teacher training 0.026 0.159 0.046 0.209 Humanities 0.011 0.105 0.010 0.102 Social sciences 0.198 0.398 0.206 0.405 Life sciences 0.015 0.120 0.022 0.146 Engineering 0.324 0.468 0.311 0.463 Agriculture 0.019 0.136 0.037 0.189 Health care 0.049 0.215 0.057 0.231 Services 0.101 0.301 0.104 0.305 Labor market outcomes Log hourly wage 2.943 0.788 2.962 0.753 Years of work 24.552 5.823 21.388 5.813 Employed 0.782 0.413 0.799 0.401 Nonactive 0.013 0.115 0.015 0.122 Note: Prereform sample is restricted to individuals born between January 1, 1958 and January 1, 1961, while the postrefom sample contains individuals born between January 1, 1961 and January 1, 1964. * question regarding the ﬁeld of education is available in Labor Force Surveys 2004 onwards (sample size of the prereform sample is N=8,296, while for the postrefom sample is N=8,360).

49 II.3.3 Identiﬁcation

Table 8 — Eﬀect of the reform on predetermined variables

Predetermined variable Female Non-Croatian 3 year window (N=22,374) Linear spline 0.008 −0.0002 (0.021) (0.0004) Quadratic spline −0.001 0.002 (0.030) (0.001) Cubic spline 0.059 −0.0002 (0.039) (0.001) Quartic spline 0.063 −0.002 (0.050) (0.002) 2 year window (N=15,065) Linear spline 0.003 0.002 (0.024) (0.002) Quadratic spline 0.038 −0.001 (0.035) (0.002) Cubic spline 0.066 0.0003 (0.049) (0.001) Quartic spline 0.062 −0.001 (0.062) (0.001) 1 year window (N=7,480) Linear spline 0.038 −0.0004 (0.034) (0.0003) Quadratic spline 0.044 −0.0003 (0.053) (0.0004) Cubic spline 0.139∗ 0.001 (0.073) (0.001) Quartic spline 0.167 −0.0003 (0.105) (0.001)

Note: Standard errors clustered at the week of birth are in the brackets. Each cell represents a different regression and presents the coefficient on the variable AFTER which takes value 1 if the individual was born after January 1, 1961, and 0 otherwise. Window width denotes ± years around the cutoff date. Covariates include female and non-Croatian dummy (excluding the female control if the outcome is "female", and vice versa) as well as dummies for the survey years. Significance levels: ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

Regression discontinuity designs rely on the assumption that individuals cannot precisely

50 manipulate their assignment variable and thus completely control their inclusion into the treatment (Lee and Lemieux, 2010). As the educational reform was announced in 1974 and implemented in the academic year 1975/76, and the assignment variable is predetermined, it seems rather implausible that individuals could manipulate the inclusion into the reform. We do however, explore whether there are discontinuities in the predetermined variables to reinforce the notion that the reform did randomly split the population. Table 8 plots the results of estimation of equation (1) on two predetermined variables: if a person is female; if a person is not Croatian. In order to present a comprehensive picture of the estimates we use four different specifications of f (ci) and a set of bandwidths ranging from one to three years. Results indicate that there was no systematic significant change in predetermined variables around the reform cutoff.

We also perform the sorting test from McCrary(2008) to see whether individuals group on the one side of the cutoff which would raise concerns regarding the identification. As the p-value on the test is 0.178 we conclude that there was no sorting on one side of the cutoff and thus the reform can be viewed as a quasi-experiment. Figure5, representing the histogram of birth dates, supports this conclusion.

The relationship between the assignment variable and the treatment status might not be deterministic, there might be noncompliers—individuals who should have been, based on the date of birth, included in the reform, but were not and vice versa. For example, parents could postpone or advance elementary school enrollment of their child, or a child could be retained in a grade or even skip one. As we do not know whether an individual was indeed included in the reform we cannot exploit the assignment variable as an instrument for reform participation so our analysis should be viewed as intention-to-treat eﬀect.

However, we argue this type of noncompliance is not a threat to our identiﬁcation; given the short lag between the announcement of the reform and actual implementation, it seems plausible that portion of these noncompliers did not change with the reform.

51 Figure 5 — Histogram of date of birth

0.075%

0.050%

0.025%

0.000%

1958 1959 1960 1961 1962 1963 1964 Date of birth

52 II.4.R esults

II.4.1 Reduced tracking and educational outcomes

In this section we present the effects of reduced tracking on the highest educational attainment, years of schooling, and the field of education. As can been seen from Figure6, results indicate stable portions of different educational attainments before and after the reform. The biggest change was in the portion of people having some university education, and university education and more.

We also test the robustness of these results using different windows of observations and different specifications of f (ci) (tables omitted for brevity). Figure 6a, where the indicator— if a person has no elementary school—is taken as an outcome, should be considered as a placebo test. The reform redesigned only high-school education so no effect should be found in this outcome. Therefore, the absence of a statistically significant effect in our results reinforces our identification strategy.

Figure 6b shows no effect on the probability of completing only elementary school imply- ing that the introduction of general-curriculum first phase did not increase the incidence of high-school dropouts. For example, pupils that enrolled carpenter programs had to cope with the same general subjects as pupils in the physics programs so some first-phase dropouts should be expected. Indeed, Obradovic´(1986) reports that 27% pupils failed to complete the first phase, but it seems that the probability of completing only elementary school did not change with the reform, at least not while analyzing the whole sample. By analyzing the results for the probability of completing high school, we reach the same conclusion—the reform did not significantly change the portion of people with secondary education as the highest educational attainment. This holds also for the distribution of the types of high school (results omitted for brevity).

While the outcome of some university education is unaffected by the reform, the effect on obtaining university education and more is negative and significant. The negative effect

53 is varying from 2.7 and 5.5 percentage points, which corresponds to 25% and 51% of the sample mean. So why did the reform disincentivize pursuing university education? One explanation could be in attaching paraprofessional context to general programs and recognizing this profession on the labor market. In the old system, general high-school programs were perceived as preparation for universities, disregarding employability concerns. In the reformed system, general programs de facto existed but were associated with some profession, allowing them to be a final educational stop, not only a link between elementary and university education. This interpretation is supported by the drop of university enrollment rates—in the academic year 1975/76, 21.37% of age group 20– 24 in the 1971 census was enrolled in the university, while in the academic year 1979/80, 19.25% of age group 20–24 in the 1981 census was attending university. In absolute terms, the number of students in the prereform 1975/76 fell from 78,511 to 69,858 in the postreform 1979/80 (Croatian Bureau of Statistics, 1980, 1993). These numbers support the interpretation that an observed drop in the probability of completing university is not caused by the inability to finish university, but by lower university enrollment rates. The effect of the reform on years of education is negative but insignificant.

These conclusions are reinforced with the results from regressions on years of schooling (tables omitted for brevity). In particular, the probability of having 16 years of education is reduced between 2.5 and 5.2 percentage points, which corresponds to 28% and 58% of the sample mean.

II.4.2 Heterogeneous eﬀects

So far we have established that the reform, when analyzing all individuals, reduced the probability of having university level education. Next, we turn to differences of these effects across gender. In terms of predetermined variables we only have access to two— nationality and gender. Everything else could be affected by the reform so we avoid conditioning on potentially endogenous covariates. Given that in the sample we have

54 Figure 6 — Regression discontinuity graphs for the highest educational attainment

(a) No elementary (b) Elementary Proportion Proportion 0.0 0.2 0.4 0.6 0.00 0.05 0.10 0.15 0.20 -150 -100 -50 0 50 100 150 -150 -100 -50 0 50 100 150 Distance from the reform (in weeks) Distance from the reform (in weeks)

(c) High school (d) Some university Proportion Proportion 0.0 0.2 0.4 0.6 0.8 1.0 0.0 0.1 0.2 0.3 0.4 -150 -100 -50 0 50 100 150 -150 -100 -50 0 50 100 150 Distance from the reform (in weeks) Distance from the reform (in weeks)

(e) University and more (f) Years of education Proportion Years ofschooling 8 9 10 12 14 0.0 0.2 0.4 0.6 -150 -100 -50 0 50 100 150 -150 -100 -50 0 50 100 150 Distance from the reform (in weeks) Distance from the reform (in weeks)

Note: Sample is restricted to individuals born from January 1, 1958 to January 1, 1964. Solid blue line represents the fourth order polynomial estimation of f (ci). Number of bins is chosen using an evenly- spaced mimicking variance method from Calonico et al.(2015). only 8.1% of non-Croatians, we turn to gender-heterogeneous eﬀects.

Table9 presents the results for males. Results indicate that the probability of completing only elementary school significantly increased as most of the specifications turn up with the significant results. This adverse effect is in line with the interpretation of the high rate of first-phase dropouts. Pupils who could have completed vocational school in the old system had to pass gymnasium-like first phase in the reformed one, which resulted in a high rate of first-phase dropouts. This is supported by the fact that the ratio of pupils continuing education after elementary school is fixed before and after the reform at around

55 92% (Croatian Bureau of Statistics, 1978). There is also evidence that male pupils were disincentivized to attend university as the negative effect on the probability of having university education is significant in few specifications. These two effects result in the drop in total years of education for males, and the adverse effect is ranging from 0.303 to 0.496 years.

Empirical evidence in Table 10, where we present the results for females, is in quite a contrast with the overall results and the results for males. The reform did not change the probability of completing elementary, high school or university or more. It did, however, positively aﬀect the probability of having some university education.

What drives these gender heterogeneous effects? Males had problems completing the first phase and did not enroll university to such an extent, while for the females we actually observe an increase in the attendance of some university education. We provide a different selection into high school as a cause of this gender heterogeneity in the reform effects. As it can be seen from Figure4, which displays distribution of education in 2011 for individuals older than 15 years of age (therefore including cohorts born from roughly 1930 to 1996), in the years prior to the reform, the distribution of education was different for males and females. More than a third of females had completed only elementary school—37.2%, while 45.9% and 16.7% had completed secondary and university education, respectively. On the other hand, 23.8% of males had completed only elementary school, while 60.0% and 16.0% had completed secondary and university education (Croatian Bureau of Statistics, 2015).14 In 1971, 13.74% of females aged 15–19 were high-school freshmen, while 15.84% of males aged 15–19 were high-school freshmen (Croatian Bureau of Statistics, 1978, 1993). This clearly indicates unequal access to secondary education across gender prior to the reform. While this is due to a number of socio-economic reasons, it does showcase that self-selection into secondary school was different for females. We argue that informal barriers in access to education, such as gender roles and family planning, actually filtered more-able females into secondary

14The numbers do not sum up to 100% due to unknown educational attainment.

56 education. Asymmetric barriers to secondary education across genders resulted in different ability distributions—while almost all males could enroll high school, females were informally selected so only more relatively able ones continued. This could explain the heterogeneous reform effect—for males we observe an increase of elementary school as the highest attainment as males across the whole ability distribution could continue education, so for a portion of them general-curriculum first phase was problematic. On the other hand, only more-able females could continue education, so not only did they not have problems with the general first phase, it actually motivated them into pursuing further education.

Analyzing the changes in the ﬁeld of education supports this interpretation.15 For males, we observe an increase of probability of completing the general program, which is consis- tent with the increased probability of completing only elementary school since elementary school is coded as general education in the Croatian Labor Force Surveys. For females, we observe a signiﬁcant drop in the probability of completing teacher education and services and an increase in the probability of completing social science programs. Therefore, extended exposure to general curriculum shifted a portion of females from teacher education and services into social sciences.

15Tables are omitted for brevity.

57 Table 9 — Results for the highest educational attainment—males

Finished education No Elementary High Some University Years of elementary school university and more education 3 year window (N=12,080) Linear spline 0.001 0.003 0.020 0.013 −0.038∗∗ −0.175 (0.008) (0.020) (0.028) (0.014) (0.018) (0.139) Quadratic spline 0.009 0.049∗ −0.018 0.012 −0.051∗ −0.440∗∗ (0.011) (0.029) (0.045) (0.021) (0.030) (0.206) Cubic spline 0.0003 0.066∗ −0.028 0.016 −0.055 −0.424 (0.012) (0.039) (0.064) (0.028) (0.041) (0.283) Quartic spline −0.007 0.097∗∗ −0.055 0.025 −0.060 −0.547 (0.016) (0.047) (0.083) (0.035) (0.054) (0.383) 2 year window (N=8,078) Linear spline 0.008 0.017 0.012 0.011 −0.048∗∗ −0.303∗ (0.010) (0.023) (0.036) (0.017) (0.024) (0.169) Quadratic spline 0.003 0.073∗∗ −0.047 0.021 −0.050 −0.461∗ (0.012) (0.036) (0.059) (0.026) (0.037) (0.256) Cubic spline −0.008 0.074 −0.024 0.017 −0.059 −0.459 (0.016) (0.047) (0.080) (0.034) (0.053) (0.375) Quartic spline −0.021 0.043 0.038 −0.012 −0.048 −0.219 (0.020) (0.056) (0.103) (0.041) (0.074) (0.525) 1 year window (N=4,045) Linear spline 0.007 0.069∗∗ −0.047 0.027 −0.056 −0.496∗∗ (0.011) (0.034) (0.054) (0.025) (0.034) (0.233) Quadratic spline −0.014 0.051 0.013 −0.004 −0.046 −0.301 (0.016) (0.049) (0.084) (0.035) (0.058) (0.408) Cubic spline −0.046∗∗ 0.046 0.093 −0.026 −0.066 −0.056 (0.022) (0.055) (0.121) (0.047) (0.084) (0.600) Quartic spline −0.029 0.139∗∗ −0.032 −0.029 −0.048 −0.452 (0.029) (0.054) (0.136) (0.062) (0.103) (0.769) Note: Standard errors clustered at the week of birth are in the brackets. Each cell represents a different regression and presents the coefficient on the variable AFTER which takes value 1 if the individual was born after January 1, 1961, and 0 otherwise. Window width denotes ± years around the cutoff date. Covariates include female and non-Croatian dummy as well as dummies for the survey years. Significance levels: ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

58 Table 10 — Results for the highest educational attainment—females

Finished education No Elementary High Some University Years of elementary school university and more education 3 year window (N=10,294) Linear spline 0.006 −0.001 −0.014 0.025 −0.016 −0.041 (0.010) (0.026) (0.034) (0.017) (0.021) (0.190) Quadratic spline −0.001 −0.032 0.062 0.001 −0.030 0.078 (0.014) (0.034) (0.049) (0.025) (0.030) (0.246) Cubic spline −0.014 −0.058 0.092 0.035 −0.055 0.297 (0.014) (0.043) (0.064) (0.030) (0.042) (0.294) Quartic spline −0.003 −0.055 0.008 0.073∗∗ −0.023 0.432 (0.015) (0.048) (0.076) (0.035) (0.052) (0.364) 2 year window (N=6,987) Linear spline 0.003 −0.023 0.049 0.001 −0.031 −0.037 (0.013) (0.029) (0.040) (0.021) (0.025) (0.216) Quadratic spline −0.012 −0.054 0.063 0.037 −0.033 0.390 (0.014) (0.039) (0.058) (0.028) (0.038) (0.270) Cubic spline −0.004 −0.032 0.034 0.055 −0.052 0.103 (0.014) (0.047) (0.074) (0.035) (0.052) (0.353) Quartic spline 0.023 −0.060 −0.029 0.068∗ −0.003 0.332 (0.022) (0.051) (0.089) (0.037) (0.066) (0.436) 1 year window (N=3,435) Linear spline −0.003 −0.052 0.089 0.014 −0.047 0.150 (0.014) (0.039) (0.057) (0.027) (0.036) (0.266) Quadratic spline −0.002 −0.051 −0.015 0.083∗∗ −0.015 0.440 (0.015) (0.050) (0.079) (0.035) (0.053) (0.370) Cubic spline 0.024 0.025 −0.121 0.084∗∗ −0.012 −0.054 (0.025) (0.054) (0.102) (0.035) (0.078) (0.471) Quartic spline −0.024 −0.060 −0.003 0.133∗∗∗ −0.047 0.499 (0.024) (0.078) (0.133) (0.045) (0.098) (0.596) Note: Standard errors clustered at the week of birth are in the brackets. Each cell represents a different regression and presents the coefficient on the variable AFTER which takes value 1 if the individual was born after January 1, 1961, and 0 otherwise. Window width denotes ± years around the cutoff date. Covariates include female and non-Croatian dummy as well as dummies for the survey years. Significance levels: ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

59 Figure 7 — Distribution of education by gender in 2011 for 15+ individuals

Elementary or less Secondary Tertiary

60%

40%

20%

0% Females Males

II.4.3 Robustness

In this section we provide additional results on the outcomes that were most affected. To explore how robust the results are, we narrow the bandwidth around the cutoff date. In particular, Figure7 presents the results of the estimates using the second-order polynomial as a functional form of f (ci) on a set of bandwidths ranging from 13 to 156 weeks (one quarter to three years). Figure 8a shows that some females were indeed motivated towards some university education. As regarding the field of education, the reform has diverted a portion of females from teacher education and services to social sciences (Figures 8b, 8c and 8d). Figures 8e and 8f display that the conclusions regarding the effect of the reform on the educational outcomes of males—higher incidence of high-school dropouts and consequently more males with general education—is fairly robust.

60 Figure 8 — Educational outcomes

(a) Females: some university (b) Females: teacher education

0.2 0.0

-0.1

0.1 -0.2 Effect Effect -0.3

-0.4 0.0

-0.5

13 26 39 52 65 78 91 104 117 130 143 156 13 26 39 52 65 78 91 104 117 130 143 156 Bandwidth (in weeks) Bandwidth (in weeks)

0.4 0.1

0.3

0.0 0.2 Effect Effect

0.1 -0.1

0.0

13 26 39 52 65 78 91 104 117 130 143 156 13 26 39 52 65 78 91 104 117 130 143 156 Bandwidth (in weeks) Bandwidth (in weeks)

(e) Males: elementary school (f) Males: general education

0.3

0.2 0.2

0.1 0.1 Effect Effect

0.0

-0.1

13 26 39 52 65 78 91 104 117 130 143 156 13 26 39 52 65 78 91 104 117 130 143 156 Bandwidth (in weeks) Bandwidth (in weeks)

Note: Solid black line represents the estimation of the δ coefficient from Equation (1), while the gray area is the 90% confidence interval based on standard errors clustered at the week of birth. Second-order polynomial is used as a functional form for f (ci), while the X-axis presents different bandwidths around the cutoff date.

61 II.4.4 Extended general curriculum and labor market outcomes

In this section we restrict the sample to nongymnasium high-school graduates and analyze the effect of more years of general education on labor market outcomes for both genders. If we include all individuals, our postreform sample will contain individuals which did not experience a curriculum change—individuals who completed only elementary school, gymnasium, or who went to study—which may pull the estimates of reform effects towards zero. By conditioning on completion of nongymnasium high school we are pinpointing a group of individuals which experienced the most drastic curriculum change. However, by doing so we are conditioning on an endogenous covariate. As results in Figure6 suggest, the sample of high-school graduates changed with the reform. Hence, estimates we present in this section are most likely upward biased, as the high- school graduates sample contains individuals who would have completed university in the old system. We therefore interpret these results as the upper bound of the effect of extended general curriculum on the labor market outcomes. Even having this in mind, results presented in Table 11 reveal no labor market premium on more years of general education. Wages, years of work and being nonactive are not affected by the reform, while there is a significant adverse effect on the probability of being employed. This lack of premium on more general education is surprising, given the potential upward bias of the estimates. This absence of a positive effect of general curriculum is in line with other research which relies on quasi-experimental evidence, (Malamud and Pop-Eleches, 2010; Oosterbeek and Webbink, 2007; Hall, 2012, 2013) so we reinforce their interpretation that the observed general vocational wage differential is mainly driven by self-selection into the type of high school. We also run the analysis on the whole sample (not only high- school graduates), as well as separately on females and males (tables omitted for brevity). Results are in line with the ones presented in Table 11, except for the heterogeneity of years of work across the gender on the full sample. Figure9 shows robust evidence that for females the reform reduced total working years, while for the males we actually see an

62 increase total years of work. The direction of the eﬀect as well as the magnitude supports the discussion on the eﬀect of the reform on educational outcomes: females, as they were inclined to obtain some university education, have lees years of work; males, as they were dropping out the high school, reducing the total time spent in school, have more years of work. Table 11 — Labor market outcomes

Labor market outcomes Log hourly wages Years of work Employed Nonactive 3 year window (N=12,677) Linear spline 0.010 0.337 −0.016 0.008 (0.030) (0.234) (0.020) (0.005) Quadratic spline 0.009 −0.230 −0.063∗∗ 0.009 (0.038) (0.346) (0.028) (0.006) Cubic spline −0.008 −0.298 −0.067∗ 0.016∗∗ (0.048) (0.444) (0.037) (0.008) Quartic spline −0.013 −0.089 −0.049 0.010 (0.054) (0.551) (0.044) (0.009) 2 year window (N=8,576) Linear spline 0.009 −0.080 −0.042∗ 0.011∗∗ (0.034) (0.278) (0.023) (0.005) Quadratic spline 0.007 −0.203 −0.063∗ 0.010 (0.045) (0.402) (0.034) (0.007) Cubic spline −0.035 −0.095 −0.059 0.017∗ (0.055) (0.529) (0.043) (0.009) Quartic spline −0.005 −0.552 −0.063 0.012 (0.064) (0.728) (0.049) (0.011) 1 year window (N=4,358) Linear spline −0.014 −0.288 −0.068∗∗ 0.012∗ (0.045) (0.370) (0.032) (0.006) Quadratic spline −0.021 −0.205 −0.044 0.011 (0.055) (0.560) (0.045) (0.009) Cubic spline 0.080 −0.164 −0.081∗ 0.020∗ (0.063) (0.772) (0.049) (0.011) Quartic spline 0.167∗∗ 0.815 −0.095∗ 0.018 (0.071) (0.854) (0.052) (0.015) Note: Standard errors clustered at the week of birth are in the brackets. Each cell represents a different regression and presents the coefficient on the variable AFTER which takes value 1 if the individual was born after January 1, 1960, and 0 otherwise. In all specifications the sample is restricted to nongymnasium high school graduates. Window width denotes ± years around the cutoff date. Covariates include female and non-Croatian dummy as well as dummies for the survey years. Significance levels: ∗p<0.1; ∗∗p<0.05; ∗∗∗p<0.01

63 Figure 9 — Years of work

(a) Females (b) Males

3 0

Effect -2 Effect

-4 0

13 26 39 52 65 78 91 104 117 130 143 156 13 26 39 52 65 78 91 104 117 130 143 156 Bandwidth (in weeks) Bandwidth (in weeks)

II.5.C onclusions

In this paper we identify the causal effect of an educational reform implemented in Croa- tia in 1975/76 and 1977/78 on educational and labor market outcomes. The reform redesigned mostly secondary education as the high school was split into two phases. The first phase, which lasted for two years, was common to all students irrespective of the type of secondary school they enrolled, and contained mostly general curriculum. Upon the completion of the first phase, students could enter the labor market or continue to the second phase, which was designed to provide vocational preparation. Depending on the profession and occupation, the duration of the program was one or two years. General gymnasium-like programs were still available, but they were associated with some vocation or profession. The reform established few important changes—tracking was reduced and the general part of the curriculum was extended as individuals could not enter a vocational school directly after an eight-year compulsory elementary school, instead they needed to attend two additional years of general education.

We ﬁnd that the reform, on average, reduced the probability of obtaining university education. We argue the reason for this lies in the attachment of paraprofessional context to

64 general programs, thus making graduates of once general programs employable after high school. When analyzing the effects across gender, we observe significant heterogeneity. For males we record an increase in the probability of completing only elementary school which is driven by high first-phase dropout rates; we also observe a drop in the probability of having university as the highest educational attainment. For females, we do not observe any adverse effects. In fact, the probability of attending some university significantly increased. We argue that this heterogeneity in the effects of the reform is caused by different selection into high school across genders. While high-school education was available for most of the males, informal barriers in access to education were still present, so more-able females were selected into high-school education. Therefore, exposing this selected sample of female pupils to more general subjects and the opportunity to change profession after two years, shifted a portion of them to some university education, and also shifted a portion of them from teacher and services education to social sciences.

Restricting our sample to nongymnasium high-school graduates, we find that two additional years of general education did not significantly affect individuals’ labor market prospects. This lack of premium on more general education is surprising, given the potential upward bias of the estimates. In particular, as the reform decreased the probability of completing university, the nongymnasium high-school graduates sample contains different ability distributions before and after the reform. These findings are in line with other studies that rely on quasi-experimental evidence on the effects of more general education.

From the policy perspective, this research is relevant as it displays unintended reform effects. One of the most important objectives of the reform was to give broader access to general and academic education. However, it resulted in increased incidence of high- school dropouts for males which is clearly opposed to its proclaimed objectives. Also, it showcases that general high-school curriculum itself is not explaining the long run labor market performance and that the observed general-vocational wage differential is mainly driven by self-selection into the type of high school. Therefore, it perpetuates the debate on not only how to combine academic and specific parts of education, but also how to

65 implement such an optimal mix.

66 III.D o Financial Incentives Alter Physician Prescription Behavior?

Evidence from Random Patient-GP Allocations

(with Alexander Ahammer)

III.1.I ntroduction

Ideally, physicians are perfect agents. They diagnose and provide treatments in a way patients would if they had perfect information. In reality, however, knowledge advantage gives physicians the possibility to maximize own utility at the expense of their patient welfare, especially when faced by economic incentives. Particularly in medical situations where no clinical guidelines and consensus about treatments prevails, and where the marginal harm for the patient is small, these incentives are shown to have the largest impact (Chandra et al., 2012). In this paper we focus on a speciﬁc principal-agent issue; namely whether physicians alter their prescription behavior when faced by monetary incentives. If this is the case and results in physicians overprescribing medication, the eﬃciency of an entire health care system is at stake, with consequences possibly reaching even to the macroeconomic level as shown by Emanuel and Fuchs(2008) for the United States (US).

The type of monetary incentive we analyze is self-dispensing of pharmaceuticals by general practitioners (GPs). Under speciﬁc conditions, GPs in Austria are allowed to dispense drugs in the form of onsite pharmacies, which makes them entrepreneurs and agents at the same time. Many countries around the globe allow onsite drug dispensing, for example the US (in some states), the United Kingdom, Germany, or Switzerland (in some kantons), only to name a few. It is permitted primarily for the purpose of ensuring unhin- dered access to medical drugs in rural areas where regular pharmacies are often diﬃcult to reach.16 Operating an onsite pharmacy, however, allows physicians to earn a mark-up

16Another purpose of onsite pharmacies (especially in Austria) is to attract doctors to practice in rural areas (which may otherwise be unattractive as a working environment) with additional income gained through mark-ups on drugs they prescribe.

67 on every drug they prescribe, which constitutes a clear incentive to induce patient-side demand. Put differently, GPs may exploit their informational advantage to prescribe medication the patient’s health status may not necessarily require, for the sole purpose of maximizing own income. Although this is a very specific setting we analyze, we have no reason to believe that the financial incentive associated with self-dispensing is any different than other financial incentives affecting prescription behavior (see the literature review in section III.2 for specific examples). Thus, implications drawn from our analysis can easily be used to assess the effectiveness of potential implications of other incentive schemes in this context.

There is some causal evidence that doctors in fact do exhibit rent-seeking behavior (e.g., Melichar, 2009 or Clemens and Gottlieb, 2014, see section III.2), hence we hypothesize that having an onsite pharmacy leads, ceteris paribus, to an increase in drug expenses. In order to verify this conjecture, we use administrative data from the Upper Austrian Sick- ness Fund (UASF) which covers around 75% of the population in Upper Austria, one of nine provinces in Austria with roughly 1.4 million inhabitants as of 2016. We have access to a total of 23,820,854 observations representing the universe of GP consultations for these insurees. Contrary to our unconditional descriptive analysis which reveals that self- dispensing GPs induce on average 33.2% higher per patient drug expenses than others, preliminary regressions reveal that doctors who run onsite pharmacies are in fact slightly less likely to prescribe medication in the ﬁrst place, and induce roughly e 2.1 ($2.25 or 5.9%) fewer drug expenses than their non-dispensing colleagues.

This is a surprising result, since the existing literature (Kaiser and Schmid, 2016; Burkhard et al., 2015) in fact finds large positive effects of dispensing on drug prescriptions. Al- though our regressions so far control for physician ability and patient health status in a rigorous ways, and sorting of GPs into pharmacies can be conditioned on GP-level fixed effects, there are two other mechanisms we have to worry about: First, through a series of consultations patients and GPs may develop a principal-agent relationship which allows the patient to bargain over drug prescriptions. In this case, the onsite pharmacy coef-

68 ficient may reflect the patient’s prescription decision rather than the GP’s, which is not what we want to measure. Second, patients may systematically avoid GPs who operate onsite pharmacies. If this type of endogenous sorting drives our results, we expect the pharmacy coefficient to be biased towards zero.

To avoid these issues, we suggest a novel identiﬁcation approach which relies on a sample of randomly allocated patient-GP matches. In particular, we restrict our sample to drugs prescribed on weekends and public holidays. On weekends and public holidays, GPs in Austria rotate to provide out-of-hours services for the purpose of ensuring provision of basic healthcare, which is especially important in rural areas where no hospital is in close proximity. In case a patient decides to consult a physician outside opening hours, assignment can thus be considered random, because it depends only on the community’s rotation schedule.17 Using this strategy to account for endogenous sorting, our estimates become even larger in magnitude and retain their statistical signiﬁcance. We interpret this as a sign of more cautious prescription behavior (Chandra et al., 2012; Lucas et al., 2010): Ceteris paribus, GPs do not seem to prescribe more medication in case the patient is unbeknownst to her.

Overall, we find evidence that GPs who operate onsite pharmacies may not necessarily induce higher drug expenses than others. Although estimates suggest that GPs with onsite pharmacies prescribe slightly more expensive medication (but only if the GP is not acquainted with the patient, i.e., the patient-GP match is random), this effect is absorbed by a much smaller likelihood to prescribe something in the first place, causing the overall effect to be negative. This is not surprising: For our sample of UASF patients, we find that self-dispensing GPs earn on average an additional e 109,882.5 ($118,328.65) in revenues per year, for doing the same work as non-dispensing GPs. Thus, the financial incentive

17To our knowledge, there is only one paper using a similar approach: Ahammer(2016) estimates labor market effects of supply-induced sick leaves. As a robustness check, he restricts his sample to sick leaves starting on weekends and public holidays as well. Since he does not observe the actual date of certification, however, Ahammer(2016) has to assume that it coincides with the start of the sick leave. In case they are systematically different, the allocation mechanism cannot be considered random anymore. In this paper, we decided to focus solely on drug prescriptions, since for those we know the exact date of consultation.

69 to overprescribe may not be as strong as initially thought, and dispensing GPs may even prescribe more cautiously due to the additional income.18

III.2.R elated literature and our contributions

Our paper generally belongs to the broad literature on practice styles and supply-induced demand (see, e.g., McGuire and Pauly, 1991 and Chandra et al., 2012 for overviews). In particular, we contribute to the literature on the role of financial incentives in medical care. A recent example providing causal evidence in this context is Clemens and Gottlieb (2014), who use price shocks triggered by regional Medicare consolidations in 1997 to estimate care elasticities with respect to reimbursement rates. They find that healthcare supplied to Medicare patients increases overproportionally with the reimbursement rate. Another notable example is Melichar(2009), who exploit within-physician variation in reimbursement schemes involving different financial incentives for marginal increases in the provision of healthcare. They find that GPs spend less time with patients they receive no marginal revenues for, as compared to patients whose expenses are reimbursed on a fee for service basis.

Similar studies analyze incentive effects of a fundholding scheme effective during the nineties in Britain, which incentivized primary care physicians to exert their gatekeeping role more efficiently by giving them a budget for secondary care procedures and allowing them to retain a potential surplus. Empirical results indicate that physicians responded by decreasing inpatient admissions when they entered the scheme (allowing them to retain a higher share of the budget), and increased admissions upon abolishment in 1999 (Croxson et al., 2001; Dusheiko et al., 2006). There is also experimental evidence from the field: Kouides et al.(1998) for example document that physicians randomly selected to receive a monetary benefit for increasing their influenza immunization rate eventually achieved a 6.9 percentage points higher rate than physicians in the control group.

18Note that, aside from initial cost of building storage space, operating cost for onsite pharmacies are likely very low, because GPs do not need additional personnel to maintain the pharmacy.

70 Related is also the literature on the role of onsite pharmacies in the choice of generic versus brand-name drugs in day to day medical care. In systems where physicians are allowed to prescribe and dispense drugs at the same time, Liu et al.(2009), Iizuka(2007, 2016), and Rischatsch et al.(2013) find that profit incentives significantly a ffect physician prescription behavior. Analyzing the interrelations between inpatient and outpatient prescription behavior, Pruckner and Schober(2016) find that GPs are less likely to adhere to the hospital’s treatment choice if they dispense drugs themselves.

There is much less literature on the actual effect of physician self-dispensing on drug expenses. To our knowledge, there are currently only two studies which specifically consider that question: Kaiser and Schmid(2016) exploit geographical variation in dispensing regulations across Switzerland. They empirically match physicians from cantons where it is permitted to operate onsite pharmacies to physicians from cantons where it is prohibited. Using doubly robust estimation, Kaiser and Schmid(2016) find that physician dispensing increases medical drug expenditures by roughly 34% per patient. Burkhard et al.(2015) replicate their analysis but decompose the estimated increase in expenditures into a price and a volume effect. They show that the volume effect is dominant, while the price effect is small and insignificantly different from zero. However, both papers implicitly assume that GPs sort exogenously into cantons where self-dispensing is permitted, and that patients are matched randomly to GPs, conditional on their explanatory variables. Although they use a very rich set of control variables, sorting based on unobservables cannot be fully ruled out.

We contribute to the literature in several important ways. First, we specifically take into account sorting of GPs into onsite pharmacies and endogenous matching between patients and GPs, the latter by employing a novel identification strategy allowing to draw a sample of randomly matched patient-GP pairs. Second, we introduce fixed effects estimation along with a rich set of covariates including a physician ability proxy based on adjusted mortality rates to the literature. Third, since we do not aggregate our data on the physician level, we can analyze the onsite pharmacy effect both on the extensive and on the intensive

71 margin. Fourth, we are the ﬁrst to analyze eﬀect heterogeneities based on age, education, gender, and wages.

III.3.I nstitutional setting

Austria has a Bismarckian welfare system where virtually all residents have universal access to healthcare. Mandatory health insurance covers all medical expenses both in the inpatient and outpatient sector including prescription medicines.19 The Federation of Austrian Social Security Institutions, an umbrella organization encompassing all 22 individual health insurance funds,20 maintains a positive list of permitted pharmaceuticals, the so-called Reimbursement Codex. In 2010, the codex contained 4,200 diﬀerent medications which patients have access to upon prescription by a physician and payment of a small prescription fee in the dispensing pharmacy.21

With 5 doctors per 1,000 inhabitants in 2013, Austria has the highest physician density among all OECD countries (OECD, 2015). Outpatient care is mainly provided by around 19,000 independently practicing physicians of whom 56% are contracted with one or several health insurance funds. These contracted physicians (both GPs and specialists) can be accessed free of charge and without a referral, non-contracted physicians on the other hand charge a fee which will partly be reimbursed by the patient’s insurance. Patients are not obliged to consult their GP before seeking specialist or inpatient treatment, thus general practitioners formally do not serve a gatekeeping function in Austria. Although it is still common to have a family doctor, patients may also switch GPs on a regular basis.

19According to Hofmarcher(2013), Austrian health policy follows the principle of ensuring equal access to health care for all, irrespective of demographic and socioeconomic preconditions. She states that, de facto, the health system comes very close to achieving this goal. Almost 99.9% of the population in 2011 was covered by health insurance, the quality of care is generally considered to be high, and most treatments and services are universally accessible. However, this comes at the expense of very high cost. Both in absolute terms and in percent of GDP, Austria ranks well above the EU-15 average in terms of health care expenditures (OECD, 2015). 20Note that aﬃliation to one of these 22 health insurance funds may not be choosen freely but depends on occupation and place of residence of the patient. Thus there is no endogenous sorting into and no competition among health insurances. 21In 2012, the prescription fee was e 5.15 or $5.51 (Hofmarcher, 2013). Pharmacies are reimbursed by the patient’s health insurance for the prescribed drug’s cost, which the fee is oﬀset against.

72 For general practitioners, it is typically preferable to secure a contract with at least one health insurance fund, as it guarantees a constant inﬂux of patients and has several bu- reaucratic advantages (ÖKZ, 2007). Contracted positions, however, are limited. Both the geographical distribution as well the absolute number of contracted physicians is regu- lated by the Federation of Austrian Social Security Institutions. Medical professionals that strive for a GP position thus have to pass through an application procedure where candidates are selected based on professional aptitude. Only contracted physicians are allowed to maintain onsite pharmacies.

III.3.1 Country doctors and onsite pharmacies

In a country where almost half of the population lives in predominantly rural regions (Eurostat, 2013), an important pillar of outpatient medical care are country doctors (in German called “Landarzte”). Oﬃcially, country doctor are contracted physicians who either practices in a community with up to 3,000 inhabitants, or is one of at most two contracted physicians in a single community (Austrian Medical Chamber, 2013). According to the medical chamber, roughly 40 percent of general practitioners in Austria fall within this category. In 2013, this amounts to 1,563 doctors being responsible for over 43% of the population.

More than half of these doctors, however, are expected to retire within the next ten years. This poses an important challenge for oﬃcials and policy makers, who have long been lamenting about the lack of young doctors applying for vacant insurance contracts in rural areas (Austrian Medical Chamber, 2013). Often living and working conditions dis- courage physicians to settle in these areas, the average number of applicants per country doctor vacancy in Upper Austria decreased from 5 in 2001 to 1.2 in 2012. Amongst other measures, onsite pharmacies are increasingly instrumentalized by policy makers to attract physicians and counteract the expected shortage of doctors in rural areas (Austrian Medical Chamber, 2013).

73 Onsite pharmacies require physicians to act as entrepreneurs. Typically they purchase a selection of common medications from pharmaceutical wholesalers which they dispense directly to the patient upon issuing a prescription. Since prices are ﬁxed through the insurance’s reimbursement rate, onsite pharmacies cannot compete on prices with regular pharmacies. A country doctor is permitted to operate an onsite pharmacy if (1) she is contracted with at least one health insurance fund, (2) there is no regular pharmacy in her community, and (3) the next regular pharmacy is more than six kilometers away. In 2016, the government passed a law which allows GPs to keep their onsite pharmacy even when a regular pharmacy opens within their community, as long as the pharmacy is more than four kilometers away. In case a pharmacy opens within a radius of four kilometers around the physician’s practice, operating an onsite pharmacy is no longer permitted.

III.3.2 Weekend prescriptions

General practitioners in Upper Austria typically work Monday to Friday. On weekends and public holidays, each community has a rotation schedule of GPs providing out-of- hours services in order to ensure the provision of basic health care. This institution is especially important in rural areas, where the nearest hospital is diﬃcult to reach. In some communities, the rotation schedule is posted on a website or in local newspapers, in others, patients have to call the emergency ambulance (typically the Red Cross) where the dispatcher informs them about the GP on duty. In case a patient decides to consult a GP on a weekend or public holiday, assignment is therefore random since it depends solely on the community’s rotation schedule.

As discussed in section III.5, our main estimations are based on a sample restricted to prescriptions issued on weekends or public holidays. Indeed, this sample may be selected in case (1) patients postpone their consultation until after the weekend because their medical condition does not require urgent treatment, or (2) they choose to go to a hospital instead. As long as patients do not base their decision on whether the GP on duty has an onsite

74 pharmacy, neither of these selection mechanisms biases our results.

III.4.D ata

The main source of data for our empirical analysis is the Upper Austrian Sickness Fund (UASF), which gathers detailed information on health care utilization in both the inpatient and outpatient sector for roughly one million insurees. As described in section III.3, these insurees correspond to about three quarters of the Upper Austrian population, composed of private as well as public sector workers, retirees, and unemployed people. We augment the data with information on patient education and wages from the Austrian Social Secu- rity Database (Zweimüller et al., 2009) as well as additional demographic information on physicians from the Upper Austrian Medical Chamber.

For our analysis we draw a sample comprising the universe of medical drug prescriptions issued by general practitioners between 2008 and 2012.22 In total, we observe over 16 million prescriptions issued by 632 GPs to over 1.1 million patients — on average, this amounts to roughly 14 prescriptions per patient over the entire period. Additionally, we add all consultations that did not result in drug prescriptions to our data, which allows us to analyze the eﬀect of ﬁnancial incentives at the extensive margin, i.e., the overall probability of receiving medication when a GP is consulted. Our primary criterion for including a prescription is whether it is issued by a general practitioner, for self-dispensing GPs we also include drugs that are dispensed at a regular pharmacy (i.e., not sold at the onsite pharmacy).23 In total, this leaves us with a sample of more than 23.8 million consultations.

Our main regressions are based on a subset of these data, namely drug prescriptions issued

22Unfortunately, our data does not allow us to analyze outcomes other than medical drug prescriptions, since we do not have an exact date of consultation (which we need to deﬁne our weekend sample) for non-drug health services. Kaiser and Schmid(2016) ﬁnd that drug and non-drug expenditures are comple- mentary goods for self-dispensing physicians. 23This could, for example, be the case for certain uncommon medications (such as cancer drugs) the GP may not have in stock at his onsite pharmacy. In general, we expect onsite pharmacies to have a smaller variety of medications than regular pharmacies, which is also a result in Pruckner and Schober(2016).

75 Table 12 — Descriptive statistics.

Full sample Weekend samplea Changersc Diﬀ.b Mean Std. dev. Mean Std. dev. Mean Std. dev. Outcomes Positive drug expenses 0.686 0.464 0.541 0.498 0.145 0.688 0.463 Total drug expenses (in EUR) 35.642 147.779 24.191 156.145 11.451 35.963 201.439 Units of medication 2.010 3.899 1.362 3.046 0.648 1.967 3.804 GP characteristics On-site pharmacy 0.299 0.458 0.347 0.476 −0.048 0.746 0.435 Female 0.122 0.327 0.111 0.314 0.011 0.539 0.498 Age Under 35 0.002 0.039 0.001 0.035 0.0003 0 0 35 to 40 0.010 0.102 0.009 0.094 0.001 0.079 0.270 40 to 45 0.041 0.197 0.032 0.176 0.009 0.243 0.429 45 to 50 0.107 0.309 0.088 0.283 0.019 0.311 0.463 50 to 55 0.256 0.436 0.233 0.423 0.023 0.212 0.409 55 to 60 0.342 0.474 0.360 0.480 −0.018 0.138 0.345 60 to 65 0.201 0.401 0.227 0.419 −0.026 0.017 0.128 Over 65 0.042 0.200 0.051 0.219 −0.009 0 0 Adjusted mortalityd 1.000 0.003 1.000 0.003 0.0001 1.000 0.003 Patient characteristics Female 0.564 0.496 0.536 0.499 0.029 0.571 0.495 Age Under 20 0.098 0.297 0.141 0.348 −0.043 0.119 0.324 20 to 30 0.076 0.265 0.099 0.299 −0.024 0.076 0.265 30 to 40 0.087 0.281 0.109 0.312 −0.023 0.088 0.284 40 to 50 0.130 0.336 0.155 0.362 −0.026 0.127 0.333 50 to 60 0.159 0.366 0.167 0.373 −0.008 0.155 0.362 60 to 70 0.183 0.387 0.144 0.351 0.039 0.177 0.382 70 to 80 0.162 0.368 0.116 0.320 0.046 0.167 0.373 Over 80 0.106 0.308 0.069 0.253 0.038 0.091 0.287 Education Compulsory 0.063 0.243 0.073 0.260 −0.010 0.061 0.240 Apprenticeship 0.156 0.363 0.198 0.399 −0.042 0.162 0.368 High school 0.117 0.322 0.152 0.359 −0.034 0.118 0.323 University 0.034 0.182 0.040 0.196 −0.006 0.030 0.170 Missing 0.629 0.483 0.537 0.499 0.092 0.629 0.483 Daily wage (in EUR) 27.872 43.745 36.373 46.925 −8.501 27.393 42.628 Migrant 0.166 0.372 0.160 0.366 0.006 0.168 0.374 Medication historye 159.829 494.278 122.481 448.909 37.349 154.987 457.232 Hospital history f 0.599 3.812 0.463 3.303 0.136 0.562 3.599 ATC medication code Missing 0.033 0.178 0.039 0.194 −0.006 0.025 0.155 Alimentary tract and metabolism 0.108 0.310 0.079 0.270 0.029 0.115 0.319 Blood and blood forming organs 0.015 0.122 0.010 0.101 0.005 0.016 0.125 Cardiovascular system 0.199 0.399 0.136 0.342 0.063 0.206 0.405 Dermatologicals 0.015 0.120 0.012 0.111 0.002 0.014 0.116 Genito-urinary system 0.016 0.124 0.010 0.102 0.005 0.017 0.129 Systemic hormonal preparations 0.018 0.131 0.014 0.119 0.003 0.018 0.132 Antiinfectives for systemic use 0.059 0.236 0.067 0.250 −0.008 0.066 0.249 Antineoplastic and imm. agents 0.006 0.078 0.005 0.069 0.001 0.007 0.083 Musculo-skeletal system 0.065 0.247 0.051 0.220 0.014 0.066 0.248 Nervous system 0.102 0.302 0.073 0.261 0.028 0.088 0.283 Antiparasitic products 0.0004 0.020 0.0003 0.018 0.0001 0.0004 0.021 Respiratory system 0.044 0.205 0.038 0.190 0.006 0.041 0.198 Sensory organs 0.006 0.079 0.005 0.070 0.001 0.008 0.089 Various 0.001 0.028 0.001 0.026 0.0001 0.001 0.035 Sample size 23,820,854 2,089,438 — 484,415 Notes: This table presents summary statistics for our sample of consultations. a Sample is restricted to medications prescribed on weekends or public holidays. b Diﬀerence in means between the full sample and the weekend sample. c Sample of patients who receive medication from GPs that change their onsite pharmacy status at least once between 2008 and 2012. d See section III.5.2 for details on the calculation of this variable. e Medication history is the aggregate amount of drug expenses one year prior to the consultation. f Hospital history is the aggregate number of days spent in hospital one year prior to the consultation.

76 on weekends or public holidays (for convenience we may call this the ‘weekend sample’ henceforth). For reasons discussed in section III.5.2, we are primarily interested in weekend and holiday prescriptions because they provide more reliable estimates than the full sample. Thus, we do not include drug prescriptions by specialists, since they typically do not provide out-of-hours services on weekends.

Summary statistics are provided in Table 12, where we provide first and second moments of our most important variables for the full sample, the weekend subsample, and a sample of ‘changers’. The latter is simply a subset of the full sample comprising the largest connected set of consultations held by GPs who open or close an onsite pharmacy at least once during our observation period. Because we include GP fixed effects in our estimations, these are in fact the observations which ultimately identify our results. Note that the means of the changer sample are remarkably similar to those obtained from the full sample, thus fixed effects estimates should be representative as well. We mean impute missing wage observations.

Our four outcome variables are discussed extensively in section III.5. At the extensive margin, we estimate the eﬀect of onsite pharmacies on a binary variable indicating whether at least one unit of medication is prescribed during the consultation (i.e., drug expenses are positive), and overall drug expenses of the consultation, including also zeros for consultations where no drug was prescribed. At the intensive margin, we look at drug expenses per unit and at the number of units prescribed, both conditional on receiving at least one unit of medication. On weekends and public holidays, in general it seems that slightly less medication is prescribed.

Our treatment indicator is a binary variable indicating whether the consulted GP operates an onsite pharmacy, and zero otherwise. Around 30% of all GPs operate an onsite pharmacy, this corresponds roughly to the oﬃcial numbers cited in section III.3.1. In the weekend sample, the fraction of GPs with onsite pharmacies is higher, which makes sense given that weekend consultations are used more by people living in rural areas, where also

77 onsite pharmacies are much more common than in densely populated areas. For the GP, we also have information on gender and age: It seems that GPs in Upper Austria are predominantly men aged 50 or older. Again, these numbers coincide with the oﬃcial ﬁgures presented in section III.3.1.

At the patient level, we control for age, wages (which we set to zero for non-working patients), and health proxies — these are time-varying variables, and their means reflect mostly what we expect a priori. Additionally, we have information on gender, education, and migratory status. Overall, patients are more likely to be male, around 50% are between 50 and 80 years of age, and their highest educational degree is most likely apprenticeship training. Our health proxies are the sum of drug expenses in the year prior to the consultation (‘medication history’) and the aggregate number of days spent in hospital the year prior to the consultation (‘hospital history’). On top of that, we include a full set of region-specific controls in our estimations.24 These are especially important because we want to pick up as much location-specific heterogeneity as possible.

Finally, we use the Anatomical Therapeutic Chemical (ATC) classification system to control for the type of medication prescribed. Unfortunately, we do not have information on diagnoses, thus the ATC code serves as a proxy for the medical condition the patient suffers from. Around 40% of all drugs prescribed fall within one of the following cate- gories: ‘Alimentary tract and metabolism’ (e.g., laxatives, antidiarrhoeals, antidiabetics, vitamins, or dietary minerals), ‘cardiovascular system’ (e.g., beta blockers, cardiac stim- ulants, or antiarrhythmics), or ‘nervous system’ (e.g., analgesics, antidepressants, anti- ADHD agents, etc.) with cardiac therapy drugs being the most common one. Missing values on education and the ATC code are flagged and included in our regressions in order to maintain a reasonable sample size.

24We build geographical clusters based on the ﬁrst three out of four ﬁgures of the patient’s zip code — these correspond roughly to larger communities.

78 III.5.M ethodology

We estimate the following ﬁxed eﬀects model:

0 0 0 0 yijt = ϑ · 1{ospijt} + Xijtβ + Witγ + Z jtδ + Miϕ + η j + τt + εijt (5)

where yijt are pharmaceuticals received by individual i = 1,..., N prescribed by GP j = 1,..., J at time t = 1,..., Ti, thus subscript ijt uniquely identiﬁes a consultation.

The treatment indicator 1{ospijt} ∈ {0, 1} equals unity if GP j providing medical care to individual i maintains an onsite pharmacy at time t, and zero otherwise — our main coeﬃcient of interest is therefore ϑ.

Additionally, the vector Xijt contains consultation-specific control variables such as the first letter of the prescribed drug’s Anatomical Therapeutic Chemical (ATC) classification system code, the vector Wit comprises time-variant patient-level controls such as age, wage, and a full set of community fixed effects, Z jt captures time-variant GP-level control variables such as age and a measure of physician ability (adjusted GP-specific mortality rates, see section III.5.2 for a detailed description), and Mi contains patient-level time- invariant control variables (e.g., gender, migratory status, and education). Finally, we include a full set of GP-level fixed effects η j as well as year and month fixed effects τt.

III.5.1 Outcome variables

25 Let expijt be the sum of prices of all drugs prescribed in consultation ijt in EUR, and let

26 volijt be the number of units of drugs prescribed. Then, our vector of outcome variables yijt consists of

(1) “positive drug expenses” 1{expijt > 0} ∈ {0, 1}, an indicator variable which equals unity when patient i receives some medication from GP j during the consultation at

25The EUR/USD exchange rate is 1.09 as of Thursday 7th September, 2017. 26A unit of medication is typically a package (containing tablets or capsules), but may also be a bottle (e.g., for cough syrup) or other types of pharmaceuticals.

79 time t, and zero if the patient does not receive any medication,

(2) “total drug expenses” log(1 + expijt), a continuous measure for the sum of the expenses of all drugs prescribed during consultation ijt,

(3) “drug expenses per unit” log[1 + (expijt/volijt)] is a continuous measure of drug

expenses per unit prescribed during consultation ijt, conditional on 1{expijt > 0} = 1, and

(4) “medication volume” volijt is a discrete measure of the number of units prescribed

during consultation ijt, conditional on 1{expijt > 0} = 1, where (1) can be interpreted as the extensive margin (i.e., the probability of receiving a drug in the ﬁrst place), whereas (3) and (4) can be interpreted as the intensive margin (i.e., the price and volume eﬀect conditional on receiving medication). Outcome (2) is also located at the extensive margin since it includes zeros as well (when no medication is prescribed).

Since most of our outcome variables are non-binary, we decide to model yijt as a linear additive function of the treatment indicator 1{ospijt} and the set of control variables

(Xijt, Wit, Z jt, Mi, η j, τt). The coefficient of interest ϑ can then be interpreted as the difference in outcomes between self-dispensing and non-self-dispensing GPs. Because we include GP fixed effects η j, we require ospijt to be time-variant for ϑ to be estimable. Thus, identification comes from GPs that open or close their onsite pharmacies during the observation period. As discussed in section III.3, the latter may for example be possible whenever a GP is not allowed to dispense drugs anymore because a regular pharmacy opens within a distance of four kilometers from her practice. In Table 12, we provide summary statistics for consultations of GPs changing their dispensing status; it turns out that their averages are remarkably close to those found for the full sample.

80 III.5.2 Identiﬁcation

In order to discuss identiﬁcation of our main parameter ϑ, we use the potential outcomes framework (Rubin, 1974). Consider again the model in equation (5). To simplify notation, deﬁne dk ≡ dk(ijt) ≡ 1{ospijt}, with k(ijt) denoting consultation k of GP j to patient i at time t. Let y1k be the potential outcome if physician j owns an onsite pharmacy at time t

(i.e., if dk = 1), and let y0k the potential outcome if the physician does not dispense drugs herself (dk = 0). Furthermore, let Vk denote the set of control variables in model (5),

Vk = (Xijt, Wit, Z jt, Mi, η j, τt). Then, the conditional average treatment eﬀect (ATE) we are ultimately interested in can be written as

ϑ = E[y1k − y0k | Vk]. (6)

For ϑ in (6) to be identiﬁed, we require the treatment status dk to be as good as randomly assigned, conditional on our set of covariates Vk. Formally, = {y1k, y0k} | dk | Vk, (7) = where | denotes statistical independence. If the conditional independence assumption in (7) holds, the diﬀerence in conditional average outcomes has a causal interpretation. That is,

E[y1k − y0k | Vk] = E[yk | Vk, dk = 1] − E[yk | Vk, dk = 0]. (8)

Due to the extensive array of control variables, we are confident that most systematic differences in patients and GPs which may be correlated with dk are accounted for in our regressions. However, there are two main threats to identification which we will discuss in more detail here, both related to self-selection. First, GPs may self-select into onsite pharmacies. Our main remedy to deal with that issue is to include GP fixed effects in model (5), arguing that the unobserved propensity to self-select into dispensing is likely

81 a time-invariant personality trait, or at least a characteristic that does not change over time. Additionally, we follow Biørn and Godager(2010) and Markussen et al.(2012) and construct adjusted mortality rates as a proxy for physician ability, which is likely also a determinant of self-selection into dispensing and potentially time-variant (e.g., through further education). We proceed as follows: First, deﬁne a GP j for every patient i in the

UASF data, and build a yearly panel for i = 1,..., N and t = 1,..., Ti. Second, perform the following regression:

0 Pr[1{deadit} = 1] = π1 · ageit + π2 · 1{ f emalei} + Citψ + ξit (9)

where 1{deadit} ∈ {0, 1} is a binary variable indicating whether patient i died in year t and

Cit is a vector of community dummies. Third, average the predicted values obtained from estimating model (9) via OLS over all patients of GP j: Let Pj be the set of patients of

GP j, and let Pj be the cardinality of Pj, then

XPj XT 1 [ Λ j = Pr[1{deadit}] (10) PjT i=1 | i∈Pj t=1

is the adjusted mortality rate for GP j. In order to ease interpretation, we centered Λ j around one, so estimates can be interpreted as percentage diﬀerences in adjusted mortality from the average GP.

Controlling for physician ability along with age and GP-level fixed effects, we believe that most unobserved factors determining endogenous sorting of GPs into self-dispensing are accounted for in our model. A different sorting mechanism, however, may also im- pede identification, namely endogenous matching of patients to certain GPs. Again, we suppose that most factors driving these sorting decisions are already controlled for in our regressions (most importantly physician ability) — however, our results may still be biased in case there are unobserved determinants we do not catch. Therefore, we restrict our sample to consultations on weekends and public holidays.

82 On weekends and public holidays, GP practices in Upper Austria are typically closed. As discussed in section III.3.2, however, each community has a schedule of GPs rotating to provide out-of-hours services in order to ensure medical care in emergency cases. Since patients do not know which GP is on duty in case they get sick on a weekend, the allocation between patient and GP is as good as random. In section III.3.2, we briefly discussed two cases where this sample may still be selected on unobservables: (1) if the patient postpones her visit until after the weekend, and (2) if the patient decides to go to a hospital instead. As long as the patient does not base her decision on whether the GP on duty operates an onsite pharmacy, these cases will not affect identification in our framework.27 Since the patient does not have any information about the GP on duty (which we ensure by keeping only the first patient-GP match in case there are multiple matches), we believe that this is a plausible assumption.

Another appealing feature of using only weekend prescriptions is that it eliminates certain principal-agent dynamics which may have evolved between patient and GP. Through a series of consultations, patients may develop a relationship with their GPs which allows them to bargain over drug prescriptions. Because we only use random patient-GP matches, such dynamics do not distort identification either. In section III.6, we report results both for the full sample as well as for the weekend sample since comparing these estimates may provide insight about effects of patient and GP side self-selection on drug prescriptions. Generally, we expect estimated onsite pharmacy effects to be biased upward in case there is endogenous sorting of GPs into onsite pharmacies, and to be downwards biased in case patients systematically avoid GPs with onsite pharmacies.

83 Table 13 — Average per patient per year drug expenses for GPs with and without onsite pharmacies.

On-site pharmacy No Yes Difference (1) (2) (3) Non-adjusted drug expenses (in EUR) 50.75 67.62 33.2% Adjusted drug expenses (in EUR) 16.57 18.65 12.6% Note: This table gives the difference in average per patient per year drug expenses of GPs who do not maintain an onsite pharmacy (“No”) and those who do (“Yes”). The adjusted difference is based on residuals from regressing drug expenses on a third-order polynomial in age and a female dummy.

III.6.R esults

In Table 13 we present average yearly per patient drug expenses, both for GPs operating an onsite pharmacy and for those who do not dispense drugs themselves. For non- dispensing GPs, non-adjusted drug expenses are based on prescriptions issued by the GP and dispensed at a regular pharmacy. For self-dispensing GPs, in contrast, we consider only prescriptions that are dispensed directly at the onsite pharmacy, disregarding drugs which are dispensed at a regular pharmacy.28

Average drug expenses of self-dispensing GPs are e 16.87 ($18.17) or 33.2% higher than the drug expenses induced by other GPs. Since we only consider drugs dispensed and billed directly by the GP, e 67.62 ($72.82) can be interpreted as the average yearly revenue generated through the onsite pharmacy. Self-dispensing GPs have on average 1,625 patients, their total average revenue per year is thus e 109,882.5 ($118,328.63),29 which they earn on top of reimbursements paid by the health insurance for other medical services. The main purpose of this paper is to verify how much of this diﬀerence can be

27Note that, even if the patient considers dispensing status of the matched GP in her decision whether to consult the GP or postpone her visit or go to a hospital, our estimates would be lower bounds of the actual effect. 28As discussed in section III.4, our data also comprises drugs prescribed by self-dispensing GP but dispensed by a regular pharmacy instead of the GP herself. The reason is that we are interested in how financial incentives affect prescription behavior overall, irrespective of whether the GP in fact sells the drug herself in the end or issues a prescription for a regular pharmacy. 29Note that this back-of-the-envelope calculation requires average revenue per year and the average number of patients per doctor to be orthogonal.

84 Table 14 — Estimations results for full sample.

Extensive margin Intensive margin Positive Total Expenses Medication expenses expenses per unit volume (1) (2) (3) (4) On-site pharmacy −0.022∗∗∗ −0.059∗∗ 0.011 0.014 (0.008) (0.028) (0.009) (0.021) Patient is female 0.013∗∗∗ −0.020∗∗∗ −0.070∗∗∗ 0.014 (0.001) (0.004) (0.002) (0.010) Patient drug historya 0.0001∗∗∗ 0.001∗∗∗ 0.0002∗∗∗ 0.001∗∗∗ (0.00001) (0.0001) (0.00002) (0.0001) Patient hospital historyb 0.002∗∗∗ 0.019∗∗∗ 0.004∗∗∗ 0.061∗∗∗ (0.0001) (0.001) (0.0003) (0.002) Patient wage −0.017∗∗∗ −0.054∗∗∗ 0.016∗∗∗ −0.055∗∗∗ (0.001) (0.003) (0.001) (0.005) Patient is migrant 0.023∗∗∗ 0.025∗∗∗ −0.057∗∗∗ 0.009 (0.002) (0.006) (0.004) (0.011) GP adjusted mortality 0.206∗ 0.665∗ −0.141 2.332∗∗ (0.114) (0.383) (0.154) (1.115) GP fixed effects Yes Yes Yes Yes Year and month Yes Yes Yes Yes ATC codes — — Yes Yes Patient education and age Yes Yes Yes Yes GP age Yes Yes Yes Yes Community fixed effects Yes Yes Yes Yes Observations 23,820,854 23,820,854 16,341,428 16,341,428 Adjusted R2 0.188 0.236 0.176 0.072 Notes: In this table we present results from estimating equation (5) on the full sample of general practitioner consultations. Every column represents an individual regression estimated by OLS: In column (1), the outcome is 1{expijt > 0}; in column (2), the outcome is log(1 + expijt); in column (3), the outcome is log[1 + (expijt/volijt)]; and in column (4), the outcome is volijt. Heteroskedasticity-robust and community- level clustered standard errors are given in parentheses below coefficients, stars indicate significance levels: * p < 0.1, ** p < 0.05, *** p < 0.01. a Medication history is the aggregate amount of drug expenses one year prior to the consultation. b Hospital history is the aggregate number of days spent in hospital one year prior to the consultation. ascribed to the possibility of self-dispensing, and how much is caused by other factors such as patient health or endogenous sorting.

In Table 14, we take a closer look at the determinants of individual drug prescriptions. Before we turn to our main analysis based on a sample of randomly allocated patient-GP matches, we run our estimations on the universe of drug prescriptions in order to gain a more comprehensive picture. For a detailed discussion of our four outcome variables we refer the reader to section III.5.1 — in general, columns (1) and (2) should capture

85 eﬀects at the extensive margin (i.e., the overall probability of receiving medication), while columns (3) and (4) consider the intensive margin (i.e., given that the patient receives medication, what determines their expenses and volume). Inference is based on analytical heteroskedasticity-robust and community-level clustered standard errors.

In column (1) we consider the overall probability of receiving medication as an outcome. In contrast to our descriptive analysis, we find that consulting a GP who has an onsite pharmacy in fact decreases the likelihood of receiving medication by 2.2 percentage points, which corresponds to 3.3% of the sample mean. In column (2), we find a similar effect: overall expenses decrease by 5.9% — in terms of the sample mean, this corresponds to a reduction from e 35.64 ($38.38) to e 33.54 ($36.12). Thus, we find rather small yet statistically significant effects at the extensive margin.

Columns (3) and (4) are only observed conditional on receiving at least one unit of medication. For both expenses per unit and the number of units we find small positive yet statistically insignificant effects. Thus, it seems that GPs with onsite pharmacies are slightly less likely to prescribe medication in the first place which leads also to a small decrease in overall expenses. Once medication is prescribed, we do not find any statistically significant differences between self-dispensing and non-self-dispensing GPs.

A priori, we would expect the onsite pharmacy effect to be positive. Similar to results from the available empirical literature, also our descriptive analysis clearly points towards substantial excess prescription of dispensing GPs, which indicates that physicians indeed respond to financial incentives. How can we rationalize this small negative effect? We do not necessarily neglect the possibility that GPs are profit-maximizing individuals, yet we conjecture that GPs may not necessarily face a strong enough incentive to overprescribe, because potential benefits do not exceed cost associated with the risk of harming the patient. Keep in mind that onsite pharmacies yield an average of e 109,882.5 ($118,328.63) in revenues for the same work other GPs earn nothing for. Thus, the additional income generated through onsite pharmacies may allow the GP to prescribe more cautiously. Fur-

86 Table 15 — Estimation results for sample of weekend and holiday prescriptions, extensive margin.

Positive expenses Total expenses (1) (2) (3) (4) (5) (6) On-site pharmacy −0.128∗∗∗ −0.125∗∗∗ −0.123∗∗∗ −0.419∗∗ −0.391∗∗ −0.389∗∗ (0.049) (0.046) (0.045) (0.192) (0.175) (0.175) Patient is female 0.023∗∗∗ 0.022∗∗∗ 0.010∗∗ 0.009∗ (0.001) (0.001) (0.005) (0.005) Patient drug historya 0.0001∗∗∗ 0.0001∗∗∗ 0.001∗∗∗ 0.001∗∗∗ (0.00001) (0.00001) (0.0001) (0.0001) Patient hospital historya 0.002∗∗∗ 0.002∗∗∗ 0.016∗∗∗ 0.016∗∗∗ (0.0002) (0.0002) (0.001) (0.001) Patient wage −0.020∗∗∗ −0.020∗∗∗ −0.050∗∗∗ −0.050∗∗∗ (0.001) (0.001) (0.003) (0.003) Patient is migrant 0.007∗∗ 0.007∗∗ −0.004 −0.004 (0.003) (0.003) (0.010) (0.010) GP adjusted mortality 0.309 −0.937 (0.642) (2.022) GP fixed effects Yes Yes Yes Yes Yes Yes Year and month Yes Yes Yes Yes Yes Yes ATC codes Yes Yes Yes Yes Yes Yes Patient education and age Yes Yes Yes Yes GP age Yes Yes Community fixed effects Yes Yes Observations 2,089,438 2,089,438 2,089,438 1,130,723 1,130,723 1,130,723 Adjusted R2 0.348 0.395 0.396 0.138 0.228 0.229 Note: In this table we present results from estimating equation (5) on the sample of weekend and public holiday GP consultations. Every column represents an individual regression estimated by OLS: In columns (1), (2), and (3), the outcome is 1{expijt > 0}; in columns (4), (5), and (6), the outcome is log(1 + expijt). Heteroskedasticity-robust and community-level clustered standard errors are given in parentheses below coefficients, stars indicate significance levels: * p < 0.1, ** p < 0.05, *** p < 0.01. a Medication history is the aggregate amount of drug expenses one year prior to the consultation. b Hospital history is the aggregate number of days spent in hospital one year prior to the consultation. thermore, onsite pharmacies generally maintain a smaller variety of drugs, and for drugs they do not have in stock, dispensing GPs have the same incentives to induce demand than non-self-dispensing GPs. This could also explain a zero effect.

Why does the existing literature find signs of supply-inducement then? First, Kaiser and Schmid(2016) and Burkhard et al.(2015) both assume that sorting of GPs into onsite pharmacies is exogenous. This may cause an upwards bias to their results which we in turn pick up with our GP fixed-effects and the physician ability measure. Second, Kaiser and Schmid(2016) and Burkhard et al.(2015) both use Swiss data where in certain cantons

87 Table 16 — Estimation results for sample of weekend and holiday prescriptions, intensive margin.

Expenses per unit Medication volume (1) (2) (3) (4) (5) (6) On-site pharmacy 0.031 0.038∗∗ 0.038∗∗ 0.033 0.032 0.044 (0.019) (0.019) (0.019) (0.125) (0.113) (0.118) Patient is female −0.074∗∗∗ −0.074∗∗∗ −0.072∗∗∗ −0.070∗∗∗ (0.003) (0.003) (0.014) (0.014) Patient drug historya 0.0002∗∗∗ 0.0002∗∗∗ 0.001∗∗∗ 0.001∗∗∗ (0.00003) (0.00003) (0.0001) (0.0001) Patient hospital historyb 0.003∗∗∗ 0.003∗∗∗ 0.052∗∗∗ 0.052∗∗∗ (0.0004) (0.0004) (0.003) (0.003) Patient wage 0.021∗∗∗ 0.021∗∗∗ −0.048∗∗∗ −0.047∗∗∗ (0.001) (0.001) (0.004) (0.004) Patient is migrant −0.045∗∗∗ −0.044∗∗∗ −0.009 −0.014 (0.004) (0.004) (0.013) (0.013) GP adjusted mortality −0.102 −2.736 (0.378) (2.488) GP fixed effects Yes Yes Yes Yes Yes Yes Year and month Yes Yes Yes Yes Yes Yes ATC codes Yes Yes Yes Yes Yes Yes Patient education and age Yes Yes Yes Yes GP age Yes Yes Community fixed effects Yes Yes Observations 1,130,723 1,130,723 1,130,723 1,130,723 1,130,723 1,130,723 Adjusted R2 0.166 0.215 0.217 0.019 0.066 0.066 Note: In this table we present results from estimating equation (5) on the sample of weekend and public holiday GP consultations. Every column represents an individual regression estimated by OLS: In columns (1), (2), and (3), the outcome is 1{expijt > 0}; in columns (4), (5), and (6), the outcome is log(1 + expijt). Heteroskedasticity-robust and community-level clustered standard errors are given in parentheses below coefficients, stars indicate significance levels: * p < 0.1, ** p < 0.05, *** p < 0.01. a Medication history is the aggregate amount of drug expenses one year prior to the consultation. b Hospital history is the aggregate number of days spent in hospital one year prior to the consultation. all doctors are allowed to dispense drugs, whereas in Austria only country doctors are permitted to do so. Country doctors may differ from others in their propensity to induce demand, which could explain the diverging results. We also know that in rural areas competition between GPs is small, and competition is typically associated with more generous prescription behavior (Scott and Shiell, 1997; Léonard et al., 2009; Ahammer and Schober, 2016). A lack of competition may explain why our observed doctors induce lower drug expenses in general.

As discussed in section III.5, we are worried that endogenous sorting between patients

88 Figure 10 — Heterogeneous eﬀects for diﬀerent patient age groups, weekend sample, extensive margin.

Positive expenses Total expenses

0.0

-0.2

-0.4

-0.6

-0.8

On-site pharmacyeffect -1.0

-1.2

(0,20] (20,30] (30,40] (40,50] (50,60] (60,70] (70,80] 80+ Patient age groups

Note: This graph depicts estimated onsite pharmacy coefficients and 95% confidence intervals from separate regressions where the sample is stratified on different patient age groups and the outcome variables are ‘positive expenses’ and ‘total expenses’ (see section III.5.1 for a detailed description). The underlying sample consists of weekend and public holiday consultations. and GPs may partly drive the effects estimated on the full sample of GP consultations. We therefore turn to the sample of weekend and holiday prescriptions (see section III.5.2 for details) where matches between patients and GPs are randomized. Estimation results can be found in Tables 15 and 16, where Table 15 considers effects at the extensive margin while Table 16 gives effects at the intensive margin. In both tables we present three different specifications for each outcome: In the first column we show the crude onsite pharmacy effect only controlling for GP fixed effects, time fixed effects, and the ATC code of the medical drug. In the second column we extend the set of covariates by patient-level observables — in particular, gender, age, migratory status, education, health proxies, and wages. In the third column we complete the model and also include time-varying GP level observables (i.e., age and our ability proxy) as well as community fixed effects.

On the extensive margin we still find a negative and statistically significant effect of con-

89 Figure 11 — Heterogeneous eﬀects for diﬀerent GP age groups, weekend sample, extensive margin.

Positive expenses Total expenses

0.3

0.0

-0.3

-0.6 On-site pharmacyeffect

-0.9

45 and less (45,60] more than 60 GP age groups

Note: This graph depicts estimated onsite pharmacy coefficients and 95% confidence intervals from separate regressions where the sample is stratified on different GP age groups and the outcome variables are ‘positive expenses’ and ‘total expenses’ (see section III.5.1 for a detailed description). The underlying sample consists of weekend and public holiday consultations. sulting a self-dispensing GP on drug expenses. The probability of receiving medication in the first place decreases by at least 12.3 percentage points — this is a rather large effect, corresponding to a reduction from 54.1% to 41.8% in terms of the sample mean. Since, conversely, the likelihood of having zero drug expenses increases by 12.3 percentage points, also overall expenses decrease by a large 38.9%. This amounts to a reduction from e 24.2 ($26.1) to e 14.8 ($15.9). These results suggest that the negative effect of having an onsite pharmacy is much more pronounced outside opening hours when the patient-GP match is random. Potentially, this could be a sign for cautious prescription behavior (Chandra et al., 2012; Lucas et al., 2010) in case GPs encounter patients whom they do not know, or conversely, for prescribing relatively more aggressive as soon as a relationship between principal and agent has been built and developed.

On the intensive margin (Table 16), we ﬁnd a positive eﬀect for drug expenses per unit:

90 Figure 12 — Heterogeneous eﬀects for diﬀerent patient education groups, weekend sample, extensive margin.

Positive expenses Total expenses

0.0

-0.2

-0.4 On-site pharmacyeffect -0.6

Compulsary Apprenticeship High school University Patient education

Note: This graph depicts estimated onsite pharmacy coefficients and 95% confidence intervals from separate regressions where the sample is stratified on different patient education groups and the outcome variables are ‘positive expenses’ and ‘total expenses’ (see section III.5.1 for a detailed description). The underlying sample consists of weekend and public holiday consultations.

In case at least one unit of medication is prescribed, self-dispensing GPs induce 3.8% higher expenses per unit. Again, we do not find any effect on medication volume. For patients that are unbeknownst to the GP, self-dispensing therefore reduces the likelihood of receiving medication. If medication is prescribed, however, it is marginally more expensive if the GP is self-dispensing. Since this effect is offset by the smaller probability of prescribing something in the first place, the overall effect of onsite pharmacies on drug expenses is negative.

In terms of our other covariates, coefficients largely have their expected sign. Females are more likely to receive medication, yet at lower cost. Sicker patients (indicated through positive coefficients on the drug and hospital coefficients) receive more and relatively expensive drugs, migrants receive more but cheaper drugs, and low-ability GPs (proxied by the adjusted mortality) prescribe more, ceteris paribus. Interestingly, higher wages

91 Table 17 — Heterogeneous eﬀects, weekend sample

Patient gender Patient wage GP gender Male Female High Low Male Female (1) (2) (3) (4) (5) (6) Positive expenses −0.112∗∗∗ −0.132∗∗ −0.092∗∗∗ −0.130∗∗ −0.021 −0.189∗∗∗ (0.037) (0.052) (0.024) (0.052) (0.017) (0.046) Total expenses −0.367∗∗ −0.405∗∗ −0.290∗∗∗ −0.411∗∗ −0.015 −0.642∗∗∗ (0.147) (0.199) (0.080) (0.205) (0.044) (0.187) Expenses per unit 0.019 0.054∗∗∗ −0.025 0.049∗∗∗ 0.039 0.030 (0.028) (0.017) (0.039) (0.019) (0.030) (0.024) Medication volume 0.202∗ −0.086 0.211∗∗∗ −0.014 0.218∗ −0.126 (0.116) (0.160) (0.078) (0.147) (0.116) (0.160) Note: In this table we present results from estimating equation (5) on different subsamples of the population, with only weekend and public holiday GP consultations considered. Every cell in the table represents an individual regression estimated by OLS. Heteroskedasticity-robust and community-level clustered standard errors are given in parentheses below coefficients, stars indicate significance levels: * p < 0.1, ** p < 0.05, *** p < 0.01. seem to have a negative effect on the extensive margin, which may also be a result of lower information asymmetry between principal and agent if we expect wages to be positively correlated with ability. Note also that our estimated onsite pharmacy coefficient is fairly stable across specifications, indicating a small correlation with other patient and GP-level observables.

III.6.1 Heterogeneous eﬀects

In Figures 10, 11, and 12, we depict estimates of the onsite pharmacy coefficients for different subsamples of the population. We restrict our analysis to outcomes on the extensive margin in the weekend sample. In all estimations we use the most comprehensive specification from columns (3) and (6) in Table 15. Figure 10 suggests that the older the patient is, the more a GP who operates an onsite pharmacy is reluctant to prescribe medication. The patient-age gradient is nonlinear — while the magnitude of the effect for both measures of the extensive margin is fairly stable up to 40 years of age, the effect increases dramatically for subsequent age groups, until it again stabilizes at the 70 year mark. Fig- ure 11 depicts effect heterogeneities for different GP age groups. We find that the negative effect on both outcomes at the extensive margin are mainly driven by mid-aged (45 to 60

92 years old) GPs, while both younger and older ones do not change their prescription behavior significantly if they have onsite pharmacies. For old GPs (above 60 years of age), we find a small positive effect, which is statistically insignificant nonetheless. Figure 12 shows that the onsite pharmacy effect increases with decreasing patient education, thus dispensing GPs prescribe more cautiously when the patient is uneducated.

Finally, Table 17 presents heterogeneous results based on patient gender and wage (where high wage is defined as above median wage, and low wage is defined as below median wage) as well as GP gender for all four outcomes considered before. Interestingly, our estimated onsite pharmacy effects seem to be driven mostly by female doctors. For male doctors effects on the extensive margin are negative as well yet smaller in magnitude and statistically insignificant. We do, however, observe a positive and borderline significant effect on number of units prescribed for males. In terms of patient gender we find almost equal effects throughout, although they generally seem to be slightly stronger for females. In terms of patient wage, effects are stronger for those earning below median.

III.7.C onclusions

In this paper, we studied whether financial incentives affect prescription behavior of general practitioners. We analyzed whether physicians who are allowed to dispense drugs themselves through onsite pharmacies (thereby earning a mark-up on every pharmaceutical they prescribe) show different prescription patterns than other, comparable doctors. It turns out that, although self-dispensing GPs have much larger per patient drug expenses than other GPs, we find negative to zero effects once we control for an extensive array of covariates and account for sorting of GPs into onsite pharmacies and matching between patients and GPs.

We have several explanations for this result which contrasts the existing literature. First, Kaiser and Schmid(2016) and Burkhard et al.(2015) both assume that sorting of GPs into onsite pharmacies is exogenous, which potentially causes their results to be biased

93 upward. In our framework, this type of sorting should be picked up by GP fixed-effects and a measure of physician ability. Second, Kaiser and Schmid(2016) and Burkhard et al. (2015) both use Swiss data where in certain cantons all doctors are allowed to dispense drugs, whereas in Austria only country doctors are permitted to do so. Country doctors may differ from others in their propensity to induce demand, and a lack of competition decreases incentives for overprescription behavior. Note, however, that we do not necessarily neglect the possibility that GPs are profit-maximizing individuals, yet the financial incentives to overprescribe may not be strong enough in our case if potential benefits do not exceed cost associated with the risk of harming the patient. Onsite pharmacies yield an average of e 109,882.5 ($118,328.63) in revenues for the same work other GPs earn nothing for. Thus, the additional income generated through onsite pharmacies may allow the GP to prescribe more cautiously. Finally, note that GPs with onsite pharmacies generally maintain a smaller variety of drugs, and for drugs they do not have in stock, dispensing GPs have the same incentives to induce demand than non-self-dispensing GPs, which could also explain a zero effect.

Although our empirical setting is very specific, at the core we analyze a very general question; namely how monetary benefits alter the provision of medical care by physicians. Our findings therefore bear important implications for policy makers: Providing financial incentives to physicians does not necessarily lead to welfare losses associated with supply inducement behavior. We do not find evidence that monetary benefits lead to excess prescription behavior, which may not only harm the individual patient, but is also costly for the entire health care system (Emanuel and Fuchs, 2008). More specifically, in terms of onsite pharmacies, our results indicate that permitting them is unlikely to affect physician prescription behavior negatively. In this context, policy makers may also consider their importance in rural medicine, where regular pharmacies are difficult to access for patients and GPs are reluctant to practice in due to an unappealing working environment.

The target of future research clearly should be to obtain further evidence on the relationship between onsite pharmacies and prescription behavior for other countries. Also, our

94 empirical set-up does not allow us to look at outcomes other than drug prescriptions; analyzing eﬀects on non-drug services or referrals along the lines of Kaiser and Schmid (2016) would deﬁnitely add to our understanding of onsite pharmacies.

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103 Curriculum Vitae Ivan Zilic

PERSONAL Name and surname: Ivan Zilic Permanent address: Ljerke Sram 4, 10000 Zagreb, Croatia Email: [email protected] Phone: +385997762723 Date of birth: 14 January 1987 Web: https://ivanziliceconomics.wordpress.com/

RESEARCH INTERESTS Applied microeconometrics, with focus on labor, health and education

EDUCATION PhD Program in Economics University of Linz & University of Innsbruck, Austria October 2014 – present

Master in Economic Analysis University Carlos III, Madrid, Spain September 2012 – September 2014

Master in Economics University of Zagreb, Croatia September 2009 – September 2010

Bachelor in Economics University of Zagreb, Croatia September 2005 – May 2009

WORK EXPERIENCE The Institute of Economics, Zagreb September 2011 – present Research assistant

PUBLICATIONS Zilic, I. (2017): Eﬀect of forced displacement on health, accepted for publication in The Journal of Royal Statistical Society: Series A.

COMPUTER SKILLS

R, Stata, LATEX