ESSAYS IN EMPIRICAL DEVELOPMENT ECONOMICS

by

Eik Leong Swee

A thesis submitted in conformity with the requirements

for the degree of Doctor of Philosophy

Department of Economics

University of Toronto

c© Copyright by Eik Leong Swee (2010)

Essays in Empirical Development Economics

Eik Leong Swee

Doctor of Philosophy

Department of Economics

University of Toronto

2010

Abstract

This thesis consists of three empirical chapters that examine issues in development eco-

nomics.

Chapter 1 focuses on the effects of civil wars on the welfare of individuals. I use a unique

data set that contains information on war casualties of the 1992-1995 Bosnian War, and exploit

the variation in war intensity and birth cohorts of children, to identify the effects of the war

on schooling attainment. I find that cohorts affected by war are less likely to complete sec-

ondary schooling, if they resided in municipalities that endured higher levels of war intensity.

Ancillary evidence suggests that my estimates are most likely picking up immediate, rather

than long-term effects. Furthermore, direct mechanisms such as the destruction of infrastruc-

ture and the out-migration of teachers do not seem to matter; instead, the ancillary evidence

suggests that youth soldiering may be more important.

Chapter 2 studies the impact of the partition which ended the Bosnian War on the post-

war provision of public goods at the municipality-level. Comparing trends in the provision

of public schooling across partitioned and unpartitioned municipalities during the 1986-2006

period, I find that partitioned municipalities provide 58 percent more primary schools and

37 percent more teachers (per capita). I also find evidence which suggests that convergent

preferences – operating via ethnic politics – for ethnically oriented schools may be an important

ii

driver of the results, although I cannot rule out the possibility of mechanical explanations. In

addition, as the increase in public goods provision may be ethnically oriented, only the ethnic

majority profits from this arrangement.

Chapter 3 provides an estimation of network effects among rural-urban migrants from

Nang Rong, Thailand, by using heterogeneous migration responses to regional rainfall shocks

among villagers as exogenous variation affecting network size. I find that social networks

significantly reduce the duration of job search, and surprisingly, draw new migrants into the

agricultural sector. I argue that this is not because agricultural jobs are more attractive than

non-agricultural ones, but rather that my estimates are essentially local average treatment ef-

fects that are estimated off agricultural workers who are most affected by rainfall shocks.

iii

Acknowledgement

I would like to thank my advisors – Professors Dwayne Benjamin, Gustavo Bobonis, and

Leah Brooks – for their guidance and support. For helpful comments and discussions, I am also

grateful to Regina Bateson, Michela Cella, Christian Dippel, Ken Jackson, Sacha Kapoor, Gian-

marco Leon, Arvind Magesan, Robert McMillan, Aloysius Siow, Hui Wang, and participants

at the HiCN Workshop, the CEA Meetings, Political Economics Conference, and the NEUDC

Conference.

My research would not have been possible without access to restricted-use data; in this

respect, I acknowledge assistance from the Bosnian Federal Office of Statistics, the Republika

Srpska Institute of Statistics, the Research and Documentation Center, and the Carolina Popula-

tion Center. I also thank the Ministry of Education and Science (Sarajevo), the Organization for

Security and Co-operation in Europe, and the United Nations High Commissioner for Refugees

for their hospitality during my stay in Sarajevo. For excellent research assistance, I am indebted

to Mirza Beširovic. I would also like to acknowledge financial support from the Centre for In-

ternational Studies and the School of Graduate Studies at the University of Toronto.

Finally, I would like to thank my family – especially to Mom and Dad – for their patience,

support, understanding, and love. And to Weilun, for her companionship and encouragement;

I truly could not have done it without her.

iv

Contents

List of Tables ix

List of Figures x

Introduction 1

1 On War and Schooling Attainment: The Case of Bosnia and Herzegovina 4

1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 4

1.2 Background to the Bosnian War . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 6

1.2.1 Bosnian War and Schooling Attainment . . . . . . . . . . . . . . . . . . . . 8

1.3 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12

1.3.1 The Bosnian Book of Dead . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12

1.3.2 The Living Standards Measurement Survey . . . . . . . . . . . . . . . . . . 15

1.3.3 Other Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18

1.4 Identifying the Effects of War . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19

1.5 Empirical Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 22

1.5.1 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 27

1.6 Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33

2 Together or Separate? Post-Conflict Partition, Ethnic Homogenization, and the Provi-

sion of Public Schooling 35

2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 35

2.2 Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 37

2.2.1 Bosnian War and the Dayton Peace Accords . . . . . . . . . . . . . . . . . 37

2.2.2 Municipal Partition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 41

v

2.2.3 Public Schooling . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 45

2.3 The Model . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 46

2.4 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 49

2.5 Empirical Methodology . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 52

2.5.1 Identification . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 52

2.5.2 Unit of Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 53

2.5.3 Addressing Threats to Validity . . . . . . . . . . . . . . . . . . . . . . . . . 54

2.5.4 Robust Standard Errors . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 57

2.6 Empirical Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 57

2.6.1 Ethnic Homogenization . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 57

2.6.2 Public Schooling . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 61

2.6.3 Ethnic Politics and Elections . . . . . . . . . . . . . . . . . . . . . . . . . . . 67

2.6.4 Distributional Consequences . . . . . . . . . . . . . . . . . . . . . . . . . . 71

2.7 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 74

2.7.1 Placebo Tests . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 74

2.7.2 Mechanical Explanations . . . . . . . . . . . . . . . . . . . . . . . . . . . . 78

2.7.3 Other Issues . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 80

2.8 Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 83

Appendix . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 85

3 Network Effects Among Migrants in the Labor Market: Evidence from Thailand 86

3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 86

3.2 Social Networks And Migration . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87

3.3 Background and Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 89

3.3.1 Nang Rong Project . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 90

3.3.2 Other Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 94

3.4 Identifying Network Effects . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 97

3.5 Empirical Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 101

vi

3.5.1 Examining Instruments . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 101

3.5.2 Instrumental Variables Regressions . . . . . . . . . . . . . . . . . . . . . . 107

3.6 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 111

3.6.1 Alternative Measures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 111

3.6.2 Selection Bias . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112

3.6.3 Other Econometric Concerns . . . . . . . . . . . . . . . . . . . . . . . . . . 114

3.7 Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 116

Appendix . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117

References 121

vii

List of Tables

1.1 Descriptive Statistics (War Casualties) . . . . . . . . . . . . . . . . . . . . . . . . . . 15

1.2 Descriptive Statistics (Schooling Attainment) . . . . . . . . . . . . . . . . . . . . . . 17

1.3 Difference-in-Differences Regressions . . . . . . . . . . . . . . . . . . . . . . . . . . 23

1.4 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 26

1.5 Difference-in-Differences Regressions (Health Outcomes) . . . . . . . . . . . . . . . 32

2.1 Pre-War Municipal Descriptive Statistics . . . . . . . . . . . . . . . . . . . . . . . . . 55

2.2 Partition and Ethnic Homogenization . . . . . . . . . . . . . . . . . . . . . . . . . . 58

2.3 Partition and Public Schooling (Raw Data and Imputations) . . . . . . . . . . . . . 63

2.4 Partition and Public Schooling . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 66

2.5 Partition and Elections . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 69

2.6 Distributional Consequences . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 72

2.7 Placebo Tests . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 75

2.7 Placebo Tests (continued) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 77

2.8 Other Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 81

2.A.1 Political Parties and Ideological Categorization . . . . . . . . . . . . . . . . . . . 85

3.1 Descriptive Statistics (Individual) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 93

3.2 Descriptive Statistics (Village) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 96

3.3 Reduced-Form Regressions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 103

3.4 OLS & IV Regressions (Job Search) . . . . . . . . . . . . . . . . . . . . . . . . . . . . 105

3.5 OLS & IV Regressions (Job Type) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 109

3.6 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 113

3.A.1 Constructing Network Size . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117

3.A.2 OLS & IV Regressions (Wages) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 118

viii

3.A.3 Alternative Specifications . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 119

3.A.4 Non-Response . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 120

ix

List of Figures

1.1 Fitted Regression of Schooling Attainment by Cohort and War Casualty Rate . . . 21

1.2 Pre-War and Post-War Statistics on Schools and Teachers . . . . . . . . . . . . . . . 25

1.3 War Effects by Cohort . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 29

2.1 Municipalities by Ethnic Majority (Pre-War) . . . . . . . . . . . . . . . . . . . . . . . 39

2.2 Municipalities by Ethnic Majority (Post-War) . . . . . . . . . . . . . . . . . . . . . . 42

2.3 Municipalities by Entity . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 43

2.4 Municipalities by Frontline and Partition . . . . . . . . . . . . . . . . . . . . . . . . 44

2.5 Demographics by Partition and Year . . . . . . . . . . . . . . . . . . . . . . . . . . . 60

2.6 Public Schooling by Partition and Year . . . . . . . . . . . . . . . . . . . . . . . . . . 62

3.1 Fitted Regression of Migration on Rainfall . . . . . . . . . . . . . . . . . . . . . . . . 106

3.2 Fitted Regression of Migration on Village Rice Production . . . . . . . . . . . . . . . 107

3.3 How Rainfall Affects The Type of Migrants . . . . . . . . . . . . . . . . . . . . . . . 111

x

Introduction

The study of development economics has witnessed tremendous change in recent decades.

By making use of economic theory and econometric methods, combined with expertise from

other academic fields such as political science and sociology, it has evolved into one of the

liveliest areas of research among the social sciences (Ray, 2000). This evolution is by no means

accidental; developing countries face a multitude of intrinsically diverse issues, all of which

require specialized treatment. In this dissertation, I consider two such issues – civil conflict

and rural-urban migration.

The first two chapters address problems related to civil conflict, an intricate phenomenon

that has plagued numerous developing countries around the world, especially in Africa, Cau-

casia, the Balkans, and the Middle East. In fact, the association of civil conflict to underdevel-

opment is startling – in the period 1965–2004, there were 84 civil wars across the globe, all of

which involved developing countries (Collier, Hoeffler, and Rohner, 2008). Nonetheless, until

recently, development economists have rarely addressed the issue of civil conflict, due in part

to the lack of reliable data (refer to Blattman and Miguel (2009) for a survey of the literature). As

such, important questions, such as those concerning the microeconomic aspects of civil wars,

have often been overlooked. To this end, the first two chapters of my dissertation employ new

micro-level data from Bosnia and Herzegovina to examine the effects of the 1992-1995 Bosnian

War on the welfare of individuals.

In Chapter 1, I explore the following questions regarding the microeconomic consequences

of civil wars. First, what are the effects of civil wars on the schooling attainment of affected

cohorts? Second, through what mechanisms do these effects operate? I use a unique data set

that contains information on municipality-level casualties of the Bosnian war, and exploit the

variation in war intensity and birth cohorts of children, to identify the effects of the war on the

1

2

schooling attainment of affected cohorts. Having collected a wide array of data on individuals’

physical and mental health, war damage and repair, and out-migration during the war, I am

also able to discuss the possible mechanisms through which war affects schooling attainment.

My empirical results suggest that individuals in the affected cohorts are less likely to complete

secondary schooling, if they resided in municipalities that experienced higher levels of war

intensity. In particular, I estimate that a one standard deviation increase in the number of war

casualties per capita decreases the likelihood of secondary school completion by 3 percentage

points. On the other hand, I find no significant effects of war on the completion of primary

schooling. Using ancillary evidence, I argue that these results are most likely picking up im-

mediate, rather than long-term effects. Furthermore, I find that direct mechanisms such as the

destruction of infrastructure and the out-migration of teachers do not seem to matter; instead,

the ancillary evidence suggests that youth soldiering may be more important. This chapter

involves one of the first empirical work to directly estimate the effects of a civil war by using

intrastate casualty rates; it also registers an attempt to infer the mechanisms through which

civil wars affect individuals’ welfare.

Chapter 2 – the main chapter of this dissertation – focuses on the effects of post-conflict par-

titions, a previously unexplored theme in the economics literature. Again, using the context of

the Bosnian War, I address the following questions. First, do we observe a greater provision

of public schooling in partitioned municipalities and, if so, why? Second, what are the dis-

tributional consequences of partition-induced differential provision of public schooling? My

results suggest that the partition induced ethnic homogenization, and that partitioned munic-

ipalities, on average, provide 58 percent more primary schools and 37 percent more teachers

(per capita) than unpartitioned ones, controlling for time-invariant municipal differences and

aggregate shocks across municipalities. These effects appear to be driven by convergent prefer-

ences – operating via ethnic politics – for ethnically oriented schools. In fact, I find that children

who reside in partitioned municipalities are more likely to attend and complete school; how-

ever, if they belong to the ethnic minority, then this advantage is completely eroded, implying

3

that the differential provision of public schooling may have benefitted the ethnic majority but

not the ethnic minority. This chapter establishes the consequences of residing in partitioned

jurisdictions in a post-conflict society, by providing estimates of level and distribution effects;

it also explores the role of ethnic homogenization in the relationship between partition and

public goods provision.

In the final chapter, I explore the issue of rural-urban migration. In the context of develop-

ing countries, networks are extremely valuable as labor markets are plagued with information

asymmetries. While network effects are important, however, they are not easily identified em-

pirically due to endogeneity biases in the form of selection and simultaneity. To this end, Chap-

ter 3 concerns the estimation of network effects – among migrants who have moved from the

rural district of Nang Rong, Thailand, to one of several urban destinations during the 1970-2000

period – by using heterogeneity in migration responses to regional rainfall shocks as exogenous

variation affecting network size. My empirical results suggest that networks are important in

the job search process. In particular, I estimate that a one standard deviation increase in the

network size increases the likelihood of finding a job within the first month of migration by

approximately 9 percentage points. Surprisingly, I also find that networks draw new migrants

into the agricultural sector, and I argue that this is because my estimates are essentially local

average treatment effects that are estimated off agricultural workers who are most affected by

rainfall shocks. This chapter represents an attempt to improve the estimation of network ef-

fects in the existing literature, by considering social networks at the village level; it also shows

that networks may appear to direct migrants into lower-paying sectors, when the effects are

estimated using rainfall as an instrument for network size.

Chapter 1

On War and Schooling Attainment: The Case of Bosnia and

Herzegovina

1.1 Introduction

The subject of civil war has received significant attention in recent years, due to numerous

episodes of intrastate armed conflict around the world, especially in Africa, Caucasia, the

Balkans, and the Middle East. According to Collier, Hoeffler, and Rohner (2008), there were

84 civil wars across the globe in the period 1965–2004. More than 50 countries have been

involved, of which 23 have experienced repeat civil wars.1 The demographic consequences

of civil wars are tremendous, as millions of people are killed or displaced from their homes.

Stewart, Huang, and Wang (2001), for instance, estimate that over 12 million people – mostly

civilians – were killed in 25 major civil wars, while the UNHCR (2008) reports that more than

20 million people have been internally displaced by civil wars by the end of 2007.2

Despite the prevalence of civil wars and the ensuing human losses, most researchers have

limited their attention to country-level statistics in examining conflict and few, hitherto, have

employed intrastate variation in conflict to examine its impact on welfare at the individual

level. For instance, scholars who seek the causes of civil wars have argued that a variety of

socio-economic and institutional factors at the aggregate level make armed conflict feasible and

profitable (Collier and Hoeffler, 1998; Collier and Hoeffler, 2004; Collier, Hoeffler, and Rohner,

2008; Miguel, Satyanath, and Sergenti, 2004), while those who examine the impact of wars

1Collier, Hoeffler, and Rohner’s (2008) figures rely on data from the Correlates of War (COW) Project, which isoriginally provided by Singer and Small (1994) and recently updated by Gleditsch (2004). Civil wars are defined byarmed conflicts that are not interstate, and which result in at least 1,000 battle deaths per year.

2Stewart, Huang, and Wang’s (2001) estimate of war casualties reflects 25 major civil wars – in countries whereover 0.5 percent of the population were killed – during the period 1970–1995, according to data provided by Sivard(1996). The exact number of displaced persons reported by the UNHCR (2008) is 26 million, of which approximately23 million are displaced by civil wars.

4

5

have focused on the macroeconomic indicators, finding no effect in the long-run (Davis and

Weinstein, 2002; Brakman, Garretsen, and Schramm, 2004; Miguel and Roland, 2006). Due to

the increasing availability of data from conflict regions in recent years, however, researchers

now find it possible to examine conflict at the intrastate level. In particular, recent research

suggests that children who are born in regions experiencing civil conflict are impacted with

lower height for age z-scores (Akresh, Verwimp, and Bundervoet, 2007; Bundervoet, Verwimp,

and Akresh, 2008), while exposure to civil conflict is found to have adverse effects on school

enrollment and attainment (Merrouche, 2006; Shemyakina, 2007; Akbulut-Yuksel, 2008; Akresh

and de Walque, 2008; Sanchez and Rodriguez, 2008).3 Nevertheless, more work remains to be

done in terms of quantifying the effects of civil wars on individuals’ welfare, as well as in

uncovering the precise mechanisms through which the relationship operates.

My main contribution in this study is the use of a unique data set that contains information

on war casualties at the intrastate level of Bosnia and Herzegovina (hereafter, Bosnia), which,

alongside cohort differences, allows me to identify the effects of the 1992–1995 civil war in

Bosnia (hereafter, the Bosnian War) on schooling attainment. My empirical strategy exploits

the variation in birth cohorts of children – which determines whether they were in primary

and secondary schools during the war – and that in war intensity, represented by the number

of war casualties per capita, across Bosnian municipalities.4 A secondary contribution of this

study is the ability to shed light on a wide range of possible mechanisms through which civil

war affects schooling attainment, given the availability of data on individuals’ physical and

mental health, war damage and repair, and out-migration during the war.

My empirical results suggest that individuals in the affected cohorts are less likely to com-

plete secondary schooling, if they resided in municipalities that experienced higher levels of

war intensity. In particular, I estimate that a one standard deviation increase in the number

3Several other authors have also examined the impact of civil wars by looking at other microeconomic outcomes.For example, exposure to war violence in Sierra Leone is associated with increased political awareness (Bellows andMiguel, 2006), while the Angolan civil war may have erected barriers to entry that benefited incumbent diamondmining companies (Guidolin and Ferrara, 2007).

4Kondylis (2007) uses the same approach on the Bosnian war casualty data to construct a measure of conflictseverity. However, to the extent that I am using an updated version (September 2008) of the data, our measuresmay differ slightly.

6

of war casualties per capita decreases the likelihood of secondary school completion by 3 per-

centage points. On the other hand, I find no significant effects of war on the completion of

primary schooling. Using ancillary evidence, I argue that these results are most likely picking

up immediate, rather than long-term effects. Furthermore, I find that direct mechanisms such

as the destruction of infrastructure and the out-migration of teachers do not seem to matter;

instead, the ancillary evidence suggests that youth soldiering may be more important.

In general, the findings in this study resonate with the existing literature. For instance,

Ichino and Winter-Ebmer (2004) and Akbulut-Yuksel (2008) find that Germans who were in

the schooling cohorts during World War II received less education than their counterparts. As

well, Merrouche (2006), Shemyakina (2007), Akresh and de Walque (2008) and Sanchez and Ro-

driguez (2008) find that exposure to civil war reduces schooling attainment in Cambodia, Tajik-

istan, Rwanda and Columbia respectively. Overall, the congruency of these findings should not

be taken lightly. Apart from the loss of human lives, civil wars can also significantly decrease

the schooling attainment of children, which may worsen their longer term welfare and impede

the economic growth of their countries [see Krueger and Lindahl (2001) for a literature review

of the long-run effects of education on growth].

The rest of this chapter is organized as follows. Section 1.2 constitutes a brief history of the

Bosnian War and a discussion on the possible channels through which it may have affected

schooling attainment. A description of the data and the identification strategy are laid out in

Sections 1.3 and 1.4. Section 1.5 provides the empirical analyses and robustness checks. Section

1.6 concludes.

1.2 Background to the Bosnian War

Bosnia is a country on the Balkan peninsula of Southern Europe, with a long history of ethnic

diversity and conflict. Being strategically located at the crossroads between east and west, it

has historically been a battleground for major military powers, including the Illyrians, Romans,

Hungarians, and Ottomans, before finally being established by Josip Broz Tito as one of the

7

six federal units – Bosnia, Croatia, Macedonia, Montenegro, Serbia and Slovenia – under the

Socialist Federal Republic of Yugoslavia in 1943.

According to the 1991 Yugoslav census, the population of Bosnia was 4.4 million, contain-

ing large groups of Bosniaks (44 percent), Serbs (31 percent) and Croats (17 percent). Although

ethnic diversity was also analogous to religious diversity – as the majority of Bosniaks are

Muslims, and almost all Serbs and Croats are Orthodox Christians and Roman Catholics re-

spectively – all Bosnians share the same heritage of being South Slavs and speak essentially

one language.

In general, inter-ethnic relations in pre-war Bosnia were amicable, as Tito managed to en-

force a strict policy of “brotherhood and unity” by suppressing ethno-nationalism among the

various narods (“nationalities” or “ethnicities”). According to Vulliamy (1994), Bosnians who

lived in towns and cities were more tolerant for a multi-ethnic state than those living in rural

areas, and those who could not assimilate to the urban lifestyle were waiting for the right mo-

ment to reignite the spirit of ethno-nationalism.5 Indeed, shortly after Croatia, Macedonia and

Slovenia declared independence in 1991, Yugoslavia began to dissolve and civil war broke out

in Bosnia between the pro-independence Bosniak-Croat coalition and the Serbs who boycotted

the referendum for independence.

When the Bosnian War began in April 1992, the Serbs were led by Radovan Karadžic, the

leader of the Serbian Democratic Party (SDS), who was a strong proponent of the Greater Serbia

agenda, alongside the President of Serbia, Slobodan Miloševic. While the agenda called for an

end to the oppression and exploitation of Yugoslav Serbs, it was later used as a propagandistic

tool to incite “ethnic cleansing” in Serb-controlled territories (Burg and Shoup, 1999). As a

result, the Bosnian Serb forces carried out waves of aggression that marked the earliest events

of the Bosnian War, killing and displacing thousands of Bosniaks and Croats (Vulliamy, 1994).

Soon, however, the Bosniak-Croat alliance fell apart – due partly to the increasing call for a

Croatian Union of Herzeg-Bosna among the Croat leaders – and the war was officially fought

5In fact, Vulliamy (1994) reports that Sarajevans regard the Bosnian War as one between the raja (“urbane andtolerant person”) and the papak (“hillbilly”).

8

on three fronts.

By and large, most of the fighting took place in the eastern, northeastern and northwestern

regions of Bosnia. These regions were vital to the Serb nationalists because they were adjacent

to Serbia and served as a corridor to the Serb-dominated enclaves in Croatia. Notably, both

regions had a substantial non-Serb population prior to the war, which presented itself as an

obstacle to the Serb aggressors. In the later stages of the war, central Bosnia also became a war

zone as it was important to the Croat nationalists who wanted to establish the Croatian Union

of Herzeg-Bosna in that region.

In August 1995, the North Atlantic Treaty Organization, prompted by widespread mas-

sacres, conducted sustained air strikes against the Serb strongholds, thus internationalizing the

conflict in its final stages (Owen, 1997a; Owen, 1997b). Subsequently, all three ethnic groups

signed the Dayton Peace Agreement in December 1995, concluding four years of conflict in

Bosnia. The agreement partitioned Bosnia by an Inter-Entity Boundary Line (IEBL) into two

ethnically-divided entities – the Bosniak-Croat Federation of Bosnia and Herzegovina (FBiH)

and the Serb Republika Srpska (RS). Overall, the human cost of the war was tremendous. The

Research and Documentation Center (RDC) reports that approximately 96,000 civilians and

soldiers were killed or missing, and the Bosnian Ministry for Human Rights and Refugees es-

timates that 2.2 million people were displaced from their homes, half of whom sought refugee

protection outside Bosnia. These figures imply a startling casualty rate of 22 deaths per thou-

sand, and a displacement rate of one in every two people, making the Bosnian War one of the

most violent conflicts in recent history.

1.2.1 Bosnian War and Schooling Attainment

While the Bosnian War was undoubtedly violent, how pervasive were its effects on the com-

pletion of schooling for the affected cohorts? And through what channels? In this section, I

explore several mechanisms that are applicable to Bosnia.

In the pre-war days, Tito considered education to be one of the most important activities for

9

the development of Yugoslavia, and made sure that the Yugoslav state retained a firm control

over education so as to cement the multi-ethnic state. A system of free schooling and the

adoption of eight years of mandatory primary schooling (for those aged 7–15) ensured that the

completion of primary schooling was virtually universal.6 That said, many students did not

go on to attend secondary schooling, which required another four years of general or technical

studies, and very few actually attended university.

On the whole, most individuals between the ages of 7–19 were in school at the time when

conflict broke out, and their education must have been affected in one way or another over

the course of nearly four years of battle. First of all, the most direct channel of impact is the

reduction in accessibility to education. According to the UNHCR, approximately 34 percent

of housing units were damaged by artillery shells during the war, of which many were com-

pletely destroyed. This suggests that many school buildings and other educational facilities

may have also been damaged or destroyed. Furthermore, many localities were forced to con-

vert schools into refugee centres or hospitals to accommodate displaced persons who fled their

homes in search of safer areas within Bosnia (Mazowiecki, 1994). Apart from the destruction

and dispossession of school infrastructure, the out-migration of teachers may have also im-

pacted accessibility to education. In fact, the UNHCR estimates that more than one million

people sought refugee protection overseas, and some of these may have included teachers and

other educators. To some extent, the military draft may have further diminished the ranks of

teachers.

Nevertheless, the impact of damaged infrastructure and the out-migration teacher may

have been muted, as several reports suggest that the remaining teachers continued to or-

ganize classes during the war, and attendance appeared to be relatively high (Mazowiecki,

1994). These so-called “war schools” were conducted in makeshift classrooms in homes, cafes,

garages and basement shelters, often without proper equipment, electricity or heat, as the dan-

6Since 2004, mandatory schooling has been increased to nine years, which effectively lowers the level of difficultyfor the first two years (although many schools continue to abide by the eight-year system). This, however, shouldnot affect my sample, as I am looking at individuals aged 15 or older in 2001, who would have started primaryschool under the eight-year system.

10

ger from artillery shelling and the destruction of school infrastructure forced schooling to go

underground.7 Moreover, it was extremely difficult to organize war schools in cities and en-

claves under siege, as the school year was truncated and class schedule was irregular – due to

the variability in the intensity of shelling and sniper fire. In fact, teachers were a scarce resource;

not only were they shared among two or more schools, they also had to take on multiple admin-

istrative duties such as coordinating class schedules and securing premises (Berman, 2001). In

particular, while it was possible to organize classes for primary education with a standardized

curriculum, coordinating secondary education was incredibly challenging, because the variety

of subjects across general and technical vocations meant that (i) secondary schools could not

benefit from resource-sharing and (ii) finding the appropriate teachers for every subject was

difficult. That said, these efforts ensured that the education system was not completely inca-

pacitated during the war, and in terms of relevance to this study, may have diminished the

effects of the war on the completion of primary (and possibly secondary) schooling.

Of course, the demand side of schooling matters too. For example, the military draft could

have affected some of the older students who may have been encouraged to fight alongside

adult soldiers. Indeed, students were reportedly alternating between attending war schools

and showing up on the front lines for duty (Berman, 2001). That said, one should note that

the most apparent impact of soldiering on schooling attainment – incompletion due to death

– cannot be ascertained in this study as deceased individuals would not be included in the

data. Therefore, should war effects be attributed to soldiering, they ought to be interpreted as

a lower bound of the true effects.8

Several other demand factors can also be seen from the parents’ perspective. For instance,

to attend school during the war meant having to commute amidst constant artillery shelling

7During the war, an incredible network of coordination was built on the enduring cooperation between parents,teachers, students, municipal and local government bodies, to ensure that students continued their schooling, andimportantly, a sense of normalcy was maintained. Specifically, schools operated at the local level, with a fair bitof centralized initiatives developed or sanctioned by the Ministry of Education and the Pedagogical Institute. Infact, explicit guidelines – which contained the “Basic Work Programs” that laid out the abbreviated school curriculaand instructions for adapting to local conditions – were pre-tested in focus groups and passed down to teachers(Berman, 2007).

8In fact, according to Blattman and Annan (2007), the stress on families of losing a child may also have a neg-ative impact on the psychological health or schooling of the remaining siblings, and these negative externalities ofsoldiering are also excluded from my estimates.

11

and sniper fire; therefore, parents, who inevitably fear for the safety of their children, may have

discouraged them from going. In addition, in the case of displaced families, parents may be in

a state of shock or feel uncertain about the duration of their stay, and thus feel less inclined to

send their children to school. There is also the possibility that parents substituted away from

schooling expenditure towards the consumption of basic necessities, especially when liveli-

hoods were taken away, as suggested by Shemyakina (2007) and Akresh and de Walque (2008).

While there is no direct evidence to support or refute this hypothesis for Bosnia, it is likely that

this channel of influence on primary schooling is minimal, given that primary schooling is free.

Also, substitution effects are only possible given the availability of war schools, which implies

that these (substitution) effects, especially on secondary schooling, are of second-order at best.

While schooling may have been disrupted during the war, the affected cohorts could have

resumed schooling after the war. In particular, this study looks at the schooling attainment

outcomes six years after the end of the conflict, which implies that individuals in the affected

cohorts would have had sufficient time to catch up on their secondary education (and for some,

primary education). As such, I ought to consider not only the immediate effects of the Bosnian

war, but also any lingering influence it may have on Bosnia’s education system.

Indeed, one glaring consequence of the war on Bosnia’s education system is the establish-

ment of ethnically-segregated schools, in which classes are conducted in the language and cur-

riculum of the ethnic majority, discouraging school attendance of the ethnic minority (Bozic,

2006). In fact, many returning refugees from the minority ethnic group are extremely un-

comfortable with their local school’s ethnocentric curriculum, and some even resort to buss-

ing their children to faraway municipalities where they can attend schools of their ethnicity

(OSCE, 2007). In addition, war may bring about differences in the accessibility to and quality

of post-war education, via differences in the extent of post-war reconstruction.

To summarize, there are several channels through which the war may have affected school-

ing attainment, including reduced accessibility to education, a fall in demand due to soldiering

commitments or parental indisposition, and other (adverse) lingering effects on the education

12

system. Whether any of these mechanisms are important remains an empirical question that I

will address later on.

1.3 Data

The empirical bases of this study are the data on municipality-level war casualties from the

1991–1995 Bosnian Book of Dead Project, and the individual-level information from the 2001–

2004 Bosnian Living Standards Measurement Surveys (LSMS). In addition, I construct wartime

statistics with the help of other data sources. The rest of this section describes the data that I

use.

1.3.1 The Bosnian Book of Dead

The 1991–1995 Bosnian Book of Dead Project (also known as the Human Losses in Bosnia

and Herzegovina Project) was conducted by the Research and Documentation Center (RDC)

in Sarajevo. Being an independent, nongovernmental, nonprofit, and nonpartisan entity, the

RDC’s primary role is to investigate, document, and publish accurate and unbiased statistics

on genocide, war crimes and human rights violations that took place during the Bosnian War.

The project collected a variety of statistics, including the number of war casualties – a col-

lective term used in this chapter to refer to individuals who were killed or missing – which

are documented based on death records and statements by surviving family members and

witnesses. Around 85 percent of the records are relatively complete – containing the victim’s

vital information at the time of death, including name, age, ethnicity, location of residence

and death, military or civilian status, and some even include a picture of the deceased. After

years of careful documentation and cross-referencing with a wide variety of other databases,

the Bosnian Book of Dead is not only methodologically sound, but also the largest and most

complete data on war casualties inflicted in the Bosnian War (Ball, Tabeau, and Verwimp, 2007).

To gain a basic understanding of the data, I construct Table 1.1 to show the descriptive

statistics of war casualties by region of suffering. As of August 2008, the Bosnian Book of

13

Dead reveals that 96,749 individuals were killed or missing, an average of 849 casualties per

municipality. From Table 1.1, it is evident that most of the victims (around 60 percent) are sol-

diers, and Bosniaks constitute the majority of casualties. The eastern and northeastern regions

have the highest number of casualties; however, in terms of the casualty rate – defined as the

number of war casualties per capita in each municipality – central Bosnia also appears to be

a region of considerable suffering. In fact, for the purpose of reflecting the severity of violent

conflict, the casualty rate is probably most suitable.9 Thus, for empirical purposes, I will use

the municipality-level casualty rate as the proxy for war intensity.10

9For example, in terms of the number of war casualties, Srebrenica – a Bosniak enclave that suffered one of theworst massacres during the Bosnian War – has the highest at 8862 but Kalinovik – which hosted several concen-tration camps – has one of the lowest at only 242. If we consider the casualty rate instead, both Srebrenica andKalinovik will be among the top 10 percentile of all municipalities, which better reflects the intensity of conflict.

10In choosing the measure of war, one possibility is to exploit the variation in the timing of war for differentlocalities (Akresh, Verwimp, and Bundervoet, 2007; Bundervoet, Verwimp, and Akresh, 2008). However, when theBosnian War began in eastern Bosnia in early 1992, ethnic violence quickly spread to the rest of the country by theend of the year, so it is difficult to implement a timing measure of war. Hence, I adopt a measure for war intensityinstead.

14

Table 1.1 ‐ Descriptive Statistics (War Casualties)

West

Northwest

North

Northeast

East

Southeast

Central

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

War casua

lties

849

856

707

835

1462

923

328

752

(1148)

(812)

(1112)

(539)

(2091)

(773)

(635)

(475)

Casua

lty ra

te0.022

0.017

0.013

0.016

0.031

0.036

0.010

0.019

(0.030)

(0.012)

(0.011)

(0.007)

(0.055)

(0.029)

(0.012)

(0.011)

Civilian

s340

138

413

166

745

358

123

148

(804)

(82)

(938)

(88)

(1585)

(422)

(212)

(96)

Male

765

815

639

778

1361

783

276

700

(1063)

(795)

(1017)

(513)

(1976)

(623)

(562)

(453)

Aged 0‐14

1512

811

2126

612

(24)

(11)

(13)

(16)

(28)

(34)

(13)

(12)

Aged 15‐64

707

769

529

733

1243

753

253

670

(969)

(772)

(820)

(463)

(1805)

(612)

(533)

(443)

Aged 65+

4427

4731

6359

3123

(76)

(23)

(70)

(18)

(128)

(83)

(46)

(11)

Bosniak

565

592

423

307

1138

656

183

444

    

(1009)

(637)

(932)

(295)

(1966)

(608)

(388)

(326)

Serb

213

248

245

387

283

223

73107

    

(219)

(253)

(195)

(334)

(232)

(194)

(131)

(134)

Croat

6815

35139

3740

69198

    

(103)

(33)

(53)

(83)

(78)

(56)

(127)

(146)

Other

31

43

44

23

    

(6)

(1)

(8)

(2)

(7)

(6)

(8)

(3)

109

717

919

2619

12

Average across 

mun

icipalities

Region of suffering

Num

ber o

f mun

icipalities

Stan

dard

deviations

inpa

rentheses.War

casualtie

sreferto

thenu

mberof

dead

ormissing

individu

alsby

mun

icipality

.Casua

ltyratesareconstructed

by using th

e nu

mber o

f war casua

lties divided by the po

pulatio

n in 1991, fo

r each mun

icipality

.

 28

15

1.3.2 The Living Standards Measurement Survey

The 2001–2004 Bosnian LSMS, conducted by the World Bank, is a nationally-representative

household survey that covers 25 municipalities (14 from the FBiH, and 11 from the RS). The

sampling procedure is as follows. First, each municipality is assigned one of six cells, by en-

tity (FBiH or RS) and type (urban, rural or mixed), using information from the 1991 Yugoslav

census. Then, municipalities are independently sampled from each cell, with a probability that

is proportional to population size. Among the chosen municipalities, 5,400 households were

randomly selected in 2001, approximately half of which were re-interviewed for the panel.

The attrition rate across waves is around 5 percent, which is relatively low compared to other

national panels.

The key variables that I use from the LSMS are schooling attainment, individual character-

istics and migration history, all of which are contained inside the first wave. However, several

other variables which are important to this study – ethnicity, subjective health, and physical

disabilities, for instance – are only available in subsequent waves from the panel. Therefore,

in order to maintain a balanced sample, I will only be using the panel in this study.11 Overall,

around 5,000 individuals remain in the sample.

The key outcome variable on schooling attainment is derived from the LSMS variable, “the

highest level of diploma obtained”. I construct dummies for primary and secondary school

completion by checking if an individual reports having at least a primary or secondary school

leaving certificate. In my sample, around 85 percent of individuals have completed primary

school, of which two-thirds have completed secondary schooling or more. I also use migration

data to match each individual’s pre-war municipality of residence to its corresponding casualty

rate. It turns out that the individuals in my sample resided in 75 pre-war municipalities, which

gives me a fair degree of geographical variation in terms of analyzing the effect of war intensity.

11Furthermore, the design of the first wave resulted in the oversampling of urban households, because munic-ipalities that were larger – and probably more urban – were chosen with higher probabilities. This problem wascompensated in the panel design, by retaining all rural and mixed municipalities while sub-sampling only the ur-ban ones. As a result, the first wave, though having the merit of having the largest sample, has a disproportionatelyurban representation when used on its own.

16

Table 1.2 shows the summary statistics of primary and secondary schooling attainment, by

age group and municipality-level casualty rate quantiles. I discard individuals who are aged 14

and below, because students normally do not complete their primary education before the age

of 15. Notice that the youngest age group (aged 15–28 in 2001) constitutes the affected cohorts,

that is, these individuals were aged 7–19 in the years 1992–1995 and would have been attending

either primary or secondary school. In particular, those aged 7–15 (or 15–24 in 2001) would

have been in primary school, and those aged 16–19 (or 22–28 in 2001) would have been in

secondary school. From Table 1.2, a quick comparison-in-means between individuals from the

high and low casualty municipalities in columns (1) and (5) indicate that the affected cohorts

may have lower completion rates in primary and secondary schooling.

However, by doing the same comparison for other (unaffected) cohorts, we can see that

differences in schooling completion existed prior to the war. On the whole, Table 1.2 suggests

the possibility of a pre-existing correlation between conflict intensity and schooling attainment,

which I will deal with in Section 1.4.

Several health variables are also available from the later waves in the LSMS. For instance,

I use responses from self-reported health (ranked “very poor” to “excellent”), physical dis-

abilities (“yes” or “no”) and the frequency of recalling war trauma (from “not at all” to “ex-

tremely often”) to construct dummies. A novel feature of the Bosnian LSMS is that a symptom

inventory – the Hopkins Symptom Checklist – was included and can be used to calculate a de-

pression score (1–4) which corresponds to the likelihood of significant emotional illness. This

depression score allows me to construct a dummy for depression, based on a well-known cutoff

(Derogatis, Lipman, Rickels, Uhlenhuth, and Covi, 1974).12

12The Hopkins Symptom Checklist questions in the Bosnian LSMS were developed by the Harvard Program inRefugee Trauma. Out of the original 25 questions, only those on depression were included in the survey, and onewas dropped based on the pilot test results. The depression score is simply the average of the score on the remaining14 questions. Barring further clinical evidence, the common cutoff of 1.75 is preferred.

17

Table 1.2 ‐ Descriptive Statistics (Schooling Attainment)

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

High casualty ra

te0.953

0.907

0.680

0.613

0.526

0.619

0.406

0.347

740

(0.211)

(0.291)

(0.468)

(0.489)

(0.501)

(0.487)

(0.492)

(0.478)

Med

ium casua

lty ra

te0.969

0.968

0.867

0.739

0.642

0.736

0.606

0.565

1741

(0.174)

(0.176)

(0.340)

(0.440)

(0.480)

(0.441)

(0.489)

(0.496)

Low casua

lty ra

te0.975

0.958

0.835

0.644

0.595

0.687

0.550

0.364

2514

(0.155)

(0.201)

(0.372)

(0.479)

(0.491)

(0.464)

(0.498)

(0.482)

Num

ber o

f ind

ividua

ls1383

1324

1282

1006

1383

1324

1282

1006

4995

Group of 

mun

icipalities

Num

ber o

f individu

als

Stan

dard

deviations

inpa

rentheses.Casua

ltyratesareconstructedby

usingthenu

mberof

war

casualtie

sdivide

dby

thepo

pulatio

nin

1991,for

each

mun

icipality

.Mun

icipalities

arecatego

rizedby

casualty

rate

into

threeequa

lqua

ntiles‐H

igh(casua

ltyrate

greaterthan

2.41

percent),

Low

(casua

ltyrate

less

than

1.24

percent),

and Med

ium (o

therwise).

Prim

ary scho

oling completion

Second

ary scho

oling completion

Aged 15‐28 

(affe

cted

)Aged 29‐42 

(una

ffected

)Aged 43‐56 

(una

ffected

)Aged 57+ 

(una

ffected

)Aged 15‐28 

(affe

cted

)Aged 29‐42 

(una

ffected

)Aged 43‐56 

(una

ffected

)Aged 57+ 

(una

ffected

)

 29

18

1.3.3 Other Data

I rely on data from the Bosnian Federal Office of Statistics (FOS) to estimate pre-war and post-

war conditions. I use the statistical yearbooks (1988, 1989, 1996, and 1997), which contain

primary schooling information such as the number of schools and teachers, to construct mea-

sures for the pre-war quality of primary schooling for each municipality. In particular, I divide

the number of primary schools (and teachers) by the population aged 0-14 in thousands, to

obtain “schools per capita”(and “teachers per capita”). Even though I also have information

on the number of students, I choose not to adopt school size or teacher-student ratios because

enrollment may be endogenous.

Typically, wartime data is difficult to obtain because the collection and processing of data

are paralyzed when organizations are diverted to conflict-related issues. However, with help

from the UNHCR, I am able to ascertain the extent of damage to housing units in 1995, as well

as repairs completed by the end of 2005, both of which are useful for uncovering mechanisms

later on. In addition, the UNHCR maintains a database of internally displaced persons that

allows me to construct data on the number of out-migrants for each municipality. As the UN-

HCR database is based on registered internally displaced persons who return to their original

municipality of residence or move to another municipality, it precludes international refugees

who remain overseas. Nevertheless, it reflects the migration patterns that took place during

the war, which is useful for testing the impact of teacher out-migration.

Notably, as Bosnia has 109 municipalities before the war, and 150 after (due to the division

of several municipalities by the IEBL), constructing pre-war per capita measures for the new

municipalities is cumbersome. Fortunately, the 1991 Yugoslav census reports data at the set-

tlement (sub-municipality) level, which enables me to compute accurate population figures for

municipalities that only existed after the war. Using this data, I am able to compute war casu-

alty rates (see Section 1.3.1) and the number of out-migrants per capita for each municipality.

19

1.4 Identifying the Effects of War

The estimation of war effects is a particularly challenging task, as unobserved pre-war condi-

tions may determine both post-war outcomes as well as war intensity (or incidence), causing

endogeneity bias in an OLS estimation. For instance, if a low level of initial income is a strong

predictor for violent conflict – as argued by (Collier, Hoeffler, and Rohner, 2008) – which in turn

decreases income, then a simple comparison-in-means of post-conflict income across conflict

and non-conflict localities may simply reflect pre-war differences in income that might have

persisted in the absence of war, and cannot be attributed to war alone.

In the case of Bosnia, schooling completion rates for the affected cohorts are lower in munic-

ipalities that endured the war at a higher intensity, but the same differences also exist for the un-

affected cohorts, suggesting that differences in schooling attainment were already present be-

fore the war (Table 1.2). In fact, when I run fitted polynomial regressions of the mean schooling

completion by cohort and war casualty rate, I find that war intensity does not necessarily de-

crease the schooling completion of affected cohorts, relative to unaffected cohorts (Figure 1.1).

Thus, to be sure that war effects are correctly identified, I adopt the difference-in-differences

approach to account for any unobserved pre-war differences across municipalities. In particu-

lar, I exploit the variation in war intensity and the birth cohorts of children – which determines

whether they were in primary and secondary schools during the war – to identify war effects

from the difference in schooling attainment between affected and unaffected cohorts from high

casualty municipalities, relative to those from low casualty municipalities. The econometric

specification is as follows:

SCHOOLijkc = β(WARj × AFFECTEDc) + αj + γk + δc + ε ijkc (1.1)

where SCHOOLijkc refers to the measure of schooling attainment for individual i of birth cohort

c, who resides in municipality j (and k) before (and after) the war; WARj is an indicator for the

high casualty municipalities; AFFECTEDc is an indicator for the affected cohorts; αj and γk

20

are pre-war and post-war municipality fixed effects; δc are the birth cohort fixed effects; and

ε ijkc represents a vector of unobserved individual characteristics. Let superscripts denote the

values for the indicators WARj and AFFECTEDc respectively, and consider the average effects

of the war as follows:

[E(SCHOOL1,1ijkc)− E(SCHOOL1,0

ijkc)]− [E(SCHOOL0,1ijkc)− E(SCHOOL0,0

ijkc)]

=β + [γ1,1k − γ0,1

k ] +{[E(ε1,1

ijkc)− E(ε1,0ijkc)]− [E(ε0,1

ijkc)− E(ε0,0ijkc)]

}(1.2)

Equation (1.2) clearly demonstrates that, by using a difference-in-differences specification,

biases due to (i) pre-war differences across high and low casualty municipalities and (ii) perma-

nent differences between affected and unaffected cohorts, are eliminated.13 However, in order

to interpret β as average effects of the war, I also need to rule out two other potential biases.

The first bias can be attributed to post-war municipality differences γ1,1k − γ0,1

k , which could be

non-zero if the affected cohorts from high and casualty municipalities face do not have equal

access to schooling, should they choose to resume schooling after the war. The second bias,

as shown in the last term in equation (1.2), is due to unobserved individual traits – ability, for

example – that may be systematically different across high and low casualty municipalities. I

will deal with both of these concerns in the next section.

13It is easy to show that pre-war municipality fixed effects αj and birth cohort fixed effects δc are eliminated bytaking difference-in-differences of the expected schooling attainment. In addition, the post-war municipality fixedeffects for unaffected cohorts, γ1,0

k and γ0,0k , are assumed to be zero because the unaffected cohorts, by definition,

would have completed schooling before the start of the war.

21

Figure 1.1 ‐ Fitted Regression of Schooling Attainment by Cohort and War Casualty Rate

1g

Secondary Schooling by Cohort and War Casualty Rate

0.2

.4.6

.81

Prop

ortio

n co

mpl

eted

prim

ary

scho

olin

g

0 10 20 30 40 50 60Age in 1992

Fitted polynomial regression for high (low) casualty municipalities shown in bold (hollow).

Primary Schooling by Cohort and War Casualty Rate

 33

0.2

.4.6

.81

Pro

porti

on c

ompl

eted

sec

onda

ry s

choo

ling

0 10 20 30 40 50 60Age in 1992

Fitted polynomial regression for high (low) casualty municipalities shown in bold (hollow).

Secondary Schooling by Cohort and War Casualty Rate

0.2

.4.6

.81

Prop

ortio

n co

mpl

eted

prim

ary

scho

olin

g

0 10 20 30 40 50 60Age in 1992

Fitted polynomial regression for high (low) casualty municipalities shown in bold (hollow).

Primary Schooling by Cohort and War Casualty Rate

 33

22

1.5 Empirical Analysis

Following the discussion above, I run difference-in-differences regressions by using two mea-

sures of schooling attainment – a dummy for having completed primary school, and another

for having completed secondary school – to identify war effects for each level of schooling

(Table 1.3). I use the specification as shown in equation (1.1), with one modification – that

the dummy for high casualty municipalities WARj be replaced by the actual casualty rate of

each municipality, so as to exploit the full variation in war casualty data. Where specified,

individual-level controls include sex, ethnicity, and a dummy for parental secondary schooling

completion.14 In all cases, the standard errors are clustered at the pre-war municipality level to

allow for any unobserved correlation within municipalities.

For both measures of schooling attainment, I run the difference-in-differences regression

without controls [columns (1) and (4)], with individual controls [columns (2) and (5)], and

finally with individual controls, cohort and municipality fixed effects [columns (3) and (6)].

The last specification – analogous to the one presented in equation (1.1) – reveals that war

effects are only evident for the completion of secondary schooling. In fact, according to the

results in column (6), the β coefficient is -1.580 and is statistically significant at the 1 percent

level. This implies that a one standard deviation increase in war casualty rate – the equivalent

of around 21 deaths per thousand – reduces an affected individual’s likelihood of completing

secondary schooling by 3 percentage points. In other words, compared to peers who reside in

municipalities with a lower war casualty rate, an affected individual is less likely to complete

secondary school.

14To ensure that these individual controls do not bias my estimates of war effects, I run a regression of the dummyfor the affected cohorts on the vector of individual controls, and find that they are uncorrelated, conditional on warcasualty rate.

23

Table 1.3 ‐ Difference‐in‐Difference Regressions

Dep

ende

nt Variable:

DID (1

)DID (2

)DID (3

)DID (4

)DID (5

)DID (6

)

Affe

cted coh

orts:

          Aged 07‐15 in 1992‐95

0.117***

0.025

0.862***

[0.023]

[0.043]

[0.055]

          Aged 16‐19 in 1992‐95

0.208***

0.190***

0.366***

[0.018]

[0.042]

[0.061]

Mun

icipality w

ar casua

lty ra

te‐0.479

‐0.290

‐0.143

0.252

[0.366]

[0.259]

[0.396]

[0.282]

Coh

ort d

ummy x War casua

lty ra

te0.340

0.387

0.275

‐1.242**

‐1.652***

‐1.580***

[0.374]

[0.310]

[0.269]

[0.570]

[0.538]

[0.480]

Individu

al con

trols

No

Yes

Yes

No

Yes

Yes

Coh

ort & m

unicipality fixed effects

No

No

Yes

No

No

Yes

Mean of dep

ende

nt variable

0.869

0.869

0.869

0.598

0.598

0.598

Num

ber o

f observatio

ns4995

4995

4995

4256

4256

4256

R2

0.02

0.22

0.27

0.02

0.37

0.42

Prim

ary scho

oling completion

Second

ary scho

oling completion

Clustered

stan

dard

errors

inpa

rentheses.*s

ignifican

tat1

0%;**s

ignifican

tat5

%;***sign

ificant

at1%

.Ind

ividua

lcon

trolsinclude

sex,ethn

icity

and

parental

second

ary

scho

oling

completion.

Scho

oling

completion

data

istaken

from

the2001

LSMS.

Thesamplein

columns

(1)‐(3)

contains

individu

alsaged

15an

dabov

ein

2001.T

hesamplein

columns

(4)‐(6)

contains

individu

alsaged

22an

dabov

ein

2001.T

hemeanan

dstan

dard

deviation of th

e war casua

lty ra

te are 0.017 and 0.022 [colum

ns (1

)‐(3)], an

d 0.017 an

d 0.021 [colum

ns (4

)‐(6)].

 30

24

Combining the evidence from Figure 1.1 and Tables 1.2 and 1.3, we can see that the com-

pletion of primary schooling was virtually impervious to the Bosnian War, while secondary

schooling was adversely affected. A couple of explanations emerge from the previous discus-

sion in Section 1.2.1. Firstly, the impact of the war may have been muted by the organization of

war schools; however, they may have been successful at providing primary schooling but not

secondary schooling, because the former has a standardized curriculum that is easier to man-

age (Berman, 2001). Secondly, the military draft may have pulled secondary students away

from school, while primary students were probably too young to become voluntary combat-

ants. That said, we have not ruled out other plausible mechanisms, such as the destruction of

school infrastructure, although it is difficult to imagine how they could have affected secondary

but not primary schooling.

Following the discussion in Section 1.4, I need to find support for the assumption that the

affected cohorts, regardless of municipality, have equal access to schooling, should they choose

to go back to school after the war. Firstly, I look at two supply-side indicators – schools and

teachers per capita, as defined in Section 1.3.3 – and compare them for municipalities with high

and low casualty rates. From Figure 1.2, we can see that differences in these indicators appear to

have increased after the war; however, these differences are not statistically significant, which

suggests that schooling attainments across municipalities are unlikely to be driven by post-war

supply-side factors.

Furthermore, I check whether refugees, who, as a result of moving from high to low casu-

alty municipalities, are systematically selecting destinations with better (or poorer) schooling

facilities, which may cause my estimates to suffer from a positive (or negative) bias. To this

end, I run a difference-in-differences regression by replacing the schooling attainment measure

with a migration dummy variable that denotes whether an individual had migrated during the

war [column(1), Table 1.4]. The β coefficient is statistically insignificant, which suggests that

affected cohorts in high casualty municipalities are no more likely to move during the war.

25

Figure 1.2 ‐ Pre‐war and Post‐war Statistics on Schools and Teachers

800s)

Statistics on Teachers by War Casualty Rate

2.5

33.

5M

ean

num

ber o

f sch

ools

per

cap

ita ('

000s

)

1988 1989 1996 1997Year

The solid (dash) line represents the mean number of schools per capita for municipalities in the top(bottom) quantile of war casualty rates.

Statistics on Schools by War Casualty Rate

 34

2022

2426

28M

ean

num

ber o

f tea

cher

s pe

r cap

ita ('

000s

)

1988 1989 1996 1997Year

The solid (dash) line represents the mean number of teachers per capita for municipalities in the top(bottom) quantile of war casualty rates.

Statistics on Teachers by War Casualty Rate

2.5

33.

5M

ean

num

ber o

f sch

ools

per

cap

ita ('

000s

)

1988 1989 1996 1997Year

The solid (dash) line represents the mean number of schools per capita for municipalities in the top(bottom) quantile of war casualty rates.

Statistics on Schools by War Casualty Rate

 34

26

Table 1.4 ‐ Robustness Checks

DID (1

)OLS (2

)DID (3

)DID (4

)DID (5

)DID (6

)DID (7

)DID (8

)DID (9

)

Affe

cted coh

orts:

          Aged 16‐19 in 1992‐95

0.018

0.475***

0.503***

0.573***

0.354***

0.348***

[0.018]

[0.063]

[0.087]

[0.054]

[0.064]

[0.065]

          Aged 16‐18 in 1992‐95

‐0.009

[0.054]

          Aged 16‐20 in 1992‐95

0.457***

[0.034]

Coh

ort d

ummy x War casua

lty ra

te0.134

‐2.056***

‐0.909

‐1.577***

‐1.411***

‐1.821***

[0.383]

[0.703]

[0.614]

[0.458]

[0.424]

[0.490]

Coh

ort d

ummy x Pe

rcentage of d

amaged hou

sing

‐0.044

[0.036]

Coh

ort d

ummy x Out‐m

igrants pe

r cap

ita‐0.382

[0.665]

Parental secon

dary schoo

ling completion

0.000

[0.000]

Percentage of rep

aired ho

using

0.000

[0.000]

Individu

al con

trols

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Coh

ort & m

unicipality fixed effects

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Mean of dep

ende

nt variable

0.525

0.169

0.702

0.495

0.605

0.594

0.598

0.598

0.598

Num

ber o

f observatio

ns4256

4256

2129

2127

4365

4172

4256

4256

4256

R2

0.96

0.27

0.67

0.34

0.42

0.43

0.41

0.42

0.42

Colum

n (1): Diff‐in‐diff re

gression w

ith m

igratio

n du

mmy being the de

pend

ent v

ariable.

Colum

n (2): OLS re

gression w

ith w

ar casua

lty ra

te being th

e de

pend

ent v

ariable.

Colum

ns (3

)‐(4): D

iff‐in‐diff re

gression w

ith m

ale an

d female sample respectiv

ely.

Colum

ns (5

)‐(6): D

iff‐in‐diff re

gression w

ith ‐1

/+1 year of the affe

cted coh

orts re

spectiv

ely. 

Colum

n (7): Diff‐in‐diff re

gression w

ith percentage of re

paired hou

sing re

placing po

st‐w

ar m

unicipality fixed effects (pre‐w

ar m

unicipality fixed effects remain).

Colum

ns (8

)‐(9): D

iff‐in‐diff re

gression w

ith m

easure of w

ar in

tensity being percentage of dam

aged hou

sing and out‐m

igrants pe

r cap

ita re

spectiv

ely.

Clustered

stan

dard

errors

inpa

rentheses.

*sign

ificant

at10%;**

sign

ificant

at5%

;***sign

ificant

at1%

.Individu

alcontrols

includ

esex,

ethn

icity

andpa

rental

second

aryscho

oling

completion.

Scho

olingcompletionda

taistakenfrom

the2001

LSMS.

Thesamplecontains

individu

alsaged

22an

dabov

ein

2001,excep

tfor

column(5),which

contains

individu

alsaged

21an

dabov

ein

2001,and

column(6),which

contains

individu

alsaged

23an

dabov

ein

2001.D

ataon

damaged

andrepa

ired

housingun

its,and

thenu

mberof

out‐m

igrantsaretakenfrom

the

UNHCR.

Mon

thly

earnings

isde

nominated

intheBo

snianKon

vertible

Marka

(KM),where

1KM

isap

proxim

ately75

UScents.Th

emeanan

dstan

dard

deviationof

thewar

casualty

rate

are 0.017 an

d 0.021 [colum

ns (1

), (5), (6) a

nd (7

)], 0.016 and 0.017 [colum

n (3)], and 0.018 and 0.023 [colum

n (4)].

Second

ary scho

oling completion

Dep

ende

nt Variable:

Migratio

n du

mmy

War casua

lty 

rate

 31

27

Another source of bias is the possible correlation between unobserved individual-level

traits and war casualty rate. For instance, if high casualty municipalities tend to have a greater

proportion of high ability individuals, who are more likely to complete schooling, then my

estimates may be biased. That said, this is problematic insofar as the systematic differences

in the unobserved trait is not a direct consequence of unobserved municipal differences (that

are already taken care of by the difference-in-differences specification). Nevertheless, I run a

regression of war casualty rate on the dummy for parental secondary schooling completion,

controlling for other individual characteristics, and cohort and municipality fixed effects, and

find that parental secondary schooling completion is uncorrelated with war casualty rate [col-

umn(2), Table 1.4]. This implies that selection by ability is unlikely, to the extent that parental

schooling is a reasonable proxy for unobserved ability.

1.5.1 Robustness Checks

The preceding section may have given us a glimpse into the effects of war on schooling attain-

ment, but more needs to be done in terms of verifying the robustness of my results as well as in

uncovering the exact mechanisms that are important. For the rest of this section, I consider the

sub-sample of individuals who would have been in secondary school, as this is the group for

which we observe evidence of war effects. Results are shown in columns (3)–(9) of Table 1.4.

First of all, I check to see if the war effects on secondary schooling are different by gender.

Column (3) shows that the effects are strongly driven by males, whereas column (4) reveals

no significant effect for females. Moreover, the β coefficient increases (substantially) by 30

percent when the sample is limited to males. This finding is consistent with both of the follow-

ing: (i) budget-constrained parents substitute away from expenditure on their sons’ (but not

their daughters’) education towards the consumption of other goods, and (ii) youth soldiering,

which affects males but not females, is a key driver of lower secondary schooling attainment.

Next, as the construction of cohort dummies are based on the average student’s schooling

age, I also conduct a sensitivity test by altering the number of cohorts that is included in the

28

dummy. From columns (5) and (6) – which show the results by adding and subtracting one

cohort respectively – we can see that the β coefficients remain statistically significant, and the

magnitudes differ only slightly, from the initial -1.580 to between -1.411 and -1.577. This sug-

gests that the war effects are precisely estimated even when we account for the fact that some

students may have taken more (or less) time to finish their secondary schooling.

For the purpose of attributing the decrease in schooling attainment to war, it is also im-

portant to make a clear distinction between immediate and long-term effects (as discussed in

Section 1.2.1). While post-war municipality fixed effects already account for unobserved mu-

nicipal factors that may influence whether the affected cohorts resume (and complete) school-

ing, I perform three additional tests to examine possible long-term effects.15 First, I investigate

possible adverse effects of post-war ethnic segregation in schools, by repeating the difference-

in-differences regressions with an additional indicator for whether the individual belongs to

the ethnic minority. I find that the augmentation has virtually no impact on my estimates of war

effects, and that the ethnic minority indicator is uncorrelated with schooling completion. Next,

I take the issue of differential post-war reconstruction seriously by repeating the difference-

in-differences regressions, and replace post-war municipality fixed effects with a variable that

measures each municipality’s percentage of repaired housing units. From column (7), we can

see that the magnitude and statistical significance of the β coefficient remains robust, and more

importantly, repairs do not seem to affect schooling attainment; this is consistent with the con-

jecture that affected cohorts do not resume schooling. Finally, suppose that affected cohorts do

resume schooling, then we should expect the war effects to be stronger for younger individuals

in the affected cohorts, because they are further away from completion, and thus, less likely to

resume schooling. However, when I decompose the dummy for affected cohorts into several

cohort dummies and examine the effects by cohort, I find that the effects are not only negative

for the younger cohorts, but also for the oldest cohort (Figure 1.3). Overall, while I cannot dis-

15Apart from these ancillary results, I also run difference-in-differences regressions with the logarithm of reportedmonthly earnings being the dependent variable, and find no significant effects. This suggests that returns to sec-ondary education may be insignificant, which corroborates my finding that the affected cohorts tend not to resumeschooling after the war.

29

count the possibility that long-term effects exist, it appears that my estimates are most likely

picking up immediate, rather than long-term effects.

Figure 1.3 ‐ War Effects by Cohort-5

05

1015

Coe

ff. o

f Age

in 2

001

X C

asua

lty R

ate

22 23 24 25 26 27 28Age in 2001 (Affected cohorts only)

Dotted lines represent the 95% confidence interval of the coefficients.

War Effects (on Secondary Schooling) by Cohort

 35 35

A key mechanism that may explain the war effects is the reduction in accessibility to educa-

tion. To investigate this, I repeat the difference-in-differences regressions by replacing casualty

rates with (i) the percentage of damaged housing units and (ii) the number of out-migrants per

capita for each municipality. Columns (8) and (9) show that the β coefficients are negative but

imprecisely estimated, which suggest that neither of these determinants of accessibility mat-

ter.16 In fact, the magnitudes of these coefficients imply that the effects of housing damage

and out-migration – even if they are statistically significant – are relatively small. For exam-

ple, a one standard deviation increase in the percentage of damaged housing may only lower

secondary schooling attainment by 1 percent (compared to 3 percent when I use war casualty

rate in a similar specification). These results are particularly helpful for ruling out a couple16These conclusions are similar to the findings of Merrouche (2006), Shemyakina (2007) and Akresh and

de Walque (2008), who find that lower quality of school infrastructure is not an important mechanism throughwhich civil war affects schooling outcomes. That said, in the case of Germany during World War II, Akbulut-Yuksel(2008) concludes that the destruction of schools and the absence of teachers appear to be an important channel.

30

of scenarios. Firstly, the out-migration of teachers, that might have contributed to the relative

success of primary over secondary war schools, is improbable now that I find no significant

out-migration effect. Also, as the secondary schooling attainment of affected cohorts is unre-

sponsive to the extent of housing damage, the destruction of school infrastructure also appears

to be unimportant.

The evidence thus far suggests that the results are driven by the male sample, and especially

among the older affected cohorts. One possible explanation may be that youth soldiering –

defined as front line duties that may have prevented students from attending war schools –

prevented the older male students from attending school. Given that I do not have soldiering

data, I investigate this possibility by examining the physical and emotional health of affected

cohorts; for example, those who fought in the war may be less healthy than those who did

not (Blattman and Annan, 2007). To this end, I use the sample of affected cohorts and run

difference-in-differences regressions by replacing the schooling attainment measures with a set

of health outcomes. The objective here is to compare the health of the affected cohorts by war

intensity and by age group (corresponding to primary and secondary schooling).17

In column (1) of Table 1.5, I use a dummy for subjective health – which equals one if the in-

dividual reports her health as being “fair” or better – and find that the β coefficient is negative

but statistically insignificant. Then, in columns (2), (4) and (5), we can see that the β coefficients

are positive but imprecisely estimated, which means that war intensity neither impact the fre-

quency of recalling painful events from the war nor the likelihood of being physically disabled

(due to the war or not). Nonetheless, the signs of these coefficients suggest that the affected

cohorts in the secondary schooling age group may be less healthy than their primary schooling

counterparts due to the war. In fact, from column (3), we can see that older affected cohorts

are more likely to suffer from depression, by using a depression indicator that is derived from

the Hopkins Symptom Checklist. The β coefficient of 0.370 implies that a one standard devi-

ation increase in war casualty rate increases an affected individual’s probability of emotional

17In this case, the unaffected cohorts are excluded because they may also endure health effects due to the war,and thus do not constitute a natural control group. In fact, affected and unaffected cohorts, by virtue of differencein age, may be subjected to different mental and physical health shocks.

31

illness by around 1 percentage point. The fact that war affects the emotional health of cohorts

aged 16-19 (in 1992-95) more than it does the younger cohorts, suggests that there is something

age-specific about how depression is related to war, which is consistent with youth soldiering

being an important driver of the war effects. Overall, while I do not have data on soldering, the

indirect evidence suggests that youth soldiering may be helpful in explaining the war effects.

32

Tab

le 1

.5 -

Dif

fere

nce

-in

-Dif

fere

nce

Reg

ress

ion

s (H

ealt

h O

utc

om

es)

Dep

end

ent

Var

iab

le:

DID

(1)

DID

(2)

DID

(3)

DID

(4)

DID

(5)

Old

er a

ffec

ted

co

ho

rts:

A

ged

16-

19 i

n 1

992-

95-0

.004

0.07

0-0

.013

0.02

90.

013

[0.0

29]

[0.0

49]

[0.0

19]

[0.0

28]

[0.0

14]

Co

ho

rt d

um

my

x W

ar c

asu

alty

rat

e-0

.594

0.21

10.

370*

*0.

051

0.07

2

[0.4

30]

[1.1

39]

[0.1

84]

[0.1

45]

[0.0

80]

Ind

ivid

ual

co

ntr

ols

Yes

Yes

Yes

Yes

Yes

Co

ho

rt &

mu

nic

ipal

ity

fix

ed e

ffec

tsY

esY

esY

esY

esY

es

Mea

n o

f d

epen

den

t v

aria

ble

0.94

90.

454

0.06

20.

012

0.00

5

Nu

mb

er o

f o

bse

rvat

ion

s10

6510

6510

6510

6510

65

R2

0.11

0.26

0.22

0.11

0.04

Clu

ster

edst

and

ard

erro

rsin

par

enth

eses

.*

sig

nif

ican

tat

10%

;**

sig

nif

ican

tat

5%;

***

sig

nif

ican

tat

1%.

Ind

ivid

ual

con

tro

lsin

clu

de

sex

,

eth

nic

ity

and

par

enta

lse

con

dar

ysc

ho

oli

ng

com

ple

tio

n.

Su

bje

ctiv

eh

ealt

his

ad

um

my

=1

ifre

po

rted

hea

lth

isn

ole

ssth

an"f

air

",b

ased

on

hea

lth

inth

ela

st12

mo

nth

s,re

lati

ve

top

eop

leo

fth

esa

me

age;

the

actu

alre

spo

nse

sin

the

LS

MS

are:

(1)

ver

yp

oo

r,(2

)p

oo

r,(3

)fa

ir,

(4)

go

od

,

(5)

exce

llen

t.W

artr

aum

ais

ad

um

my

that

refe

rsto

the

reca

llo

fw

artr

aum

ain

the

pre

vio

us

wee

k.

Dep

ress

ion

isa

du

mm

yth

atta

kes

the

val

ue

1w

hen

anin

div

idu

alis

Ho

pk

ins

Sy

mp

tom

Ch

eck

list

(HS

CL

)p

osi

tiv

e,w

ith

ad

epre

ssio

nsc

ore

of

1.75

or

hig

her

(ou

to

fa

po

ssib

le4)

,

wh

ere

ah

igh

ersc

ore

corr

esp

on

ds

toa

gre

ater

lik

elih

oo

do

fsi

gn

ific

ant

emo

tio

nal

illn

ess;

the

HS

CL

isa

sym

pto

min

ven

tory

wh

ich

mea

sure

s

sym

pto

ms

of

dep

ress

ion

.T

his

sam

ple

con

tain

sin

div

idu

als

aged

28an

db

elo

win

2001

.P

hy

sica

ld

isab

ilit

y(d

ue

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32

33

1.6 Conclusions

In this chapter, I explain the detrimental effects of the Bosnian War on the affected cohorts that

were in the process of completing their primary and secondary schooling during the war. I

attempt to estimate war effects by using a unique data set that contains information on war ca-

sualties at the intrastate level. By exploiting the variation in war intensity and the birth cohorts

of children – which determines whether they were in primary and secondary schools during

the war – I account for the unobserved pre-war differences across municipalities, to correctly

identify war effects. I find that war intensity significantly reduces the schooling attainment

of affected cohorts, and in particular, a one standard deviation increase in war casualty rate –

the equivalent of 21 deaths per thousand – reduces an affected individual’s likelihood of com-

pleting secondary schooling by 3 percentage points. However, I find no noticeable effects on

primary schooling, which could be the result of the successful organization of war schools at

the primary level. Indirect evidence also suggests that youth soldiering may have prevented

students from attending school.

While the existing economics and political science literature on examining civil conflicts

is vast, until recently, few empirical works have examined the microeconomic impact of civil

wars. Among those, none has made use of a methodologically-sound war casualty data set to

estimate war effects. To my knowledge, this study is the first to directly estimate the effects

of a civil war by using intrastate casualty rates, and will contribute to the general literature on

quantifying the welfare costs of civil wars. In addition, this study registers an attempt to infer

the mechanisms through which civil wars affect individuals’ welfare, and is the one of the first

in the economics literature to present indirect evidence of youth soldiering effects on schooling

attainment and emotional health.

Given that civil wars lower schooling attainment, which may worsen individuals’ longer

term welfare and impede the economic growth of their countries, the results of this study not

only provide policy-makers with important insights on the consequences of conflict, but also

reaffirms the importance of aid spending on the post-war rebuilding of the education sector.

34

While the results of this study are both important and interesting, it is unfortunate that there is

no available data on soldiering and attendance in war schools, which could be used to directly

ascertain the importance of youth soldiering as a key mechanism. Should these data become

available in the future, it will be fruitful to revisit the analysis of possible mechanisms, and to

verify the reach and success of war schools.

Chapter 2

Together or Separate? Post-Conflict Partition, Ethnic

Homogenization, and the Provision of Public Schooling

2.1 Introduction

The partitioning of political jurisdictions is becoming an increasingly common component of

agreements to end ethnic conflict. Of the approximately 80 episodes of ethnic civil wars since

the end of World War II, at least 20 were resolved by separating warring ethnic groups into

partitioned jurisdictions, with 14 such partitions being implemented in the last two decades.1

While partitions have proved to be effective in achieving immediate peace, their effect on post-

conflict recovery remains unclear. On one hand, partitions induce ethnic homogenization,

which may increase the provision of public goods due to convergent preferences over the type

of public goods to provide (Cutler, Elmendorf, and Zeckhauser, 1993; Temple, 1996; Poterba,

1997; Goldin and Katz, 1999; Alesina, Baqir, and Easterly, 1999). On the other hand, partitions

do not resolve the underlying ethnic rivalry or prevent future conflict because it precludes in-

terethnic cooperation (Sambanis, 2000) and, if homogenization is incomplete, ethnic minorities

may face significant repression (Kaufmann, 1998; Bose, 2002).

This study examines the effects of partitioning political jurisdictions on post-conflict re-

covery, by analyzing its impact on the provision of public goods. I consider the Inter-Entity

Boundary Line (IEBL) that ended the 1992–1995 Bosnian War and divided Bosnia and Herze-

govina (hereafter, Bosnia) into two separately-administered entities. Although the IEBL was

drawn to approximate the frontlines of the war, it did not always follow pre-war municipal

boundaries and, as a result, created several partitioned municipalities. The variation in the

1According to Sambanis (2000), there were 80 episodes of ethnic civil wars from 1945–2000, of which 18 involvedpartitions. In addition, two other partitions were implemented since 2000 to end ethnic conflicts in East Timor andKosovo.

35

36

incidence of municipal partition among municipalities thus forms the basis for the empirical

identification of partition effects. With regards to public goods, I focus on public schooling

for two reasons. Firstly, as human capital accumulation is an important determinant of future

economic performance, it informs us about the effects on post-war recovery in the long run.

Moreover, as public schooling in Bosnia is not only ethnically oriented but also a significant

municipal responsibility, the nature of schooling provision may generate distributional impli-

cations.

The questions I address are the following. First, do we observe a greater provision of public

schooling in partitioned municipalities and, if so, why? Second, what are the distributional con-

sequences of partition-induced differential provision of public schooling? To empirically iden-

tify the effects of the partition on the provision of public schooling, I exploit the fact that while

the IEBL was determined by war-related factors, the creation of partitioned municipalities was

not. This allows me to adopt a difference-in-differences strategy, comparing municipality-level

outcomes across partitioned and unpartitioned municipalities before and after the war. My

results suggest that the partition induced ethnic homogenization, and that partitioned munic-

ipalities, on average, provide 58 percent more primary schools and 37 percent more teachers

(per capita) than unpartitioned ones, controlling for time-invariant municipal differences and

aggregate shocks across municipalities.

Given that partitioned municipalities provide more public schooling, do children who re-

side in them actually benefit? By using a nationally-representative sample of individuals, I

find that children who reside in partitioned municipalities are more likely to attend and com-

plete school; however, if they belong to the ethnic minority, then this advantage is completely

eroded. These results suggest that the differential provision of public schooling may have ben-

efitted the ethnic majority children but not the ethnic minority ones. Moreover, they reaffirm

the finding that effects are working through ethnic homogenization.

In addition, I find evidence which suggests that partitioned municipalities provide more

public schooling because ethnically homogeneous communities find it easier to attain ethni-

37

cally oriented public goods – in this case, ethnically oriented schools – through political means.

While this is consistent with the established relationship between diversity in preferences and

public goods provision (Cutler, Elmendorf, and Zeckhauser, 1993; Temple, 1996; Poterba, 1997;

Goldin and Katz, 1999; Alesina, Baqir, and Easterly, 1999), I show that the Bosnian case is

unique to the extent that it is also associated with ethnic politics.2 That said, I cannot rule

out mechanical explanations that emerge due to unobserved incentives for partitioned munic-

ipalities to build more schools.

In summary, the contribution of this study is twofold. Firstly, it is one of the first papers to

empirically establish the consequences of residing in partitioned jurisdictions in a post-conflict

society; in particular, it provides estimates of level and distribution effects. Secondly, it explores

the role of ethnic homogenization in the relationship between partition and public goods pro-

vision. The findings of this study will not only improve our understanding of how partitions

affect the lives of individuals after the conflict, but also of whether and how altering political

boundaries may influence economic recovery in conflict regions.

The rest of this chapter is organized as follows. Section 2.2 constitutes a brief discussion on

the Bosnian War and the Dayton Peace Accords, as well as the provision of public schooling.

A theoretical framework is laid out in Section 2.3 to help guide subsequent empirical analyses.

Sections 2.4 and 2.5 contain descriptions of the data and the empirical methodology respec-

tively. Section 2.6 provides the main empirical results, while robustness checks are discussed

in Section 2.7. Section 2.8 concludes.

2.2 Background

2.2.1 Bosnian War and the Dayton Peace Accords

Before the war, Bosnia was the most ethnically diverse among the ex-Yugoslav republics, com-

prising mainly Bosniaks (44 percent), Serbs (31 percent) and Croats (17 percent). Moreover,

2At the cross-country level, Easterly and Levine (1997) present evidence in favor of a negative relationshipbetween ethnic diversity, public policies and economic growth. Beyond preference-based theories, Miguel andGugerty (2005) argue that ethnically diverse communities find it harder to impose social sanctions, resulting incollective action failures.

38

ethnic identity was strengthened by religious affiliation, as the majority of Bosniaks are Mus-

lims, and almost all Serbs and Croats are Orthodox Christians and Roman Catholics respec-

tively.3 In general, interethnic relations in Bosnia were amicable under the Yugoslav regime,

due partly to a strict policy of brotherhood and unity that was enforced by suppressing ethno-

nationalism among the various narods (“nationalities” or “ethnicities”). To get a sense of the

degree of ethnic integration before the war, I present a municipality map of pre-war Bosnia

in Figure 2.1, where municipalities with a numerical ethnic majority (more than 50 percent)

are shaded. As we can see, approximately one-third of the municipalities had no dominant

ethnicity (unshaded), which hints at the fact that Bosnia was not only ethnically diverse but,

to some extent, ethnically integrated. However, following the successful secession of Slovenia

and Croatia from the Socialist Federal Republic of Yugoslavia in 1991, Bosnian Serbs began de-

manding annexation to Serbia while their Bosniak and Croat counterparts voted in favor of the

independence of Bosnia. These events ultimately led to the onset of the Bosnian War in April

1992 (Kalyvas and Sambanis, 2005).

The Yugoslav People’s Army and the Bosnian Serb forces – led by Radovan Karadžic, the

leader of the Serbian Democratic Party – initiated the first waves of combat in eastern and

northwestern Bosnia, to control Bosnian territories that had a Serb majority. Ethnic violence

quickly spread to many parts of the country, including the capital, Sarajevo, which was subse-

quently besieged by the Serbs.4 Throughout the course of the war, the international community

sent thousands of peacekeeping troops and brokered several peace plans that ultimately failed.

In August 1995, widespread massacres in Sarajevo and Srebrenica finally prompted the North

Atlantic Treaty Organization to conduct air strikes against the Serb strongholds, which even-

tually led to the peace talks. According to the Research and Documentation Center (Sarajevo)

and the Bosnian Ministry for Human Rights and Refugees, approximately 96,000 civilians and

soldiers were killed during the war, and over 2.2 million people were displaced from their

homes, half of whom sought refugee protection outside Bosnia.

3These ethnic composition figures were collected by the Socialist Federal Republic of Yugoslavia for the 1991census.

4For a detailed exposition of the key events of the war, refer to Vulliamy (1994) and Burg and Shoup (1999).

39

Fig

ure

2.1

- M

un

icip

alit

ies

by

Eth

nic

Maj

ori

ty (

Pre

-War

) Cro

atia

Ser

bia

Mo

nte

neg

ro

No

te: M

un

icip

alit

ies

wit

h a

nu

mer

ical

eth

nic

maj

ori

ty (

mo

re t

han

50

per

cen

t) a

re s

had

ed; a

Ser

b m

ajo

rity

is

shad

ed i

n d

ark

gre

y, a

Cro

at m

ajo

rity

is

shad

ed i

n m

ediu

m g

ray

, an

d a

Bo

snia

k m

ajo

rity

is

shad

ed i

n l

igh

t g

rey

.

40

Negotiations at Dayton began slowly as the warring parties maintained the same disagree-

ments that had characterized earlier peace negotiations.5 The Bosniaks and the Croats dis-

agreed over how power was to be allocated in Bosnia, while the Serbs and the Croats continued

to tussle over the future of Eastern Slavonia – a Serb-controlled region of Croatia. Without a

doubt, however, it was agreement on a map designating the de facto partition that proved the

most difficult to achieve (Burg and Shoup, 1999). Prior to the meeting in Dayton, the warring

parties had already agreed to a partitioning line – known formally as the Inter-Entity Bound-

ary Line (IEBL) – that would divide Bosnia into two entities: the Federation of Bosnia and

Herzegovina (FBiH) for the Bosniak-Croat alliance, and Republika Srpska (RS) for the Serbs. In

addition, the consensus was to implement the partition such that 51 percent of Bosnia would

be allocated to the Bosniak-Croat alliance, and 49 percent to the Serbs, so as to reflect the actual

territorial shares on the ground at the time. Nevertheless, they remained divided over how

exactly the line should be drawn, as the status of several key territories – the Posavina corridor

near Brcko that connects eastern and western Serb areas, the last remaining Bosniak enclave of

Goražde, and Sarajevo – were still in contention.

The American negotiators proposed a map that approximated the real-time frontlines of

the war, and began persuading each party to compromise on one dispute at a time, revising

the map as and when necessary. The deadlock eventually broke as Miloševic agreed to a land

corridor that would connect Goražde to Sarajevo; in return, the Serbs received an egg-shaped

territory – comprising parts of Drvar, Jajce, Kljuc, Kupres, Mrkonjic Grad, Petrovac and Šipovo

– in western Bosnia, and Brcko was to remain neutral and be subjected to international arbi-

tration (Chollet, 2005). The successful conclusion of the peace talks led the warring parties to

sign the Dayton Peace Accords which, apart from ending the war, laid down a blueprint for

transforming Bosnia into a peaceful democracy.

5Negotiations were led by the United States Secretary of State, Warren Christopher, and negotiator, RichardHolbrooke. The leaders of the three warring parties – Alija Izetbegovic (Bosniak), Franjo Tudman (Croat), andSlobodan Miloševic (Serb) were present, as well as a so-called Contact Group comprising representatives from theUnited Kingdom, France, Germany, Italy and Russia.

41

2.2.2 Municipal Partition

The division of Bosnia is most apparent when one looks at an ethnic map of Bosnia immedi-

ately after the accords (see Figure 2.2). Evidently, all RS municipalities were dominated by the

Serbs, while FBiH municipalities were dominated by either the Bosniaks or the Croats, which

meant that ethnic integration was eradicated. In addition, as the IEBL did not always follow

pre-war municipal boundaries, the accords led to another significant legacy – the implementa-

tion of municipal partition. In particular, 28 of the 109 pre-war municipalities were partitioned,

creating 58 partitioned municipalities. These partitioned municipalities not only became geo-

graphically smaller, but also more ethnically homogeneous as they became part of the FBiH (30

municipalities) or the RS (28 municipalities). Furthermore, as the IEBL was drawn to approx-

imate the frontlines of the war prior to the meeting at Dayton, partitioned municipalities are

also frontline municipalities.

Figure 2.3 provides a geographical overview of the Bosnian municipalities at the time of

the partition. The dark line that runs through the country denotes the IEBL which separates

the RS municipalities (shaded) from their FBiH counterparts (unshaded). For empirical pur-

poses, I will use the post-war municipal boundaries to define municipalities, unless otherwise

specified. In other words, partitioned municipalities are analyzed at the post-war municipal

level; unpartitioned municipalities are unaffected by the boundary line, so whether they are

analyzed at the pre- or post-war municipal level is irrelevant. By virtue of its neutrality, Brcko

(crossed) will be excluded from my analyses. To get a better idea of how partitioned munici-

palities were created, I focus on the frontline municipalities in Figure 2.4. Here, only frontline

municipalities are shaded, where partitioned and unpartitioned municipalities are shaded dark

and light respectively. Clearly, the position of the IEBL was strongly influenced by proximity to

the frontlines; however, the creation of partitioned municipalities appear somewhat arbitrary

as several frontline municipalities dodged the IEBL by fairly narrow margins, so the incidence

of municipal partition is arguably exogenous.

42

Figure 2.2 ‐ Municipalities by Ethnic Majority (Post‐W

ar)

Note: M

unicipalities w

ith a num

erical ethnic majority (m

ore than 50 pe

rcent) are shad

ed; a Serb majority is sha

ded in dark grey, a Croat m

ajority is 

shad

ed in m

edium gray, and a Bosniak m

ajority is sha

ded in ligh

t grey.

43

Figure 2.3 ‐ Municipalities by Entity

Note: The dark lin

e de

notes the IEBL w

hich sep

arates th

e RS (sha

ded) from FBiH (u

nsha

ded). B

rčko (crossed

) is exclud

ed from th

e an

alyses in th

is 

pape

r.

44

Figure 2.4 ‐ Municipalities by Frontline and Partition

Note: The dark lin

e de

notes the IEBL

. Frontlin

e mun

icipalities are sha

ded, w

here partitioned (unp

artitioned) m

unicipalities are sha

ded da

rk (light). 

Brčko (crossed

) is exclud

ed from th

e an

alyses in th

is pap

er.

45

2.2.3 Public Schooling

Under the pre-war Yugoslav regime, public schooling was considered to be one of the most

important activities for the development of the multi-ethnic socialist state. As such, the federal

government of Yugoslavia made sure that schooling was made accessible to everyone, regard-

less of ethnicity. In particular, primary schooling (for those aged 8-15) was made mandatory

and provided for free, and the geographical coverage of public schools was expanded to in-

clude even the most remote areas. As a republic, Bosnia had significant autonomy over eco-

nomic and fiscal management, and retained control over the provision of public schooling (Fox

and Wallich, 1997). In fact, decisions on school construction and teacher recruitment were

highly decentralized, as cantonal (provincial) and municipal governments were responsible

for secondary and primary schooling respectively (World Bank, 1996).

After the war, primary schooling continues to be mandatory and the geographical coverage

of public schools remains extensive; moreover, the provision of public schooling remains highly

decentralized.6 While general education matters – such as the standardization of curricula and

textbooks – are administered by the federal government’s Federal Ministry of Education and

Science, each FBiH canton (province) and RS has a separate education ministry that possesses

considerable financial autonomy. These education ministries make budgetary decisions on

public school construction and maintenance, teacher recruitment and training, and equipment

purchases. Fund transfers from the entity and cantonal governments then allow municipalities

to select the number of public schools and teachers they want to provide.7

A distinctive feature of post-war public schooling is that of ethnic segregation. In fact, the

overwhelming majority of Bosnian public schools are ethnically oriented with curricula tai-

lored to the dominant ethnic group (OSCE, 2007). Specifically, public schools in the RS are

6In 2004, mandatory schooling was increased to nine years (for those aged 7-15), which meant that childrenwould enter primary schooling a year earlier, and be subjected to a less intensive curriculum for the first two years.While this changes the cohort at which primary schooling is targeted, it does not impact my empirical analyses as Iuse the population aged 0-15 to construct per capita measures of public schooling.

7The precise role of municipalities vary across entities and cantons, but for the most part, they hold significantresponsibilities not only in the provision of public schooling, but also health care, parks and sports facilities, wastemanagement, and water supply, with public schooling and health care being the largest components of spending(Bieber, 2005; Werner, Guihéry, and Djukic, 2006).

46

Serb oriented, while those in the FBiH tend to be either Bosniak or Croat oriented.8 While

the existence of ethnically oriented schools in the RS can be justified by the fact that Serbs are

free to pursue ethnocentric agendas in their own entity, Bosniaks and Croats also seek their

own schools because they are especially insecure about being locked in an shared territory,

and those insecurities prompt them to be more protective of their respective ethnic identities.

Fundamentally, all three ethnic groups run ethnic public schools not only to enhance the con-

sciousness of their respective ethnic identities, but also to exclude the other ethnic groups from

the education system (Bozic, 2006).

2.3 The Model

In this section, I develop a simple theoretical model of electoral accountability to explain how

a partition may affect the provision of public schooling through ethnic homogenization, and

derive its distributional consequences. A key objective is to provide a framework that would

provide testable implications by which subsequent empirical analyses can be guided.

I begin by describing an environment in which incumbent municipal mayors are incen-

tivized by reelection to provide different types of public goods, given ethnic composition of

the municipal electorate. Consider a two-period model in which an incumbent mayor has been

voted into office at the start of period 1. Incumbents are bestowed with a municipal budget B

which can be spent on two types of public goods – universal p or ethnically oriented q – such

that p + q ≤ B. Ethnically oriented public goods can only be provided for the ethnic group

to which the incumbent belongs.9 An election is held at the start of period 2 where voters can

potentially reward the incumbent – through reelection – for good performance.

Let k denote the fraction of partisan voters whose voting decisions depend solely on eth-

8The only exceptions are the so-called "two-in-one" schools, in which Bosniak and Croat students have separateentrances, classrooms, teachers, and curricula. In these cases, Bosniaks and Croats attend the same school but donot interact with each other, and the majority group (Bosniak or Croat, depending on municipality) usually receivespreferential treatment in terms of access to funding and facilities.

9As ethnically oriented public goods can also be thought of as patronage or club goods that are exclusive to aparticular ethnic group (Kimenyi, 2006), it is reasonable to assume that incumbents can only credibly offer suchgoods to their own group. Like citizen-candidates – in models of electoral competition – whose credible policies areconstrained by innate preferences , the policy choice set of incumbents in my model is limited by ethnicity.

47

nicity. Assume that k is uniformly distributed on the interval [a, 2b− a], where b measures the

expected fraction of partisan voters and a denotes the noise in partisanship.10 The uncertainty

in k allows for unexpected variation in the socio-political climate, which may affect the level of

partisan support for the incumbent. The remaining non-partisan voters support the incumbent

with probability v(p, q) ∈ [0, 1], where vp(p, q) > 0, vq(p, q) > 0, vpp(p, q) < 0, vqq(p, q) < 0,

and vpq(p, q) = 0. Support for the incumbent is thus increasing in the provision of public

goods (at a decreasing rate), and public goods are non-substitutable across type.11 In addition,

as the minority ethnic group does not benefit from ethnically oriented public goods, the non-

partisan ethnic minority’s support for the incumbent v(p, 0) depends solely on the provision

of universal public goods.

Let m denote the ethnic majority share, where 12 < m ≤ 1. Suppose that the incumbent

belongs to the ethnic majority, then he is reelected if:

km + (1− k) [mv(p, q) + (1−m)v(p, 0)] >12

Notice that the incumbent’s reelection likelihood consists of two parts: a partisanship com-

ponent derived solely from the size of his ethnic group, and a performance-driven component

that depends on how he allocates his budget to provide different types of public goods. This

setup captures the feature of partisanship, while ensuring that political accountability exists

even when ethnic composition is heavily skewed i.e. when m→ 1.12

Next, let the reelection probability be π = Prob{

km + (1− k) [mv(p, q) + (1−m)v(p, 0)] > 12

}.

By exploiting the distributional properties of k, we can also express the reelection probability

as π = 1− 12(b−a) ×

[1/2−[mv(p,q)+(1−m)v(p,0)]m−[mv(p,q)+(1−m)v(p,0)] − a

]. Assuming that incumbents are opportunistic

and derive utility u from office, they maximize πu subject to the budget constraint, and the first

10This setup also assumes that 1 > b > a ≥ 2b− 1, and is equivalent to k = b + ε, where ε is uniformly distributedon [−b + a, b− a] with a zero mean.

11Without loss of generality, I also make the implicit assumptions that v(0) ≥ 0 and v(B) ≤ 1.12Insofar as k is not too large (small), the incumbent will not win (lose) for sure. The exact conditions that are

required for an interior solution are a ≯ 1/2−[mv(p,q)+(1−m)v(p,0)]m−[mv(p,q)+(1−m)v(p,0)] ≯ (2b− a).

48

order conditions reduce to:

vp(p∗, q∗) = mvq(p∗, q∗)

The equilibrium result above suggests that the marginal effect of providing universal public

goods on voter support is proportional to that of providing ethnically oriented public goods,

by a factor that is equal to the share of the ethnic majority. In other words, optimality requires

the equalization of the incumbent’s marginal benefits (votes), given the ethnic composition of

the electorate. Without specifying the functional form of v(p, q), we cannot compare between

p∗ and q∗ as it depends crucially on the relative contribution of votes from providing universal

and ethnically oriented public goods. For instance, it may well be the case that q∗ > p∗ if

providing ethnically oriented public goods confers significantly more votes than an equivalent

provision of universal public goods. That said, the equilibrium result does imply that public

goods provision {p∗, q∗} depends only on budget size and the ethnic majority share.

Now, suppose that a municipality is partitioned, and as a result, is subjected to ethnic ho-

mogenization. Through implicit differentiation, I obtain the following, omitting the equilib-

rium arguments {p∗, q∗}:

∂q∗

∂m=

vq

vpq −mvqq> 0

The result above says that spending on ethnically oriented public goods will be relatively

higher when the ethnic majority share is greater. Therefore, comparing partitioned and un-

partitioned municipalities, the former will direct more resources towards ethnically oriented

public goods, as the payoff for the incumbent mayor is higher due to ethnic homogenization.

As the overwhelming majority of Bosnian schools are ethnically oriented with curricula spe-

cific to the dominant ethnic group (Bozic, 2006; OSCE, 2007), subsequent empirical analyses on

public schooling in Section 2.6.2 will effectively be testing this result.

On a related note, as partitioned municipalities form a subset of frontline municipalities, the

49

model also provides a caution against (possibly) attributing the effect of budget differentials

to the partition. Specifically, if frontline municipalities receive more rebuilding aid that are

allocated to the provision of public schooling (since ∂q∗∂B > 0), we may not be able to isolate the

effects of the partition by comparing partitioned and unpartitioned municipalities. This issue

will be considered more carefully in Section 2.5.3.

Finally, I examine the model’s distributional implications by considering how the provision

of public goods affect both the ethnic majority and minority. In particular, I use the support

probabilities – v(p, q) for the ethnic majority, and v(p, 0) for the ethnic minority – to measure

the welfare gains that each ethnic group derives from the public goods.13 It is then straight-

forward to deduce that any non-zero provision of ethnically oriented public goods will divert

resources towards benefitting the ethnic majority, creating a disparity in welfare between the

ethnic majority and minority. If partitioned municipalities provide more ethnically oriented

public goods, this result implies that the ethnic majority (minority) should be better (worse)

off residing in partitioned municipalities. I will examine this prediction by comparing primary

school attendance rates across partitioned and unpartitioned municipalities in Section 2.6.4.

2.4 Data

To address the question of whether and why partitioned municipalities provide more public

goods, I compile a 15-year panel of municipality-level data from several sources. The panel

includes four pre-war years (1986–1989) and 11 post-war years (1996–2006).14 Data on pri-

mary schools and teachers are obtained from the Bosnian Federal Office of Statistics and the

Republika Srpska Institute of Statistics. The provision of public schooling is measured by the

13From this perspective, the municipal welfare gains can be represented by mv(p, q) + (1 − m)v(p, 0), whichis simply a weighted combination of ethnic group gains. In fact, a utilitarian central planner who maximizesmv(p, q)+ (1−m)v(p) subject to the budget constraint, will arrive at the same equilibrium as that of the opportunis-tic incumbent. This implies that the model’s equilibrium is Pareto efficient, assuming that the utilitarian approachis correct. Notably, the equilibrium provision of public goods described in Alesina, Baqir, and Easterly (1999) is alsoefficient, as both of our models rely on preference-aggregating mechanisms under full information.

14Data for 1990 and 1991 were unavailable because the Yugoslav regime reported information on schools andteachers with a two-year lag, which meant that the last Yugoslav yearbook in 1991 only contained figures up to1989. Demographic data for 1991, however, exist because they were collected during the 1991 Yugoslav census.Understandably, no official statistic exists for the period of the war (1992–1995).

50

per capita number of primary schools (and teachers), defined as the number of public primary

schools (and teachers) by the number of children aged 0-14 in thousands.15

Notably, as the pre-war data on schooling resources are only observed at the relevant mu-

nicipality level, the raw data is effectively an unbalanced panel with a smaller pre-war com-

ponent. In general, there are two ways to proceed. First, without making assumptions about

the pre-war distribution of schools and teachers, we can collapse the partitioned municipalities

into their pre-war units, losing observations as a result. Second, we can impute the pre-war

number of schools and teachers for each pair of partitioned municipalities, by distributing the

aggregate resources of the pre-war unit according to some reasonable formula. A discussion of

these two methods follows in Section 2.5.2.

Demographic indicators, including population size, age group, ethnic composition, and

birth, death and infant mortality rates, are also taken from the Bosnian Federal Office of Statis-

tics and the Republika Srpska Institute of Statistics. These data are drawn from annual sta-

tistical yearbooks, except for pre-war ethnic composition which is constructed by using birth,

death and infant mortality rates from the 1991 census. Determining pre-war demographic data

for partitioned municipalities that only came into existence after the war is cumbersome; for-

tunately, the 1991 census contains data at the sub-municipal level which allow me to compute

pre-war demographic indicators. In addition, I use ethnic composition to construct measures

of ethnic heterogeneity at the municipality level. Following the standard approach in the liter-

ature on ethnic diversity, I calculate the ethnic fractionalization index – first proposed by Taylor

and Hudson (1972) – which measures the probability that two randomly selected individuals

are of different ethnicity (Alesina, Devleeschauwer, Easterly, Kurlat, and Wacziarg, 2003). In

addition, I compute the polarization index, which determines how close the ethnic distribu-

tion is to the bi-polar case with two equally sized groups (Reynal-Querol, 2002; Montalvo and

15As population data are only provided in broad age categories (0-14, 15-64, and 65 and over), the 0-14 agegroup is the best available estimate of the primary schooling population. On a separate note, although alternativemeasures such as school size and student-teacher ratio are available, they are difficult to implement as enrollmentmay be responsive to the partition, given that some students bus across jurisdictions just to be able to attend mono-ethnic schools of their own (OSCE, 2007).

51

Reynal-Querol, 2005). Both of these indices increase in the extent of ethnic heterogeneity.16

In addition to the municipality-level data, I use the 2001–2004 Bosnian Living Standards

Measurement Survey to help address the question on distributional consequences. The Bosnian

Living Standards Measurement Survey contains a nationally-representative sample of individ-

uals from 25 municipalities (14 from the FBiH, and 11 from RS). Twelve of these are frontline

municipalities, and six are partitioned municipalities. The attrition rate of households and in-

dividuals across waves is no more than 5 percent, which is relatively low compared to other

national panels. The key variables pertain to individual characteristics and schooling informa-

tion, all of which are contained within the first two waves. In particular, I will be using school

attendance data from approximately 1000 primary schoolers aged 7-15, to examine distribu-

tional effects by ethnicity.

Finally, I use data from several other sources to address threats to the identifying assump-

tion and perform robustness checks. For instance, to shed light on the possible endogeneity of

partition, I use the following to conduct placebo tests: war casualty data from the Research and

Documentation Center in Sarajevo; war damage, post-war repair, and migration data from the

UNHCR; and topographic data – GTOPO30 – from the United States Geological Survey’s Cen-

ter for Earth Resources Observation and Science.17 I also compile data on municipal elections

(1990, 1997, 2000, and 2004) based on the works of Arnautovic (1996) and Schmeets (1998), and

from the Election Commission of Bosnia, to shed light on the electoral process.18 These data

16In the Bosnian context, these indices also approximate measures of religious heterogeneity given the (almost)perfect mapping of ethnicity to religious affiliation. On a separate note, these indices assume constant ethnic dis-tance across groups; for example, they assume away the possibility that Bosniaks and Croats may be more similarbecause they both use the Latin (instead of the Cyrillic) alphabet, or that Croats and Serbs may be more similarbecause of their shared Christian (and not Islamic) faith.

17In particular, the extent of war damage – in terms of the percentage of damaged buildings – was surveyed at theend of the war, while post-war repairs – in terms of the percentage of repaired buildings – were ascertained at theend of 2005. The UNHCR also maintains a database of internally displaced persons that allows me to construct dataon the number of out-migrants for each municipality. As the UNHCR database is based on registered internally dis-placed persons who return to their original municipality of residence or move to another municipality, it precludesinternational refugees who remain overseas. Nevertheless, it is useful to the extent that it reflects migration patternsthat took place during the war.

18The 1990 municipal elections were the first genuine multi-party elections in which voters elected mayors whohad considerable authority in local governance. After the war, municipal elections are based on the system of party-list proportional representation; candidates run for the Municipal Assembly of their municipality, not for specificpositions, while voters vote for parties rather than candidates. From 2000 onwards, voters can vote on an open list,on which they can choose by party or by candidates.

52

allow me to check whether electoral factors – such as the winning margin or the number of

municipal seats – could be driving the relationship between the partition and the provision of

public schooling.

2.5 Empirical Methodology

2.5.1 Identification

To identify the effects of the partition on public schooling, I employ municipality-level panel

data in a difference-in-differences (DID) regression as follows:

PUBLICmt = β(PARTITIONm × POSTt) + αm + γt + εmt (2.1)

where PUBLICmt refers to the measure of public schooling – per capita number of primary

schools or teachers – in municipality m at year t; PARTITIONm and POSTt are indicators

for partitioned municipalities and the post-war period respectively; αm and γt denote time-

invariant municipality fixed effects and year fixed effects respectively; and εmt is the idiosyn-

cratic error term.

In this specification, the effects of the partition – represented by β – are estimated from

differences in public schooling before and after the war, across partitioned and unpartitioned

municipalities. The identifying assumption is that changes in public schooling over time would

have been the same across partitioned and unpartitioned municipalities, in the absence of the

partition. While the DID estimator is usually subject to the problem of differential trends, the

issue is less of a concern here as I am able to estimate pre-war trends from four years of data

(1986-1989).

The inclusion of municipality fixed effects is particularly important for the identification

of β, as it ensures that I am not attributing the influence of time-invariant municipal traits to

the partition. For example, while municipalities in the Sarajevo canton – many of them parti-

tioned – appear to have more public primary schools than the average municipality, there may

53

be something intrinsic about being located in the capital of the country that also affects the

provision of public schooling. Therefore, controlling for municipality fixed effects allows me

to capture the effects of the partition that are over and above those due to municipal character-

istics.

Similarly, economic and political cycles may also help explain the variation in the provision

of public schooling, so it is important to understand how year-specific effects may matter for

the identification of β. For instance, if municipal mayors try to improve their chances for reelec-

tion by increasing their expenditure on public goods before an election, my estimate may be

biased if the political cycle is correlated with the timing of the partition. In this case, however,

the partition was imposed simultaneously and permanently, so we do not have to be concerned

with the possibility that municipalities were partitioned in years that coincided with the eco-

nomic and political cycles. Nevertheless, year fixed effects help account for changes in the

provision of public schooling over time and are thus included in the econometric specification.

2.5.2 Unit of Analysis

As mentioned earlier, the pre-war data on schooling resources are only observed at the relevant

municipality level, so I have to make adjustments to obtain a balanced panel. The first method

involves collapsing the partitioned municipalities into their pre-war units, and thus require no

assumption about the pre-war distribution of schools and teachers. That said, this approach

removes variation in the data – among pairs of partitioned municipalities – that may be impor-

tant, and reduces power in identifying the effects of the partition. The alternative is to impute

the number of pre-war schools and teachers by some reasonable formula, to be able to exploit

the full variation of the data.

A reasonable starting point is to assign pre-war schooling resources fairly between pairs

of partitioned municipalities, such that each partitioned municipality has the same per capita

number of pre-war schools and teachers as its counterpart. This naive procedure effectively as-

sumes that pairs of partitioned municipalities are identical in terms of their pre-war schooling

54

capacity, which may not be true. For example, it is completely reasonable to imagine that, prior

to the partition, the ethnic minority section was already receiving less resources than ethnic

majority one. Therefore, to examine the sensitivity of my results to assumptions about the pre-

war distribution of schooling resources, I also consider alternative imputations that apportion

schools and teachers unequally across ethnicities. This sensitivity analysis will shed light on

possible biases that may be due to the arbitrary assignment of pre-war schooling resources.

2.5.3 Addressing Threats to Validity

Suppose we have reasons to believe that, in the absence of the partition, there exist unobserved

factors that could cause public schooling to evolve differently for partitioned and unpartitioned

municipalities, then the identifying assumption in the DID approach may be violated. Indeed,

according to Besley and Case (2000), the source of policy variation – in this case, the variation

in the incidence of municipal partition – must be thoroughly investigated to avoid erroneous

inferences. To this end, I look for possible pre-war differences between partitioned and un-

partitioned municipalities that may be worrisome. In the left panel of Table 2.1, we can see

that the incidence of municipal partition is at least uncorrelated with most pre-war municipal

characteristics; however, partitioned municipalities appear to be more ethnically polarized and

also experience significantly more damage. Should partitioned municipalities receive more aid

for rebuilding public schools, my DID estimate may suffer from endogeneity bias. 19

19Differences in reconstruction aid are important in this case because targeted programs such as the EmergencyEducation Reconstruction Project resulted in the reopening of many schools (World Bank, 1996; Bisogno and Chong,2002).

55

Table 2.1 ‐ Pre‐War Municipal Descriptive Statistics

Total

Partition

Other

Diff.

P‐value

Total

Partition

Other

Diff.

P‐value

War casua

lty ra

te0.022

0.022

0.022

0.000

0.974

0.023

0.022

0.023

‐0.001

0.893

    

(0.030)

(0.027)

(0.030)

(0.006)

(0.023)

(0.027)

(0.023)

(0.006)

Percentage of d

amaged hou

sing

0.337

0.475

0.289

0.186

0.000

0.430

0.475

0.386

0.089

0.163

    

(0.245)

(0.235)

(0.245)

(0.051)

(0.240)

(0.235)

(0.240)

(0.063)

Out‐m

igrants pe

r cap

ita0.053

0.064

0.049

0.015

0.217

0.063

0.064

0.063

0.000

0.974

    

(0.055)

(0.051)

(0.055)

(0.012)

(0.051)

(0.051)

(0.051)

(0.014)

Ethn

ic fractio

nalisation, 1991

0.473

0.516

0.458

0.058

0.137

0.515

0.516

0.513

0.003

0.946

    

(0.177)

(0.141)

(0.177)

(0.039)

(0.144)

(0.141)

(0.144)

(0.039)

Ethn

ic polarization, 1991

0.719

0.785

0.696

0.089

0.076

0.776

0.785

0.767

0.017

0.688

(0.228)

(0.162)

(0.228)

(0.043)

(0.162)

(0.162)

(0.162)

(0.043)

Popu

latio

n size (tho

usan

ds), 1991

39.717

44.471

38.053

6.418

0.377

43.903

44.471

43.354

1.117

0.905

(32.946)

(29.262)

(32.946)

(9.302)

(34.799)

(29.262)

(34.799)

(9.302)

Prop

ortio

n of Bosniaks, 1991

0.393

0.404

0.389

0.016

0.773

0.408

0.404

0.412

‐0.008

0.891

    

(0.246)

(0.238)

(0.246)

(0.058)

(0.216)

(0.238)

(0.216)

(0.058)

Prop

ortio

n of Serbs, 1991

0.349

0.397

0.333

0.064

0.286

0.414

0.397

0.431

‐0.034

0.599

    

(0.272)

(0.217)

(0.272)

(0.064)

(0.239)

(0.217)

(0.239)

(0.064)

Prop

ortio

n of Croats, 1991

0.203

0.146

0.222

‐0.076

0.203

0.122

0.146

0.099

0.047

0.289

(0.272)

(0.201)

(0.272)

(0.044)

(0.165)

(0.201)

(0.165)

(0.044)

Prop

ortio

n of Yug

oslavs, 1991

0.036

0.035

0.037

‐0.002

0.809

0.038

0.035

0.040

‐0.005

0.605

    

(0.034)

(0.034)

(0.034)

(0.010)

(0.039)

(0.034)

(0.039)

(0.010)

Prim

ary scho

ols pe

r cap

ita, 1989

2.885

2.814

2.910

‐0.096

0.753

2.852

2.814

2.888

‐0.074

0.850

(1.387)

(1.420)

(1.387)

(0.390)

(1.459)

(1.420)

(1.459)

(0.390)

Prim

ary sch. teachers per cap

ita, 1989

24.308

24.579

24.213

0.366

0.649

25.036

24.579

24.478

‐0.899

0.406

(3.636)

(3.598)

(3.636)

(1.075)

(4.047)

(3.598)

(4.047)

(1.075)

Observatio

ns108

2880

5728

29

Full sample

Fron

tline m

unicipalities

Stan

dard deviatio

ns in parentheses. Figures re

flect averages at th

e pre‐war m

unicipality level. Th

is sam

ple of pre‐w

ar m

unicipalities exclude

s Brčko.

56

To address this concern, I consider two alternative identification strategies. The first strat-

egy locates a sub-sample for which the identifying assumption might hold, and conducts the

estimation from municipalities in the sub-sample. As articulated by Besley and Case (2000), the

choice of a comparison group must be considered carefully, as it must be stable and adequately

reflect the effects of changes in other determinants of outcomes. By considering only frontline

municipalities, we can see that the incidence of municipal partition appears to be uncorrelated

with municipal characteristics (right panel, Table 2.1). As such, I exploit this exogeneity by

estimating the effects of the partition among frontline municipalities only. To distinguish this

estimate from its DID counterpart, I call it the frontline difference-in-differences (FDID) esti-

mator.

The second strategy takes the violation of the identifying assumption seriously by us-

ing a propensity score – introduced by Rosenbaum and Rubin (1983) – to adjust for relevant

time-invariant differences between partitioned and unpartitioned municipalities. The propen-

sity score measures the probability of being a partitioned municipality, conditional on several

pre-partition covariates, including war casualty rate, proportion of damaged buildings, out-

migration rate, population size, polarization and fractionalization indices, and the per capita

number of primary schools and teachers. Following Hirano, Imbens, and Ridder (2003), I use

the inverse of a nonparametric estimate of the propensity score to construct weights that would

yield a more representative sample, and use them to run weighted least squares difference-in-

differences (WDID) regressions.20 In this case, the WDID estimator is not only consistent, but

also achieves the semiparametric efficiency bound.

While the two alternative estimators – FDID and WDID – address the possible endogeneity

of partition, the identifying assumption is never directly tested and thus remains a lingering

identification issue. As such, I also perform a series of placebo tests – deferred to Section 2.7.2

– to check whether my results could be driven by confounding factors.

20Given that p(xi) is the nonparametric estimate of the propensity score conditional on pre-partition covariatesxi, the weights assigned to partitioned and unpartitioned municipalities are 1

p(xi)and 1

1− p(xi)respectively.

57

2.5.4 Robust Standard Errors

Following standard practice in the empirical literature, I compute cluster-robust standard er-

rors that are adjusted to allow for heteroscedasticity and within-municipality correlations.

However, as I am also using a fairly long panel in a setting with simultaneous intervention (the

municipal partition, that is), even cluster-robust standard errors are subject to biases from serial

correlation (Bertrand, Duflo, and Mullainathan, 2004; Donald and Lang, 2007; Cameron, Gel-

bach, and Miller, 2008). As such, I employ two correction methods to compute autocorrelation-

consistent standard errors. The first correction is through the use of the block-bootstrap with

1,000 replications, and the second is to run the DID with an aggregated sample that is col-

lapsed into pre- and post-war. In deciding whether or not coefficient estimates are statistically

significant, these autocorrelation-consistent standard errors should provide a more conserva-

tive perspective relative to the cluster-robust ones.

2.6 Empirical Analysis

2.6.1 Ethnic Homogenization

In this section, my first task is to establish whether the partition brought about ethnic homog-

enization among partitioned municipalities. To this end, I run DID regressions – similar to the

one shown in equation (1) – with the ethnic majority share, and the ethnic fractionalization and

polarization indices as dependent variables. From column (1) of Table 2.2, we can see that the

ethnic majority share is approximately 9.9 percent larger in partitioned municipalities, relative

to unpartitioned ones. The coefficient estimates of the partition on ethnic fractionalization and

polarization indices are -0.104 and -0.160 respectively, both of which represent a substantial

decrease of more than half a standard deviation [columns (2)-(3), Table 2.2]. These estimates

indicate that partitioned municipalities not only have a larger ethnic majority share, but also

less ethnic diversity, suggesting that they experienced significant ethnic homogenization after

the partition.

58

Table 2.2 ‐ Partition and Ethnic Homogenization

Ethn

ic m

ajority 

share

Fractio

naliz

ation 

inde

xPo

larizatio

n       

inde

xMigratio

n         

dummy

DID (1

)DID (2

)DID (3

)OLS (4

)

Partition x Post

0.099***

‐0.104***

‐0.160***

[0.028]

[0.029]

[0.054]

Ethn

ic m

inority (p

re‐w

ar) 

0.221**

[0.106]

Partition (p

re‐w

ar) x Ethnic minority (p

re‐w

ar)

0.085*

[0.047]

Individu

al cha

racteristics

YMun

icipality fixed effects

YY

YY

Year fixed effects

YY

Y

Mean of dep

ende

nt variable (pre‐w

ar)

0.614

0.495

0.738

Mean of dep

ende

nt variable (post‐w

ar)

0.909

0.141

0.265

0.527

Num

ber  o

f observatio

ns1824

1824

1824

7225

R‐squa

red

0.84

0.85

0.78

0.75

Dep

ende

nt variable:                            

Stan

dard

errors,clustered

bymun

icipality

,are

inpa

rentheses.*sign

ificant

at10%;**sign

ificant

at5%

;***

sign

ificant

at1%

.Colum

ns(1)‐(3)

depict

diffe

rence‐in‐differencesestim

ates

usingthesampleof

mun

icipalities,e

xcluding

Brčko.

Colum

n(4)de

pictstheordina

ryleasts

quares

estim

ates

usingindividu

al‐le

veld

atafrom

theBo

snianLiving

Stan

dardsMeasurementS

urvey.

Individu

alcharacteristicsinclud

eagean

dsex

atthetim

eof

thesurvey,a

ndpa

rental

second

aryscho

olingattainment.Pa

rtition

(pre‐w

ar)an

dEthn

icminority

(pre‐w

ar)d

enotewhether

anindividu

alʹs pre‐war m

unicipality w

as partitioned, and w

hether she w

as an ethn

ic m

inority

, respe

ctively.

59

As the IEBL was designed to end the war by separating ethnic groups, these results may

not be that surprising. Nonetheless, if Bosnians were free to migrate across municipalities (and

across entities, if they so wish) to their desired post-war destinations, it may be puzzling as to

why the degree of ethnic homogenization was greater among partitioned municipalities. The

answer, I believe, lies in the fact that Bosnians were strongly rooted to their pre-war homes,

and despite threats, coercion, and violence, many ethnic minorities refused to leave unless

absolutely necessary. Therefore, while the fear of being an ethnic minority may have been a

significant catalyst for out-migration, the partition turns out to be just as effective in accom-

plishing ethnic homogenization. Indeed, by using data from the Bosnian Living Standards

Measurement Survey, I find that while ethnic minorities are approximately 22 percent more

likely to move out of their pre-war municipalities, the likelihood increases by an additional 9

percent if they were also residing in a partitioned municipality, controlling for pre-determined

individual characteristics (age and sex) and municipality fixed effects [column(4), Table 2.2].

This implies that the partition had a substantial effect on ethnic composition that is over and

above that of the war.

Finally, are these effects on ethnic homogenization being attributed correctly to the parti-

tion, or do they also represent effects on ethnic composition due to post-war population move-

ment? For instance, if partitioned municipalities receive a greater influx of return migrants

which in turn affects ethnic composition, the interpretation of my results as partition effects

will be incorrect. To examine this, I track population size and ethnic majority share by partition

and year, and find that both of these demographic measures received a one-off shock after the

partition, and remained relatively stable for up to 10 years thereafter (Figure 2.5). This evidence

suggests that the partition induced a singular shock on ethnic diversity that persisted over the

years.

60

Figure 2.5 ‐ Demographics by Partition and Year

Ethnic majority share by Partition and Year

2030

4050

60Av

g. p

opul

atio

n si

ze ('

000s

)

1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006Year

Observations for partitioned (unpartitioned) municipalities are connected by a bold (dashed) line.

Population size by Partition and Year

.6.7

.8.9

1Av

g. e

thni

c m

ajor

ity s

hare

1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006Year

Observations for partitioned (unpartitioned) municipalities are connected by a bold (dashed) line.

Ethnic majority share by Partition and Year

2030

4050

60Av

g. p

opul

atio

n si

ze ('

000s

)

1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006Year

Observations for partitioned (unpartitioned) municipalities are connected by a bold (dashed) line.

Population size by Partition and Year

61

2.6.2 Public Schooling

Next, I examine the effect of the partition on public schooling. As implied by the theoretical

model, if the partition induced ethnic homogenization, I should expect a positive effect on

ethnically oriented public goods – in this case, ethnic schools and teachers. To get a clear idea on

what the DID estimation achieves, I plot the average per capita number of primary schools and

teachers by partition and year in Figure 2.6. Tracking these measures by year demonstrates that

the post-war provision of public schooling is significantly greater in partitioned municipalities,

even after controlling for possible pre-war differences.

Moving on to the DID analyses, I present two sets of estimates in Table 2.3 – first with the per

capita number of primary schools as dependent variable, then with the per capita number of

primary school teachers. Within each set, the first column depicts DID estimates from using the

raw data, collapsing the partitioned municipalities into their pre-war units. The second column

assigns pre-war schooling resources fairly between pairs of partitioned municipalities. The

third and fourth columns assign more pre-war schooling resources to the ethnic majority by 10

and 20 percent respectively. Finally, the fifth column assigns all pre-war schooling resources to

the ethnic majority, leaving the ethnic minority with nothing.

The coefficient estimate in column (1) indicates that the per capita number of primary

schools is higher by 2.59 (or 70 percent) in partitioned municipalities, relative to unpartitioned

ones. The point estimate hardly changes – 2.24 (58 percent) – when I assign pre-war schooling

resources fairly between pairs of partitioned municipalities [column (2)]. Indeed, only when

the imputations involve discrimination towards the ethnic minority do the estimates vary sig-

nificantly [columns (3)-(5)]. All estimates are statistically significant at the 10 percent level or

less.

62

Figure 2.6 ‐ Public Schooling by Partition and Year

23

45

67

Avg.

num

ber o

f prim

ary

scho

ols

per c

apita

1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006Year

Observations for partitioned (unpartitioned) municipalities are connected by a bold (dashed) line.

Schools per capita by Partition and Year

ta Teachers per capita by Partition and Year

23

45

67

Avg.

num

ber o

f prim

ary

scho

ols

per c

apita

1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006Year

Observations for partitioned (unpartitioned) municipalities are connected by a bold (dashed) line.

Schools per capita by Partition and Year

2030

4050

Avg

. num

ber o

f prim

ary

scho

ol te

ache

rs p

er c

apita

1986 1988 1990 1992 1994 1996 1998 2000 2002 2004 2006Year

Observations for partitioned (unpartitioned) municipalities are connected by a bold (dashed) line.

Teachers per capita by Partition and Year

63

Table 2.3 ‐ Partition and Public Schooling (Raw Data and Imputations)

Dep

ende

ntvariable:

Prim

ary scho

ols pe

r cap

itaPrim

ary scho

ol teachers per cap

ita

Raw data

Raw data

DID (1

)DID (2

)DID (3

)DID (4

)DID (5

)DID (6

)DID (7

)DID (8

)DID (9

)DID (1

0)

Partition x Post

2.591*

2.236**

3.615***

3.617***

3.289***

17.614*

12.886*

24.987***

25.025***

22.543***

[1.479]

[1.117]

[1.192]

[1.197]

[1.240]

[9.291]

[7.191]

[7.716]

[7.748]

[8.034]

Dep

ende

nt variable:                    

Impu

tatio

nsIm

putatio

ns

[1.479]

[1.117]

[1.192]

[1.197]

[1.240]

[9.291]

[7.191]

[7.716]

[7.748]

[8.034]

Mun

icipality and year fixed effe

cts

YY

YY

YY

YY

YY

Mean of dep

ende

nt variable (pre‐w

ar)

2.872

2.875

2.306

2.303

2.435

27.486

26.972

22.038

22.013

23.005

Mean of dep

ende

nt variable (post‐w

ar)

3.702

3.884

3.884

3.884

3.884

34.321

34.470

34.470

34.470

34.470

pp

Num

ber o

f observatio

ns1504

1824

1824

1824

1824

1504

1824

1824

1824

1824

R‐squa

red

0.49

0.51

0.49

0.49

0.48

0.34

0.37

0.37

0.37

0.36

Stan

dard

errors,clustered

bymun

icipality

,are

inpa

rentheses.*sign

ificant

at10%;**s

ignifican

tat5

%;***sign

ificant

at1%

.Thissampleof

mun

icipalities

exclud

esBrčko.

All

columns

depict

diffe

rence‐in‐differencesestim

ates.Colum

ns(1)an

d(6)usetheraw

data

and

colla

psepo

st‐w

armun

icipalities

totheirpre‐war

units,losing

All

columns

depict

diffe

rencein

diffe

rences

estim

ates.Colum

ns(1)an

d(6)usetheraw

data

and

colla

psepo

stwar

mun

icipalities

totheirprewar

units,losing

observations

asaresult;

columns

(2)a

nd(7)a

ssignpre‐war

scho

olsan

dteacherfairlyto

pairsof

partition

edmun

icipalities;colum

ns(3)a

nd(8)a

ssign10

percentm

orepre‐

war

scho

olsan

dteachers

totheethn

icmajority

;colum

ns(4)a

nd(9)a

ssign20

percentm

orepre‐war

scho

olsan

dteachers

totheethn

icmajority

;colum

ns(5)a

nd(10)

assign

all p

re‐w

ar schoo

ls and teachers to th

e ethn

ic m

ajority

.

64

By comparing the results across columns, we ca see that the effects are considerably large, as

even the smallest of these estimates would imply that partitioned municipalities have at least

two more schools for every thousand children under the age of 15. Put another way, while

unpartitioned municipalities have only one primary school for every 330 children, partitioned

municipalities have approximately one primary school for every 200 children. Moreover, the

sensitivity analyses show that the effects are more substantial when the ethnic majority holds

a pre-war advantage. As an example, under the extreme case where the ethnic majority mo-

nopolizes resources, the per capita number of primary schools is higher by 3.29 (or 85 percent).

These results suggest that the naive approach of assigning assigning pre-war resources fairly

between pairs of partitioned municipalities actually yields us conservative estimates of the par-

tition effects. More importantly, these results suggest that the pre-war distribution of schooling

resources – that is missing from the raw data – may convey valuable information about under-

lying preferences for ethnically oriented public goods.

In terms of the per capita number of primary school teachers, the results follow a similar

pattern but the estimates are substantially smaller and less precise. From column (6), we can

see that there are about 17.61 (or 51 percent) more primary school teachers for every thou-

sand children under the age of 15 in partitioned municipalities. In the alternative specifica-

tions [columns (7)-(10)], the estimates are no smaller than 12.89 (or 37 percent) although they

are nowhere as large as those found for the per capita number of primary schools. There are

two possible explanations for this. First, although municipal governments are responsible for

building and maintaining primary schools as well as recruiting teachers, they have no control

over teacher salaries; instead, salaries are paid by the cantonal government in the FBiH, and

the entity government in RS (Werner, Guihéry, and Djukic, 2006). Therefore, to the extent that

partition municipalities have more autonomy over decisions on schools than on teachers, we

should expect weaker results on the provision of teachers. Second, even if partitioned mu-

nicipalities have complete control over teacher recruitment, they may find difficulty in getting

more teachers, especially since ethnic minority teachers are intentionally excluded in the hiring

65

process. This may also account for the weaker results on the provision of teachers.

Next, with regards to identification, I run the difference-in-differences under alternative

specifications (Table 2.4). From now on, I adopt the naive imputation procedure (of distributing

pre-war resources fairly) so as to exploit the full variation of the data. Again, there are two sets

of estimates – first with the per capita number of primary schools as dependent variable, then

with the per capita number of primary school teachers. Within each set, the first column de-

picts DID estimates while the second and third columns depict the FDID and WDID estimates

respectively. The fourth column depicts DID estimates with block-bootstrapped standard er-

rors, and the fifth column depicts DID estimates with an aggregated sample that is collapsed

into pre- and post-war.

In general, the results on public schooling are robust to alternative specifications. In par-

ticular, the coefficient estimates under the FDID and WDID specifications are not too different

from their DID counterpart, allaying concerns over the validity of the identifying assumption

(discussed in Section 2.5.3). In fact, if one had suspected that the DID coefficient estimates are

positive because partitioned municipalities are building more primary schools over time for

reasons unrelated to the partition, the results certainly suggest otherwise since the FDID and

WDID estimates [columns (2)-(3)] are actually larger. In other words, if the FDID and WDID

specifications are properly accounting for a possible bias, the results actually indicate that the

bias is downwards, in which case the DID estimate should be seen as a conservative one. Fur-

thermore, the results on public schooling are also robust to standard error adjustments as the

precision of the estimates is neither affected by the block-bootstrap or the collapsed sample

modification. Overall, the results from alternative specifications and standard error adjust-

ments suggest that we can be reasonably confident of the DID estimates.

66

Table 2.4 ‐ Partition and Public Schooling

DID (1

)FD

ID (2

)WDID (3

)DID (4

)DID (5

)DID (6

)FD

ID (7

)WDID (8

)DID (9

)DID (1

0)

Partition x Post

2.236**

2.714**

2.859**

2.236**

2.175**

12.886*

14.549*

12.751+

12.886*

12.106*

[1.117]

[1.155]

[1.138]

[1.027]

[1.033]

[7.191]

[7.818]

[7.995]

[6.852]

[6.750]

Mun

icipality and year fixed effe

cts

YY

YY

YY

YY

Mean of dep

ende

nt variable (pre‐w

ar)

2.875

2.776

2.875

2.875

2.875

26.972

25.934

26.972

26.972

26.972

Mean of dep

ende

nt variable (post‐w

ar)

3.884

4.178

3.884

3.884

3.884

34.470

36.069

34.470

34.470

34.470

Num

ber o

f observatio

ns1824

1150

1824

1824

289

1824

1150

1824

1824

289

R‐squa

red

0.51

0.50

0.58

0.51

0.06

0.37

0.46

0.57

0.37

0.03

Dep

ende

nt variable:                    

Prim

ary scho

ols pe

r cap

itaPrim

ary scho

ol teachers per cap

ita

Stan

dard

errors

arein

parentheses,

andareclusteredby

mun

icipality

,except

forcolumns

(4)an

d(9),where

they

areblock‐bo

otstrapp

ed.+

sign

ificant

at15%;*

sign

ificant

at10%;**sign

ificant

at5%

;***

sign

ificant

at1%

.Thissampleof

mun

icipalities

exclud

esBrčko,

andinclud

esim

putedpre‐war

values

that

aredistribu

ted

fairly

betw

eenpa

rtition

edmun

icipalities.C

olum

ns(1),(4),(6),an

d(9)de

pict

diffe

rence‐in‐differencesestim

ates;c

olum

ns(2)an

d(7)de

pict

diffe

rence‐in‐differences

estim

ates

basedon

thesampleof

fron

tline

mun

icipalities;columns

(3)an

d(8)de

pict

weigh

tedleastsqua

resdiffe

rence‐in‐differences

estim

ates,w

eigh

tingon

the

inverseof

ano

n‐pa

rametricestim

ateof

theprop

ensity

score;

columns

(5)an

d(10)

depict

diffe

rence‐in‐differencesestim

ates

basedon

anaggregatesamplethat

iscolla

psed in

to pre‐ a

nd post‐w

ar, and th

erefore do not in

clud

e mun

icipality and year fixed effe

cts.

67

2.6.3 Ethnic Politics and Elections

So far, I have shown that partitioned municipalities are more ethnically homogeneous and pro-

vide more public schooling. This result is consistent with the findings of the existing literature

on ethnic diversity, as many scholars have argued that homogenized communities have conver-

gent preferences over the type of public goods to provide, and thus demand more of it (Cutler,

Elmendorf, and Zeckhauser, 1993; Temple, 1996; Poterba, 1997; Goldin and Katz, 1999; Alesina,

Baqir, and Easterly, 1999).21 My objective in this section, therefore, is to go beyond where a typ-

ical analysis of ethnic diversity and public goods would end, by exploring the channel through

which homogeneous communities in partitioned municipalities attain ethnically oriented pub-

lic goods.

As posited in the theoretical model in Section 2.3, the ethno-political mechanism may be

particularly relevant in Bosnia, as preferences for ethnically oriented public goods are highly

pronounced. Indeed, as most Bosnians care deeply about having ethnic schools in which

classes are conducted in the language and curriculum that cater to their own ethnic group

(Bozic, 2006; OSCE, 2006), it is plausible that homogeneous communities in partitioned munic-

ipalities elect politicians who are more likely to provide ethically oriented public goods.22

To investigate this, I examine the results of four municipal elections (1990, 1997, 2000, and

2004). First, I check whether ethno-nationalist parties – that are presumably more willing in

providing ethnically oriented public schooling – are more likely to win in partitioned munici-

palities. To this end, I run a DID regression using a dummy for an ethno-nationalist winner as

dependent variable, controlling for municipality and year fixed effects.23 From column (1) of

Table 2.5, we can see that the coefficient is positive but imprecisely estimated, which suggests

21Alternatively, the negative relationship between ethnic diversity and public schooling can be explained byhigher coordination costs among diverse communities (Vigdor, 2004; Miguel and Gugerty, 2005). However, as I ar-gue in this section, the relevant mechanism for Bosnia appears to be related to preferences rather than coordination.Moreover, in the next section, I find evidence of the ethnic majority group benefitting more from the differentialprovision of public schooling, which is consistent with the results being driven by preferences (Jackson, 2008).

22A recent public opinion survey conducted by the OSCE reveals strong preferences for ethnically oriented syl-labi. Specifically, 69 percent of the respondents insist that the “National Group of Subjects” – consisting of ethnicallybiased components like mother tongue, literature, geography and history – are important and necessary; moreover,63 percent think that it guarantees their cultural identity (OSCE, 2006).

23The ideological categorization of political parties is shown in Appendix Table 2.A.1, which follows closely thework of Pugh and Cobble (2001).

68

that the probability of electing ethno-nationalists is uncorrelated with the incidence of munic-

ipal partition. This result may appear puzzling at first, as partitioned municipalities are more

ethnically homogeneous and should thus have more partisan supporters; however, given that

ethno-nationalist parties win these municipal contests around 87 percent of the time, the effect

of partition on winning – that is, the extensive margin – may be minimal. As such, I also explore

whether winners in partitioned municipalities receive more votes – that is, the intensive margin

– by repeating the DID regression using the winning margin as dependent variable. In column

(2) of Table 2.5, I find that elected politicians acquire winning margins of around 10.4 percent-

age points higher in partitioned municipalities, relative to unpartitioned ones. Furthermore,

when I divide the sample into municipalities with ethno-nationalists and non-nationalists win-

ners, I find that the average winning margin for ethno-nationalists is greater than that for non-

nationalists by over 12 percentage points. In fact, when I run DID regressions separately with

these sub-samples, it becomes clear that the intensive margin effects are strictly driven by the

ethno-nationalist winners [columns (3)-(4), Table 2.5].

69

Table 2.5 ‐ Partition and Elections

All

Ethn

o‐na

tiona

list 

wins

Non‐

natio

nalist 

wins

DID (1

)DID (2

)DID (3

)DID (4

)DID (5

)DID (6

)

Partition x Post

0.066

0.104**

0.110**

0.059

2.034**

10.544*

[0.059]

[0.051]

[0.054]

[0.146]

[1.022]

[6.204]

Partition x Pre‐election year

0.402***

6.182

[0.143]

[4.104]

Partition x Post‐e

lection year

0.532

5.119

[0.426]

[3.274]

Mun

icipality and year fixed effe

cts

YY

YY

YY

Mean of dep

ende

nt variable (pre‐w

ar)

0.965

0.307

0.314

0.096

2.875

26.972

Mean of dep

ende

nt variable (post‐w

ar)

0.840

0.272

0.291

0.177

3.884

34.470

Num

ber o

f observatio

ns561

561

489

721824

1824

R‐squa

red

0.45

0.50

0.55

0.69

0.51

0.37

Winning m

argin

Ethn

o‐na

tiona

list 

winner

Dep

ende

nt variable:                    

Stan

dard

errors

arein

parentheses,an

dareclusteredby

mun

icipality

.*sign

ificant

at10%;**s

ignifican

tat5

%;***sign

ificant

at1%

.This

sampleof

mun

icipalities

exclud

esBrčko.

Ethn

o‐na

tiona

listwinnerde

notesamun

icipality

inwhich

anethn

o‐na

tiona

listmayor

was

elected.

Winning

margins

referto

thevo

tesharediffe

rencebetw

een

thewinneran

dtherunn

er‐up.

Colum

ns(3)an

d(4)de

pict

diffe

rence‐in‐differencesestim

ates

based

onthesub‐sampleof

mun

icipalities

inwhich

ethn

o‐na

tiona

lists

and

non‐na

tiona

lists

are

elected respectiv

ely.

Prim

ary 

scho

ols pe

r capita

Pri. scho

ol 

teachers per 

capita

70

Of course, elected mayors, who ultimately make decisions on public goods, must be re-

sponsive to the preferences of the electorate for the election mechanism to work. In fact, to

the extent that mayors derive votes from the delivery of public goods, they will not only allo-

cate their budgets optimally but also ensure that their spending decisions are made sufficiently

salient. For instance, mayors may time their fiscal decisions strategically, by increasing ex-

penditure on public schooling in pre-election years. Indeed, a brief examination of Figure 2.6

indicates that there may be significant surges in the provision of public schooling just before

municipal elections in 2000 and 2004, which is suggestive of a political budget cycle; more-

over, this pattern appears to be rather pronounced for partitioned municipalities and absent in

unpartitioned municipalities.24 To confirm this formally, I repeat the DID regression of public

schooling with additional control indicators for a partitioned municipality in pre- and post-

election years. From column (5) of Table 2.5, we can see that the per capita number of public

primary schools in partitioned municipalities are indeed higher by 0.402 in pre-election years,

which is over and above the average effect of the partition that is equal to 2.034. Furthermore,

the same finding does not apply to partitioned municipalities in post-election years, suggest-

ing that a political budget cycle may be in place. That said, in terms of the per capita number

of public primary school teachers, the political budget cycle appears to be absent [column (6),

Table 2.5]. This is consistent with my earlier claim that municipal governments may have more

control over the number of schools than the number of teachers.

Overall, the empirical evidence seems to agree with the conjecture that ethnically homo-

geneous communities tend to garner support for ethno-nationalist candidates who, in turn,

provide more ethnically oriented public goods. These results suggest that homogeneous com-

munities in partitioned municipalities may be getting more ethnically oriented public goods

through political means.

24In addition, the divergence in public schooling between partitioned and unpartitioned municipalities appearsto have started only after the first post-war municipal elections in 1997, which further corroborates with the ideathat the divergence is driven by spending decisions of incumbent mayors.

71

2.6.4 Distributional Consequences

While my results suggest that partitioned municipalities provide more public schooling, how

are the potential benefits being distributed among the ethnic groups? According to the theoreti-

cal model’s prediction, if resources are being directed towards ethnically oriented public goods,

such as mono-ethnic schools, the ethnic majority will benefit from residing in partitioned mu-

nicipalities while the ethnic minority will not. In this case, I use data on school attendance and

primary schooling completion from the Living Standards Measurement Survey to measure the

potential benefits that individuals may derive from public schooling.

First, I consider the school attendance of approximately 1000 children aged 7 to 15, and

examine whether there are differences across partitioned and unpartitioned municipalities. I

regress a dummy for school attendance – that equals one if a child is attending school in the

survey year – on the indicator for a partitioned municipality, controlling for age, sex, ethnicity,

parental schooling attainment and municipal characteristics. From column (1) of Table 2.6, we

can see that the coefficient of the partition indicator is 0.6 percent, statistically significant at the

10 percent level. While this is not a remarkable effect, it does suggest that school attendance

may be higher in partitioned municipalities. Next, I include the interaction of the partition

indicator and a dummy for ethnic minority as an additional control, to elicit the distributional

effects. Results from column (2) of Table 2.6 imply that being an ethnic majority residing in

a partitioned municipality increases attendance by around 5.6 percent, while being an eth-

nic minority residing in a partitioned municipality does not statistically increase attendance.

Therefore, it seems that the partitioned-induced differential provision of public schooling has

only benefitted children from the majority ethnic group.

72

Table 2.6 ‐ Distributional Consequences

Migratio

n du

mmy

OLS (1

)OLS (2

)OLS (3

)OLS (4

)OLS (5

)

Partition

0.006*

0.056***

[0.004]

[0.005]

Partition x Ethnic minority

‐0.041**

[0.016]

Partition x Coh

ort

0.041*

0.051**

[0.022]

[0.023]

Partition x Coh

ort x Ethnic minority

‐0.090**

[0.043]

Parental secon

dary schoo

ling

0.022*

[0.011]

Parental secon

dary schoo

ling 

‐0.072**

 x Ethnic minority (p

re‐w

ar)

[0.028]

Sum of a

bove coefficients

0.015

‐0.039

‐0.052*

F‐statistic

1.39

0.81

3.51

[p‐value

][0.251]

[0.378]

[0.073]

Individu

al cha

racteristics

YY

YY

YMun

icipality fixed effects

YY

YY

Y

Mean  of dep

ende

nt variable

0.975

0.975

0.968

0.968

0.527

Num

ber o

f observatio

ns1055

1055

1627

1627

7225

R‐squa

red

0.10

0.12

0.05

0.06

0.71

Dep

ende

nt variable:                    

Scho

ol atte

ndan

cePrim

ary scho

ol com

pletion

Stan

dard

errors,c

lustered

bymun

icipality

,are

inpa

rentheses.

*sign

ificant

at10%;**sign

ificant

at5%

;***

sign

ificant

at1%

.Colum

ns(1)‐(5)

depict

ordina

ryleastsqua

resestim

ates

using

individu

al‐le

velda

tafrom

the

Bosnian

Living

Stan

dards

MeasurementS

urvey.

Scho

olattend

ance

refers

towhether

anindividu

alisattend

ingscho

olin

thesurvey

year.P

rimaryscho

olcompletionrefers

towhether

anindividu

alha

sob

tained

theprim

aryscho

olcertificate.Ethn

icminority

(pre‐w

ar)de

notes

whether th

e individu

al w

as an ethn

ic m

inority in her pre‐w

ar m

unicipality of residence.

73

While the results on attendance are telling, they rely on a particular cohort of children that

may be systematically different across partitioned and unpartitioned municipalities. Therefore,

I also conduct the following cohort analysis on primary schooling completion. I first define

an affected cohort as individuals who were still in their primary schooling years in the post-

war period but would have completed primary schooling at the time of the survey. Then, I

compare them to an older cohort who would have completed primary schooling before the

war.25 Results from the cohort analysis reveal a similar pattern to that of school attendance.

Specifically, while affected cohorts in partitioned municipalities are more likely to complete

primary schooling [column (3), Table 2.6], the benefits are only accrued by the ethnic majority

– who are approximately 5.1 percent more likely to complete primary schooling – but not by

the ethnic minority [column (4), Table 2.6]. Together, the results on school attendance and

primary schooling completion indicate that the ethnic majority are the only beneficiaries from

the partitioned-induced differential provision of public schooling.

Finally, to ascertain that these distributional results are not driven selective migration –

for instance, the out-migration of ethnic minorities with a higher ability from partitioned mu-

nicipalities, leaving behind less able ethnic minorities – I also consider the determinants of

migration. To this end, I run a regression of migration on parental secondary schooling and its

interaction with a dummy for ethnic minority (pre-war), controlling for individual and munici-

pal characteristics. By examining the coefficient of parental secondary schooling attainment on

the migration dummy in column (5) of Table 2.6, we can see that it increases the likelihood of

migration by around 2.2 percent. This suggests some degree of positive ability sorting, insofar

as parental secondary schooling attainment is a good proxy for ability. However, if we look

only at ethnic minorities, it appears that more able ethnic minorities are the ones who tend

to stay as parental secondary schooling attainment lowers migration probability by about 5.2

percent. As such, we can deduce that even if selective migration is present, it should not be

driving the distributional results.

25The affected cohorts are aged 15–20 at the time of the survey in 2001, which means that they were still in primaryschool after the war, but should have completed primary schooling at the time of the survey. For comparison, I selectan older cohort aged 26–31 who would have completed primary schooling before the war.

74

2.7 Robustness Checks

2.7.1 Placebo Tests

The empirical identification of partition effects relies on the identifying assumption being valid,

that is, there are no unobserved factors that could cause the provision of public schooling to

evolve differently across partitioned and unpartitioned municipalities. Even though alterna-

tive estimators – FDID and WDID – address this issue, the identifying assumption is never

directly tested. Thus, I conduct a series of placebo tests in this section to check whether my

results could be driven by confounding factors.

First, I consider the possibility that partitioned municipalities were subjected to a greater

loss of population, thereby creating positive effects on per capita measures of public school-

ing through a smaller denominator. To address this concern, I first run a DID regression with

municipal population size as dependent variable, controlling for municipality and year fixed

effects [column (1), Table 2.7]. The coefficient of interest is imprecisely estimated, which im-

plies that population sizes are no lower in partitioned municipalities; in fact, the coefficient is

positive, which suggests that partitioned municipalities may have actually grown in popula-

tion size, relative to unpartitioned municipalities. Furthermore, if my results are truly picking

up the effects of partition on public schooling, and not as a consequence of systematic out-

migration due to the war, we should not observe out-migration rates as having a similar effect

on public schooling. To show this, I repeat the DID regressions, replacing the indicator for

partition with an indicator for high out-migration rate. In particular, I use UNHCR data on

out-migration and define municipalities as having experienced high (low) out-migration rates

if the number of out-migrants per thousand is above (below) the mean. Results from columns

(2)-(3) of Table 2.7 show that the coefficients are imprecisely estimated, suggesting that the

provision of public schooling is not statistically related to out-migration.

75

Table 2.7 ‐ Placebo Tests

Popu

latio

n s ize

Pri. scho

ols 

per c

apita

Pri. scho

ol 

teachers per Pri. scho

ols 

per c

apita

Pri. scho

ol 

teachers per Pri. scho

ols 

per c

apita

Pri. scho

ol 

teachers per 

De p

ende

nt variable:                     

size

per c

apita

capita

per c

apita

capita

per c

apita

capita

DID (1

)DID (2

)DID (3

)DID (4

)DID (5

)DID (6

)DID (7

)

Partition x Post

1.197

[1.221]

Hihou

ti

atio

ate

Pot

1054

9103

Dep

ende

nt variable:                     

High ou

t‐migratio

n rate x Post

1.054

9.103

[1.663]

[9.187]

High bu

ilding da

mage x Po

st1.320

4.121

[1.337]

[10.545]

High bu

ilding repa

ir x Post

1.333

5.410

[1539]

[10606]

[1.539]

[10.606]

Mun

icipality and year fixed effe

cts

YY

YY

YY

Y

Mean of dep

ende

nt variable (pre‐w

ar)

33.852

2.875

26.972

2.875

26.972

2.875

26.972

Meanof

depe

ndentv

ariable(post‐w

ar)

27.688

3.884

34.470

3.884

34.470

3.884

34.470

Mean of dep

ende

nt variable (post‐w

ar)

27.688

3.884

34.470

3.884

34.470

3.884

34.470

Num

ber o

f observatio

ns1824

1824

1824

1824

1824

1824

1824

R‐squa

red

0.98

0.50

0.37

0.50

0.37

0.50

0.37

Stan

dard

errors,clustered

bymun

icipality

,arein

parentheses.

*sign

ificant

at10%;**

sign

ificant

at5%

;***sign

ificant

at1%

.Th

issampleof

mun

icipalities

exclud

esBrčko,

andinclud

esim

putedpre‐war

values

that

aredistribu

tedfairly

betw

eenpa

rtition

edmun

icipalities.P

opulationsize

ismeasuredin

thou

sand

san

dinclud

esda

taon

pre‐war

popu

latio

nforpa

rtition

edmun

icipalities.Ind

icatorsforhigh

out‐m

igratio

nrate,h

ighbu

ilding

damage,

andhigh

build

ingrepa

ir,equa

lon

ewhenthemun

icipality‐le

velvalueexceed

sthemean.

Out‐m

igratio

nrate

ismeasuredby

taking

the

UNHCRestim

ateof

thenu

mberof

out‐m

igrantsdivide

dby

pre‐war

popu

latio

n(per

thou

sand

).Bu

ildingda

mageis

measuredby

thepe

rcentage

ofda

maged

build

ings

(relativeto

totalnu

mberof

pre‐war

build

ings).Bu

ildingrepa

iris

measuredby

thepe

rcentage

ofpo

st‐w

arrepa

ired

build

ings

(relativeto

thenu

mbero

fdam

aged

build

ings)

(relative to th

e nu

mber o

f dam

aged buildings).  

76

Having considered confounding factors that may affect the denominator in per capita mea-

sures of public schooling, I now look to those that may affect the numerator. In particular, I

examine whether partitioned municipalities suffered more war damage and thus undertook

more post-war reconstruction projects, as this could also generate positive effects on public

schooling. To do this, I employ UNHCR data on the percentage of damaged buildings in-

curred during the war (relative to total number of pre-war buildings) and the percentage of

repaired buildings (relative to the number of damaged buildings). Again, I conduct placebo

tests by repeating the DID regressions, replacing the indicator for partition with indicators for

high building damage and post-war building repair. Municipalities with the percentage of

damaged or repaired buildings above (below) the mean are assigned a high (low) indicator. It

turns out that the DID coefficients from these regressions are imprecisely estimated, so neither

war damage nor post-war repair appears to be associated with the provision of public school-

ing [columns (4)-(7) of Table 2.7]. These findings weaken the conjecture that the partition effects

are only a facade of differential war damage or post-conflict school construction.

Related to the point above, a confounding factor could, more generally, be associated with

war intensity. In other words, if the intensity of conflict was higher in partitioned municipal-

ities, post-war recovery aid – including funds for the reconstruction of schools – could well

be directed towards these municipalities. Barring municipality-level data on reconstruction

aid, I should at least examine whether war intensity is correlated with the provision of public

schooling. To this end, I use war casualty rate as a measure of war intensity, and repeat the

DID regressions, replacing the indicator for partition with an indicator for high war intensity.

I define municipalities as having endured high (low) intensity if the casualty rate is higher

(lower) than average. As the DID coefficients in columns (8)-(9) of Table 2.7 are imprecisely

estimated, it appears that war intensity does not account for my results on the provision of

public schooling.

77

Table 2.7 ‐ Placebo Tests (continued) Pr

i. scho

ols 

per c

apita

Pri. scho

ol 

teachers per Pri. scho

ols 

per c

apita

Pri. scho

ol 

teachers per Pri. scho

ols 

per c

apita

Pri. scho

ol 

teachers per 

De p

ende

nt variable:                     

per c

apita

capita

per c

apita

capita

per c

apita

capita

DID (8

)DID (9

)DID (1

0)DID (1

1)DID (1

2)DID (1

3)

High casualty ra

te x Post

2.224

0.920

[1.656]

[10.702]

Hih

ued

eide

Pot

0349

1752

Dep

ende

nt variable:                     

High rugg

edness in

dex x Po

st0.349

1.752

[0.940]

[6.738]

High std.de

v. elevatio

n x Po

st0.061

0.272

[0.942]

[6.954]

Mun

icipality

andyear

fixed

effects

YY

YY

YY

Mun

icipality and year fixed effe

cts

YY

YY

YY

Mean of dep

ende

nt variable (pre‐w

ar)

2.875

26.972

2.875

26.972

2.875

26.972

Mean of dep

ende

nt variable (post‐w

ar)

3.884

34.470

3.884

34.470

3.884

34.470

Num

ber o

f observatio

ns1824

1824

1824

1824

1824

1824

R‐squa

red

0.51

0.37

0.50

0.37

0.50

0.37

Stan

dard

errors,clustered

bymun

icipality

,are

inpa

rentheses.*s

ignifican

tat1

0%;**s

ignifican

tat5

%;***sign

ificant

at1%

.Th

issample

ofmun

icipalities

exclud

esBrčko,

andinclud

esim

putedpre‐war

values

that

aredistribu

tedfairly

betw

eenpa

rtition

edmun

icipalities.

Indicators

forh

ighcasualty

rate,h

ighrugg

edness

inde

x,an

dhigh

stan

dard

deviationin

elevation,

equa

lone

whenthemun

icipality‐le

vel

alue

eeed

the

eaCaua

ltyatei

eaued

bythe

ube

ofkilled

oi

ie

oe

aita

The

ued

eide

valueexceed

sthemean.

Casua

ltyrate

ismeasured

bythenu

mberof

killed

ormissing

person

spe

rcapita.Th

erugg

edness

inde

xap

proxim

ates

the

average

uphill

slop

ewhile

the

stan

dard

deviation

inelevation

measuresheterogeneity

inelevation

with

ina

mun

ici pality

. 

78

Finally, one could think of terrain ruggedness as being yet another confounding factor.

Specifically, partitioning a municipality with rugged terrain could be problematic; as well, ter-

rain ruggedness could conceivably constrain the siting of public schools. Therefore, the identi-

fying assumption could be violated. To address this concern, I conduct two sets of placebo tests

with indicators for high degree of terrain ruggedness. The first indicator is derived from the

terrain ruggedness index, which approximates the average uphill slope within a municipality

(Riley, DeGloria, and Elliot, 1999).26 The second indicator makes use of the standard deviation

in elevation, which measures the heterogeneity in elevation for a given municipality. Both in-

dicators take the value one when a municipality is more rugged than average. From columns

(10)-(13) of Table 2.7, we can see that none of the coefficients are statistically significant and all

of them are much smaller in magnitude when compared to the DID coefficients in Table 2.3.

Overall, results from the above placebo tests provide reassurance that my results on public

schooling are not picking up confounding effects. In particular, the DID coefficients are impre-

cisely estimated and, in general, have magnitudes far lower than those obtained from using

the indicator for partition. Therefore, we can conclude with reasonable confidence that the

partition effects on the provision of public schooling are not driven by confounding factors.

2.7.2 Mechanical Explanations

While I have argued for the partition effects being driven by homogeneity in preferences through

ethnic politics and elections, other mechanisms are also plausible. Specifically, the channel

through which the partition affects public schooling could be mechanical insofar as partitioned

municipalities face stronger incentives to build more public schools or provide more teachers.

Here, I discuss a couple of mechanical explanations that are observationally equivalent to what

I have presented so far, and note that while my empirical results suggest the importance of the

ethno-political mechanism, I cannot completely rule out the mechanical explanations either.

26The precise definition of the terrain ruggedness index is the root mean square of elevation differences of ageographical cell to its eight adjacent cells. Notably, it uses the root mean square instead of the arithmetic mean.For my purpose, I calculate the average terrain ruggedness index for all geographical cells within a municipality todetermine its ruggedness.

79

One mechanical explanation pertains to the issue of how pre-war schooling facilities were

allocated between pairs of partitioned municipalities. If an ethnic minority section is parti-

tioned with little or no schooling facilities, it may be forced to channel resources into build-

ing schools and recruiting teachers. This sort of mechanical effect may be due to an unequal

pre-war distribution of schooling facilities or simply an uneven partition. My earlier findings

indicate that the partition effects are remarkably robust to a variety of alternative imputations,

including the case where more pre-war schooling facilities are allocated to the ethnic minority.

This suggests that the pre-war distribution of schooling facilities may not be as problematic.

On the other hand, mechanical explanations that are driven by an uneven partition is harder

to rule out, especially since I do not have data on the pre-war location of public schools. How-

ever, if we were to speculate about the conditions under which this sort of mechanical effect

is most plausible, we could think of the (geographically) smallest partitioned municipalities as

being likely culprits. It turns out that, by repeating the DID regressions, removing partitioned

municipalities in the lowest quartile by geographical size, the partition effects remain robust

in terms of magnitude and statistical precision (results not shown). While these findings do

not formally rule out the mechanical story, they definitely seem to suggest that my results are

picking up something other than mechanical effects.

On a related note, partitioned municipalities could also be building more public schools

not because of the uneven partition, but because of a need to accommodate the remaining

ethnic minority who – as a result of the partition – face the undesirable option of attending

schools that are designed for the ethnic majority. This sort of mechanical effect, while being

strongly correlated with ethnic homogenization, operates via unobserved incentives that in-

fluence the provision of public schools. While the conjecture is plausible, one must note that

even though Bosnians prefer public schools that are ethnically oriented (OSCE, 2006), there is

little evidence to suggest that municipal governments are willing to fund schooling projects

that benefit the ethnic minority. Quite the opposite, not a single public school in RS provides

the curricula for Bosniaks or Croats, while public schools in the FBiH are void of the Serb cur-

80

riculum (Perry, 2003). Instead, to keep students of different ethnic groups apart, municipal

governments deliberately void their jurisdictions of ethnic minority schools, leaving ethnic mi-

nority children with little choice but to travel across jurisdictional boundaries to get to school

(Perry, 2003; OSCE, 2007). Nevertheless, I cannot rule out this mechanical story without school-

level data on the ethnic composition of students and precise measures of ethnically defined

syllabi.

2.7.3 Other Issues

Several issues remain. First, I examine the possibility of composition effects by including mu-

nicipality characteristics – population size, the share of the ethnic majority, and ethnic diversity

measures – as control variables in the DID regressions. The concern here is that compositional

changes in the population may be systematically different across partitioned and unpartitioned

municipalities, which may in turn be driving demand for public schooling. By controlling for

the aforementioned municipality characteristics, the effects of the partition on the provision of

public schooling should be over and above compositional determinants. Indeed, results from

columns (1)-(2) of Table 2.8 indicate that my results on the per capita number of public primary

schools and teachers are reasonably robust.

Next, as several municipalities – including Goražde, Drvar, Jajce, Kljuc, Kupres, Mrkon-

jic Grad, Petrovac and Šipovo, and parts of Sarajevo – were traded between the Serbs and

the Bosniak-Croat alliance during the negotiations at Dayton, the partitioning of these munic-

ipalities may not be exogenous. Thus, I remove them from the sample and repeat the DID

regressions of public schooling. From columns (3)-(4) of Table 2.8, we can see that the DID

coefficients on the per capita number of primary schools and teachers are 2.61 and 14.57 re-

spectively. Compared to the coefficients obtained with the full sample [columns (1) and (6) of

Table 2.3], these coefficients are quite similar in magnitude and precision. Therefore, the results

on public schooling are rather robust to the exclusion of these traded municipalities.

81

Table 2.8 ‐ Other Robustness Checks Pr

i. scho

ols 

perc

apita

Pri. scho

ol 

teachers per 

Pri. scho

ols 

perc

apita

Pri. scho

ol 

teachers per 

Rate of n

atural 

pop

chan

ge

Mun

icipal 

seats pe

r Dep

ende

ntvariable:

per c

apita

capita

per c

apita

capita

pop. cha

nge

capita

DID (1

)DID (2

)DID (3

)DID (4

)DID (5

)DID (6

)

Partition x Post

2.018*

13.013*

2.605*

14.569*

‐1.572*

78.745

[1.128]

[7.141]

[1.447]

[8.155]

[0.863]

[54.556]

Dep

ende

nt variable:                     

Mun

icipal cha

racteristics

YY

Mun

icipality and year fixed effe

cts

YY

YY

YY

Mean of dep

ende

nt variable (pre‐w

ar)

2.875

26.972

2.803

27.101

8.156

2.030

Meanof

depe

ndentv

ariable(postw

ar)

3884

34470

3862

34340

0955

30978

Mean of dep

ende

nt variable (post‐w

ar)

3.884

34.470

3.862

34.340

0.955

30.978

Num

ber o

f observatio

ns1824

1824

1569

1569

1747

1496

R‐squa

red

0.51

0.37

0.50

0.34

0.73

0.18

Stan

dard

errors,clustered

bymun

icipality

,are

inpa

rentheses.*s

ignifican

tat1

0%;**s

ignifican

tat5

%;***sign

ificant

at1%

.Thissampleof

mun

icipalities

yp

yp

gg

gp

pexclud

esBrčko,

andinclud

esim

putedpre‐war

values

that

aredistribu

tedfairly

betw

eenpa

rtition

edmun

icipalities.Th

erate

ofna

turalpo

pulatio

nchan

gerefers

tothe

thenu

mberof

births

minus

deaths

perthou

sand

.Mun

icipal

seatspe

rcapita

deno

testhenu

mberof

mun

icipal

seatsforevery

thou

sand

reside

ntsin

agivenmun

icipality

.Mun

icipal

characteristicsareinclud

edin

columns

(1)‐(2),c

omprisingpo

pulatio

nsize,sha

reof

theethn

icmajority

,and

ethn

icdiversity

measures.Th

efollo

wingmun

icipalities

areexclud

edin

columns

(3)‐(4):Gorazde

,Drvar,Jajce,K

ljuc,

Kup

res,Mrkon

jicGrad, Petrovac, Si pov

o, and parts of S

arajevo.

82

As the theoretical model implies, the diversion of resources towards ethnically oriented

public goods should also result in a corresponding decline in the provision of other universal

public goods. In other words, we should observe a lower provision of universal public goods

in partitioned municipalities, relative to unpartitioned municipalities. Given that health care

is plausibly non-discriminatory and is also a significant responsibility of the municipal gov-

ernment, I examine the effect of the partition on the provision of health care by repeating the

DID procedure using the rate of natural population change – the number of births minus infant

mortality and deaths per thousand – as a dependent variable. From column (5) of Table 2.8,

we can see that natural population outcomes are indeed worse in partitioned municipalities.

While changes in natural population may not be the best indicator for the provision of health

care, I take this as suggestive evidence that the results on public schooling are driven by re-

source allocation at the municipality level, rather than some other mechanism that ought to

have affected the provision of health care positively as well.

Finally, I address the possibility that distributive politics may cause an overspending bias

in federally financed projects that confer benefits on a targeted community, especially when

the number of jurisdictions increases (Weingast, Shepsle, and Johnsen, 1981; Baqir, 2002). As

Bosnia’s public schooling is federally financed and ethnically targeted, my results are subject

to the common-pool problem. To verify that the differential provision of public schooling is

not driven by an increase in the number of politicians from partitioned municipalities vying

for federal funds, I run a DID regression with the per capita number of municipal seats as

dependent variable, controlling for municipality and year fixed effects. From column (6) of

Table 2.8, we can see that, compared to the pre-war period, partitioned municipalities do not

seem to have more municipal seats per capita, relative to their unpartitioned counterparts. This

result suggests that even if the common-pool problem exists, it should not be the reason why

partitioned municipalities provide more public schooling.

83

2.8 Conclusions

In this study, I examine whether partitioning political jurisdictions – as a means towards end-

ing ethnic conflict – affect the provision of public goods. Specifically, I study the effect of the

IEBL on public schooling in post-war Bosnia, by exploiting possibly exogenous variation in the

incidence of municipal partition. Through the use of a difference-in-differences strategy and

alternative specifications, I find that partitioned municipalities, on average, provide 58 percent

more schools and 37 percent more teachers (per capita) than unpartitioned ones, controlling

for time-invariant municipal differences and aggregate shocks across municipalities. More-

over, I find that the increase in public schooling – in the form of ethnically oriented schools and

teachers that cater to the dominant ethnicity – only benefits children from the majority ethnic

group.

In addition, I find evidence which suggests that partitioned municipalities provide more

public schooling because the partition brought about ethnic homogenization, which makes

it easier for communities to attain ethnically oriented public goods through political means.

However, without access to school-level data, I cannot rule out mechanical explanations that

emerge due to unobserved incentives for partitioned municipalities to build more schools.

This paper makes two main contributions. Firstly, it is one of the first papers to empirically

establish the consequences of residing in partitioned jurisdictions in a post-conflict society; in

particular, it provides estimates of level and distribution effects. Secondly, it explores the role of

ethnic homogenization in the relationship between partition and public goods provision. The

findings of this paper will not only improve our understanding of how partitions affect the

lives of individuals after the conflict, but also of whether and how altering political boundaries

may influence economic recovery in conflict regions. That said, the results here speak only to

situations of ethnic conflict, and we should be careful about drawing inferences from this study

to answer ethnic diversity issues in a (relatively) peaceful context.

In conclusion, should warring ethnic groups be kept together or separate? While the find-

ings in this paper provide no affirmative answer, they certainly suggest that the ethnic major-

84

ity in partitioned regions benefits from a greater provision of public goods, while the ethnic

minority does not. This implies that ethnic minorities face strong obstacles in achieving post-

conflict economic recovery, and that partitioned regions may subsequently become more un-

equal. Given that ethnic inequality may potentially undermine the sustainability of peace in

the long run, policy makers ought to consider this particular implication should partitions be

proposed to resolve ethnic conflicts in the future.

85

Appendix

Table 2.A.1 ‐ Political Parties and Ideological Categorization

1990 1997 2000 2004

Bosnian‐Herzegovinian Patriotic Party BPS Yes Yes Yes BosniakDemocratic People’s Community DNZ Yes Yes Yes BosniakDemocratic Patriotic Party DPS Yes SerbDemocratic Party of Socialists DSS YesCitizenʹs Democratic Party GDS Yes Yes YesCroatian Democratic Union BiH HDZ Yes Yes Yes Yes CroatCroatian Christian Democratic Union HKDU Yes Yes CroatCroatian Peopleʹs Alliance BiH HNS BiH Yes CroatCroatian Natonal Union BiH*** HNZ Yes YesCroatian Party of Rights BiH HSP Yes Yes Yes CroatCroatian Peasant Party BiH*** HSS Yes YesCroatian Alliance HSS‐NHI*** HSS‐NHI YesCoalition HDZ‐HNZ‐DEM K HHD Yes Yes Yes CroatCoalition HDZ‐HKDU‐HSP K HHH Yes CroatLiberal Democratic Party LDS YesLiberal Civic Coalition LGK Yes YesMuslim Bosnian Organization MBO Yes Yes Yes BosniakNew Croatian Initiative*** NHI YesParty of Democratic Progress RS PDP Yes Yes SerbParty for BiH** SBiH Yes Yes Yes BosniakDemocratic Alliance BiH SCD BiH YesParty of Democratic Action SDA Yes Yes Yes Yes BosniakSerbian Democratic Party SDS Yes Yes Yes Yes SerbLeague of Communists ‐ Social Democratic Party SK‐SDP YesSerbian People’s Alliance RS SNS Yes Yes SerbUnion of Independent Social Democrats* SNSD Yes Yes YesSerbian Patriotic Party RS SPAS Yes Yes SerbSerbian Movement for Renewal SPO Yes SerbSocialist Party RS SPRS Yes Yes YesSerbian Radical Party RS**** SRS Yes Yes SerbAlliance of Reform Forces of Yugoslavia SRSJ YesSerbian Party of Krajina and Posavina SSKiP Yes SerbUnion of Bosnian‐Herzegiovinian Social Democrats UBSD YesUnited BiH List Z Lista YesDisplaced Serb Party Zavicaj Yes Yes

Electoral participationAbbre‐viation

Political party Ethno‐Nationalist

*Serb nationalist since 2006. **Nationalist by ideology but has a significant number of non‐Bosniak politicians. ***ExclusivelyCroat by membership, but have an agenda that pushes for constructive change. ****Banned by the OSCE from participating inthe 2000 elections, for openly opposing the Dayton peace process.

Chapter 3

Network Effects Among Migrants in the Labor Market: Evidence

from Thailand

3.1 Introduction

Social networks are extremely important in labor markets when information asymmetries are

significant. Often, individuals who are better connected can harness their social ties to gain

access to private information that will benefit them directly. In particular, the role of social

networks in providing information and job referrals is well-documented, as several authors

argue that established migrants – who have a better knowledge of the job market and job-

seekers – can help bridge the information gap between new migrants and potential employers

(Banerjee, 1991; Winters, de Janvry, and Sadoulet, 2001; Munshi, 2003).

While network effects are important, however, they are not easily identified empirically due

to endogeneity biases in the form of selection and simultaneity. Specifically, the self-selection

of individuals into destinations with large social networks may induce a selection bias, while

unobserved city shocks, when serially correlated, will be associated with network size and

cause a simultaneity bias.

My main contribution in this study is the use of heterogeneity in migration responses to

regional rainfall shocks – as exogenous variation affecting network size – to identify network

effects among migrants who have moved from the rural district of Nang Rong, Thailand, to

one of several urban destinations during the 1970–2000 period. Specifically, I propose the use

of the interaction between lagged annual rainfall and the village level proportion of net rice

producers as an instrument for the number of migrants at the destination city. In particular,

I find that higher rainfall induces an exogenous decrease in the flow of migrants, and that

86

87

these rainfall shocks have differential impact on villages with varying proportions of net rice

producers. A secondary contribution in this study is that I am able to estimate network effects

over small, closely-knit villages, in which one would expect social networks to be operational.

My empirical results suggest that networks are important in the job search process. In

particular, I estimate that a one standard deviation increase in the network size increases the

likelihood of finding a job within the first month of migration by approximately 9 percentage

points. Surprisingly, I also find that networks draw new migrants into the agricultural sector,

and I argue that this is because my estimates are essentially local average treatment effects that

are estimated off agricultural workers who are most affected by rainfall shocks. These results

are robust to a series of sensitivity checks.

The rest of this chapter is organized as follows. Section 3.2 constitutes a discussion on

social networks and migration. Section 3.3 provides an overview of the Nang Rong district

and a description of the data. I present the empirical difficulties in identifying network effects

and present my model in Section 3.4. Empirical analyses and robustness checks are laid out in

Sections 3.5 and 3.6 respectively. Section 3.7 concludes.

3.2 Social Networks And Migration

Why are social networks important to new migrants? In the context of rural-urban migra-

tion, individuals who contemplate on migrating care about employment opportunities, living

conditions and social support. However, they often face tremendous difficulties in acquiring

information about potential destinations, and this is where existing migrant networks can help

bridge the information gap.

In two separate articles on migration, Massey, Goldring, and Durand (1994) and Carrington,

Detragiache, and Vishwanath (1996) argue that new migrants often have to deal with high risks

and costs of migration, but as information about the destination grows and networks ramify,

future generations of migrants benefit from the support provided by earlier cohorts and hence

find it less costly to move. In addition, a study of Mexican migrants in the United States by

88

Winters, de Janvry, and Sadoulet (2001) concludes that when networks are (numerically) weak,

migration decisions are strongly influenced by household and individual attributes; however,

once networks are established, they become the single most important determinant of migra-

tion.

In fact, employers who want to hire new migrants may also depend on established mi-

grants for information. To the extent that employers seek the most capable migrants among

the “freshmen” but cannot observe their abilities and attributes, they often rely on existing

employees to help screen potential new hires and overcome the adverse selection problem

(Montgomery, 1991; Fernandez, Castilla, and Moore, 2000). In summary, social networks play

an important role in (i) providing job referrals and social support to new migrants and (ii)

helping potential migrants decide whether to move or not by passing on information (often by

word of mouth). The latter poses a problem to the econometrician because of self-selection into

social networks, an issue I will discuss at length in Section 3.4.

Given that social networks are important, how do we measure them? Authors such as

Aguilera and Massey (2003) and Curran, Garip, Chung, and Tangchonlatip (2005) suggest the

use of indices that capture (i) the closeness of social ties and (ii) the degree to which individuals

within the social network have previous migration experiences. This type of formulation is not

ideal for my purpose, as it favors strong ties (with family and close friends) over weak ties

(acquaintances). In fact, the “strength of weak ties” – a term coined by Granovetter (1973) –

is extremely relevant in the job search process, especially for those whose social positions are

relatively low (Lin and Dumin, 1986). Therefore, following Winters, de Janvry, and Sadoulet

(2001), Munshi (2003) and Korinek, Entwisle, and Jampaklay (2005), I focus on the quantity

dimension and use the stock of established migrants by origin village, destination city and

migration year – hereafter, network size – as the sole measure of social networks.

Finally, how do we measure the exact benefits of social networks? More often than not, new

migrants have a pressing need for employment and income, and it is likely that social networks

may be helpful to the process of job search (Banerjee, 1991). Indeed, in the only other study that

89

has a precise quantitative measure of migrant network effects, Munshi (2003) estimates that a

one standard deviation increase in the network size increases (i) the likelihood of employment

by 8 percentage points and (ii) the probability of working in the non-agricultural sector by 19

percentage points.1 These estimates, however, are based on networks that are defined over

large communities.2 In another paper, Aguilera and Massey (2003) find that networks may

increase the level of earnings from a migrant’s first job and the likelihood of finding a non-

agricultural job; however, the use of constructed network indices that measure both quantity

and quality forbids them from quantifying interpretable network effects. In this study, I will

explore two measures of employment outcome – job search duration and job type – and attempt

to identify interpretable network effects.

3.3 Background and Data

The area of study is the Nang Rong district in the Buriram province of Thailand. Nang Rong is

approximately 410 kilometers east of the capital, Bangkok, and is situated in a historically poor

northeast region of the country. Despite a decade of change and progress, including better road

networks and improved public transportation, Nang Rong remains relatively poor and rural.

Nang Rong occupies approximately 1,300 square kilometers of the province, and agricul-

tural production is by far the single most important source of income for its people, with rice

cultivation being the most popular activity, and cassava cultivation a distant second. This is not

surprising since rice is a critical crop for food security and a mainstay for the rural population.

Moreover, rice cultivation is not just a form of food production but a part of the Thai culture

– rice farming is often passed on from one generation to the next. Even though the Thai gov-

ernment has been actively promoting new farming methods, the technological adoption rate

1These are my estimates using IV results from Munshi (2003). My calculations are based on the following:the mean and standard deviation of the proportion of established migrants per community are 0.0631 and 0.0519respectively; and the coefficients of IV regressions on employment and non-agricultural occupation dummies are1.554 and 3.585 respectively. I will attempt to compare his estimates with mine in Section 3.5.

2Given that my network cells are village, city and year-specific, I have a tighter grasp of network effects thanMunshi (2003) because (i) the mean population of a village in my data is only around 600, which is significantlysmaller than that of a community in his data, and (ii) I examine multiple destinations at the city level while heexamines them at the state level in the United States.

90

remains extremely low in Nang Rong, with virtually all households relying on rainfall and only

15 percent using water pumps by the year 2000. Such over reliance on one crop and the lack

of sufficient knowledge and training prohibit farmers from adjusting their crop composition to

response to relative price changes (Sachchamarga and Williams, 2004).

Like most poor, technologically backward regions, Nang Rong stands in stark contrast to

her urban neighbors that experience a rapid pace of modernization and economic expansion.

Consequently, rural-urban migration becomes an important route to better employment op-

portunities for Nang Rong’s rural population. Indeed, figures from the Nang Rong Project

indicate that more than 10 percent of the entire district had migrated between 1984 and 2000.

In addition, job networks – both at the household and village level – are extremely important.

Interviews with Nang Rong villagers reveal tales of failed migrants who had returned home

without being paid for weeks of work or had lived in harsh conditions (Curran, Garip, Chung,

and Tangchonlatip, 2005). As a result, obtaining good information about jobs from friends and

family are critical in determining whether a migrant trip is actually worth undertaking.

3.3.1 Nang Rong Project

The empirical bases of this study are the Nang Rong surveys conducted by the Institute for

Population and Social Research, Mahidol University, and the Carolina Population Center, Uni-

versity of North Carolina in 1984, 1994 and 2000. The primary focus is on processes of migra-

tion, fertility decisions and life course choices within the context of rapid social and economic

change. Community and household census were conducted in the villages of Nang Rong, and

a migrant follow-up survey was added in 1994 and 2000 to track migrants who had migrated

to one of several popular urban destinations, including the capital city of Bangkok, the Eastern

Seaboard (which comprises of Rayong and Chonburi), the regional city of Korat (also known

as Nakhon Ratchasima) and the provincial city of Buriram.

The household data consists of 51 villages, 5,860 households and 34,035 individuals in 1984,

expanding to 92 villages, 8,638 households and 51,924 individuals in 2000. In particular, a sub-

91

set sample of 22 villages – selected randomly within strata created by cross-classifying gen-

eral location (quadrant) and distance from major paved roads in 1984 – has complete migrant

follow-up data, which includes the migrant’s life history, the extent of social support received

and her initial employment outcome at the destination. In particular, the migration history data

is retrospective and may be subject to reliability issues; nevertheless, as most survey respon-

dents are recent migrants (the modal average number of years since migration being seven),

the recall is perhaps not too demanding. Due to administrative splits in the zoning of villages,

the subset sample of villages increased from 22 in 1984 to 40 in 2000, although the geographical

target groups remained the same. The process of collecting migrant data is as follows. First,

the village and household surveys are conducted. Then, the survey coordinators assign inter-

viewers to track down migrants who (i) have migrated to one of several urban destinations

and (ii) belong to one of the selected villages. By this definition, roughly 14 percent of each

village’s population are classified as migrants. The attrition rate in the migrant survey due to

non-traceability was approximately 30 percent.

In particular, each migrant’s life history data allows me to match her migration year to her

initial employment outcome at the destination and construct the annual flow of migrants from

any of the selected villages to one of the urban destinations, stretching back to the year 1970.

As a result, I am able to obtain a repeated cross section of migrants by assigning each migrant

the network size that is specific to her village, destination city and migration year. In the event

that the individual is a return migrant, I only consider networks in the year of her last trip, so

as to be consistent with the employment outcome variables. I describe how I assign network

size to each migrant in Appendix Table 3.A.1. I also re-scale network size in multiples of 10 for

better exposition.

To gain a basic understanding of the data, I construct Table 3.1 to show the descriptive

statistics of individuals from the survey rounds of 1994 and 2000. Combining the two surveys,

there are 19,654 non-migrants who remain in Nang Rong and 2,150 migrants. Bangkok, being

the capital of the country, receives the highest proportion of migrants in both rounds of the

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survey. Columns (1) and (2) allow for a comparison between non-migrants and migrants while

the other columns provide a breakdown of the migrants by destination. For the purpose of this

study, I discard individuals aged 13 and below from the data as they are unlikely to migrate at

such a young age.

From Table 3.1, we see that migrants are more likely to be single and young, but equally

likely to be male or female. Their average school attainment is about six and a half years,

which is approximately one and a half years more than that of non-migrants in the data (or one

year more than that of non-migrants in comparable birth cohorts). The average network size

is around 12, with Bangkok and Korat offering the largest and smallest networks respectively.

More than three quarters of the migrants lived with family and friends during the transition

period, and received support in the form of free accommodation and help with job search from

fellow villagers. Such an astounding level of support further articulates the importance of

social networks in the Nang Rong villages.

93

Table 3.1 ‐ Descriptive Statistics (Individual)

All Bangkok Korat

(1) (2) (3) (4) (5) (6) (7)

Age 38.88 25.55 25.37 25.29 26.35 24.95 27.42

     (17.13) (5.81) (5.97) (5.73) (5.22) (5.53) (5.84)

Male 0.47 0.50 0.44 0.53 0.59 0.58 0.58

     (0.50) (0.50) (0.50) (0.50) (0.49) (0.50) (0.49)

Single 0.23 0.49 0.49 0.49 0.55 0.46 0.37

     (0.42) (0.50) (0.50) (0.50) (0.50) (0.50) (0.48)

School attainment 5.02 6.45 6.13 6.14 9.16 6.57 6.19

     (2.82) (3.31) (3.03) (2.98) (4.51) (3.25) (3.02)Network size (multiples of 10) 1.16 1.61 1.21 0.42 0.38 0.18     (1.16) (1.25) (1.11) (0.42) (0.39) (0.17)

Job offer prior to migration 0.55 0.60 0.48 0.53 0.59 0.55

Job within first month 0.90 0.90 0.93 0.80 0.92 0.92

Agricultural job 0.86 0.02 0.01 0.02 0.05 0.01 0.04

Agricultural background 0.84 0.88 0.87 0.90 0.81 0.91 0.84

Wages from first job 20.95 18.41 21.74 30.95 21.81 22.48

Number of siblings 4.41 4.34 4.28 4.39 4.18 4.16 4.86

Money received from home 1.98 2.16 1.65 2.63 1.75 1.69

Money sent home 4.02 4.05 3.92 4.33 4.02 3.87

Moved with family/friends 0.59 0.61 0.55 0.67 0.54 0.57

Lived with family/friends 0.78 0.78 0.81 0.73 0.71 0.75

Received support 0.75 0.76 0.79 0.68 0.70 0.72

Migration year 1988 1988 1993 1984 1993 1986

Observations (1994 survey) 9071 1151 504 343 112 97 95Observations (2000 survey) 10583 1128 500 354 97 106 71Number of observations 19654 2279 1004 697 209 203 166

Standard deviations in parentheses. Means are shown for age, school attainment, network size, wages from first job,number of siblings and money received/sent; modes are shown for migration year; all other figures correspond tobinary variables and refer to the proportion of one. Network size refers to the year/origin/destination‐specific numberof established migrants. Wages are measured in Thai baht per hour and deflated by consumer price indices using 2000as the base year. Money sent or received is measured in Thai baht and coded in six intervals: 1:[1,1000], 2:[1001,3000],3:[3001,5000], 4:[5001,10000], 5:[10001‐20000], 6: [20001,∞). 1,000 baht equals approximately 25 US Dollars. Migrantʹsagricultural background is derived from her village familyʹs occupation. Due to thin cells, I combine Rayong andChonburi to form the Eastern Seaboard.

Eastern Seaboard

Other Province

Non‐migrants

Migrants (by destination)Buriram City

 27

94

At this point, a couple of key dependent variables warrant an elaborate description. “Job

within first month” is a binary variable which equals one if the migrant manages to find a

job within the first month of migration, zero otherwise. “Agricultural job” is a dummy that

equals one if the migrant is employed in the agricultural sector, and zero otherwise. Data for

these variables are incomplete due to non-response, and I will address this issue in Section

3.6. In this sample, 90 percent of migrants find jobs within the first month of migration, with

little variation across destinations. Even though 88 percent of migrants have an agricultural

background, only 2 percent of them work in the agricultural sector, suggesting the presence

of cross-sector mobility. In particular, more than half of the migrants find employment in the

public sector or become craft workers and laborers. Differences in occupation by location of mi-

grants are evident. Bangkok and the Eastern Seaboard offer less agricultural opportunities than

the provincial city of Buriram and Korat. As a rule of thumb, destinations that are closer Nang

Rong have larger agricultural sectors. This mirrors the anecdotal evidence on the geographical

distribution of occupations – craft workers and laborers are known to be the dominant occu-

pations for migrants in Bangkok and the Eastern Seaboard while agricultural jobs are more

abundant in the regional growth centers.

3.3.2 Other Data

Since the Nang Rong surveys do not include household rice production data, I use information

from the Townsend Project of Thailand to estimate rice production for each Nang Rong house-

hold. Although the two data sets are entirely separate, I exploit the fact that the Townsend

Project provides data on the province of Buriram – in which the Nang Rong district is situated

– to match households across the two data sets.3

I first use rice production and consumption data in the Townsend Project to determine

3The Townsend Project provides household microeconomic data for the years 1997, 1998 and 1999, with anaverage response rate of 96 percent in the latter years. The survey covers 2,880 households across four provinces –Chachoengsao, Lopburi, Sisaket and Buriram – and many of the household level variables resemble those reportedin the Nang Rong surveys. In fact, by comparing agricultural variables such as the number of tractors, buffalos andcultivation plots, I find that Nang Rong households are not that different from their counterparts in other Buriramdistricts, so the use of Townsend data to proximate rice production in Nang Rong appears to be reasonable.

95

whether each household is a net producer of rice. Then, I run a logistic regression of net rice

production on several household-level variables, and use the coefficients to predict net rice

production for Nang Rong households.4 Finally, I construct the village proportion of net rice

producers by averaging the household rice production statuses within each village (descriptive

statistics are shown in Table 3.2).

Apart from the Nang Rong and Townsend data, I use annual rainfall data from the Thailand

Meteorological Office that covers all years starting 1970 and is measured in meters of rain and

the number of rainy days. In this study, I use meters of rain as it is a finer measure of rainfall

than the number of rainy days. Unfortunately, as there is only one weather station in Nang

Rong, we only have rainfall variation over time, not villages. This turns out to be an issue in

the estimation of year effects which I will address later on.

4I use the following household-level variables to predict rice production: age, sex, marital status and school-ing attainment of the head of household; ownership of assets like TV, VCR, air conditioner, washing machine,telephone, refrigerator, bicycle, motorcycle, car, truck, farm tractors, farm animals and the size and number of cul-tivation plots. The logistic regression results suggest that the ownership of tractors and buffalos, as well as thenumber and size of cultivation plots, are good predictors of rice production. These provide us with some confi-dence that the logistic regression is predicting rice production correctly. In addition, I compute the goodness-of-fitby using the following procedure. For each household in the Townsend Project, I adjust the predicted net rice pro-duction propensity to unity if it is more than 0.5; if it is no more than 0.5, it is adjusted to zero. It turns out that thegoodness-of-fit (based on the proportion of correct predictions, weighted by the proportion of net rice producers)is around 70 percent. Notably, my estimates are also robust to alternative polynomial specifications.

96

Table 3.2 ‐ Descriptive Statistics (Village)

(1) 514 75 0.15 1991 0.69 2.39

(2) 528 79 0.15 1991 0.59 1.79

(3) 528 41 0.08 1987 0.51 1.76

(4) 620 45 0.07 1991 0.57 1.88

(5) 650 55 0.08 1986 0.66 1.91

(6) 434 32 0.07 1987 0.61 1.96

(7) 456 39 0.09 1993 0.69 3.05

(8) 537 34 0.06 1994 0.68 2.70

(9) 633 53 0.08 1991 0.68 2.59

(10) 556 73 0.13 1989 0.69 2.34

(11) 300 38 0.13 1990 0.60 1.83

(12) 530 38 0.07 1996 0.60 1.84

(13) 418 10 0.02 1993 0.65 1.87

(14) 534 22 0.04 1994 0.67 2.32

(15) 611 103 0.17 1989 0.53 1.72

(16) 660 65 0.10 1991 0.60 2.01

(17) 782 84 0.11 1989 0.58 1.87

(18) 388 23 0.06 1986 0.65 2.33

(19) 604 49 0.08 1992 0.61 2.08

(20) 704 47 0.07 1995 0.66 2.20

(21) 471 54 0.11 1996 0.56 1.66

(22) 833 69 0.08 1993 0.65 2.50

Average 559 51 0.09 1991 0.62 2.12

These 22 sample villages were selected randomly within strata created by cross‐classifying generallocation (quadrant) and distance from major paved roads in 1984. The population and number ofmigrants include individuals 13 years or older only. All the statistics shown here are taken from thesurvey conducted in 2000. The ʺaverageʺmode year of migration shown above is in fact the mode year ofmigration across all 22 villages.

Proportion     of net rice producers

Mean number of plots 

cultivated

Migration rate

Village ID

Population size

Number of migrants

Mode year of migration

 28

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3.4 Identifying Network Effects

In this section, I discuss the common problems in estimating network effects and present a

method to overcome those difficulties. Consider a model in which individuals choose between

staying in the village and migrating to the cities by comparing their employment outcome at

both locations. The city outcome equation, conditional on migration, is as follows:

ocivct = Xivctβ

c + θmvct−1 + φyct + δcωiv + εcivct (3.1)

where ocivct represents the employment outcome of individual i who moved from village v to

city c in year t; Xivct denotes the vector of exogenous individual characteristics; mvct−1 is the

existing network size in city c as of year t− 1; yct represents city-year effects; and ωiv measures

the time-invariant unobserved characteristics of i. In particular, ωiv is unobserved and we are

interested in the consistent estimation of coefficient θ which measures the network effects.5

On the other hand, conditional on non-migration, village outcome is a function of individ-

ual attributes (observed and unobserved) and annual rainfall rvt:

ovivt = Xivtβ

v + ψrvt + δvωiv + εvivt (3.2)

The individual’s migration decision is based on relative outcomes. In particular, I assume a

migration equation that is linear in the difference between city and village outcomes:

mivct = ocivct − ov

ivt

= Xivctβc − Xivtβ

v + θmvct−1 + φyct − ψrvt + (δc − δv)ωiv + εcivct − εv

ivt (3.3)

Since counterfactuals for migrants are unobservable – we know their city outcomes but not

village outcomes – several identification problems arise. Firstly, an exogenous increase in net-

5By using these subscripts to denote individual, space and time, I do not attempt to describe a longitudinal datasetting, but rather to provide a clearer exposition of the model. In fact, as explained in the previous section, what Ihave is effectively a repeated cross section.

98

work size improves city outcome, so individuals will sort themselves (by destination and year)

into cities with large networks, other things being equal. Suppose that the unobserved individ-

ual characteristic ωiv in question is ability, then an increase in network size reduces the ability

threshold, attracting migrants with lower ability.6 If δc > δv, then the estimate of θ will be

biased downwards.7

In fact, ωiv is not the only potential unobserved variable. We can think of labor supply

and demand factors that matter if some villages systematically yield more migrants or some

cities are naturally more attractive than others. Particular years may also be more conducive

for rural-urban migration for reasons we cannot observe. In short, village-specific, city-specific

and year-specific effects are also potentially correlated with network size.

Another common source of bias stems from the correlation between unobserved city-year

shock and network size. Suppose yct is serially correlated such that:

yct = λyct−1 + εct (3.4)

where the sign of λ denotes the direction of serial correlation. Then, an increase in the city-

year effect, which increases network size, is also associated with an increase or decrease in the

following year’s city-year effect. In this case, the estimation of θ will yield a positive or negative

simultaneity bias depending directly on the sign of λ.8

We need to eliminate all sources of bias to identify network effects. To circumvent the si-

multaneity bias, a natural solution is to include city-year effects in the ordinary least squares

(OLS) regression of equation (3.1). In addition, I suggest an even tighter specification by using

lagged annual rainfall rvt−1 as an exogenous variation to instrument for network size, sidestep-

6Here, I describe a unidirectional selection story in which individuals at the lower end of the ability distributionare affected at the margin. An alternative story of selection at both ends of the distribution could also be true if lowability individuals are credit-constrained and high ability individuals find migration unattractive (McKenzie andRapoport, 2007).

7To see that mvct−1 and ωiv are negatively correlated, rearrange equation (3.3) to get cov(mvct−1, ωiv) =−(δc−δv)

θ σ2ω . Then, derive the negative bias by computing plim(θ − θ) = − δc(δc−δv)

θσ2

ω

σ2m

< 0 if δc > δv.8To see the correlation between mvct−1 and yct, take the village average of equation (3.3) to get

cov(mvct−1, yct−1) = φσ2y . Then, by substituting equation (3.4) into equation (3.1), we can obtain plim(θ − θ) =

φ2λσ2

y

σ2m

≷ 0 if λ ≷ 0.

99

ping any unobserved factor that may influence both outcome and network size.9 By taking the

village average of equation (3.3), it becomes immediately clear that rvt−1 is negatively corre-

lated to mvct−1 and thus satisfies the partial correlation condition. This result is very intuitive

because rainfall affects village outcome positively – especially when agricultural production is

an important source of village income – and should thus be a significant deterrent of migration.

As well, rvt−1 must satisfy the exclusion restriction E(rvt−1|yct, ωiv, εcivct) = 0. In this case, we

need villages to be reasonably far away from the cities, and that destination cities have little

agricultural activity that may depend on rainfall. If mvct−1(rvt−1) is the instrumented network

size, the instrumental variable (IV) regression is as follows:

ocivct = Xivctβ

c + θmvct−1(rvt−1) + φyct + δcωiv + εcivct (3.5)

Notably, since city outcomes are conditional on migration, the error term εcivct in equation

(3.5) is also conditional on mivct [and thus, on rainfall rvt, according to equation (3.3)]. As

such, if rainfall is serially correlated, mvct−1(rvt−1) will not be exogenous to εcivct, so I should

also include year fixed effects to circumvent the potential problem.10 At this point, I should

point out the limitation that there is only one rainfall station in Nang Rong which leaves me

with rainfall variation across years but not across villages. Consequently, year effects cannot

be identified from the estimation equation because rainfall and year dummies are perfectly

collinear. To get around this problem, I need an instrument that exhibits variation across vil-

lages. Specifically, I propose using the interaction of lagged annual rainfall rt−1 with the village

proportion of net rice producers pv – hereafter, the interaction instrument – as an instrument

for network size. This interaction instrument satisfies the partial correlation condition when

cov(rt−1 pv, mvct−1) 6= 0. If villages with a higher proportion of rice producers are more depen-

dent on rainfall, then the covariance term is negative; if villages with a lower proportion of

9Rainfall has been widely used as an exogenous variation in the empirical literature since its inception by Paxson(1992), who used it to estimate transitory income.

10In fact, I find no evidence of any serial correlation in rainfall. By regressing annual rainfall on lagged rainfall ofup to 10 years, I find that no individual lag is statistically correlated to contemporaneous rainfall, and that lags arenot jointly significant either.

100

net rice producers – and thus a larger pool of seasonal laborers – are more adversely affected

by low rainfall, then the covariance term is positive. In addition, if the proportion of net rice

producers is uncorrelated to city-year shocks as well as unobserved individual characteristics,

the exclusion restriction E(rt−1 pv|yct, ωiv, εcivct) = 0 is satisfied.11 The augmented IV regression

is:

ocivct = Xivctβ

c + θmvct−1(rt−1 pv) + φyct + δcωiv + εcivct (3.6)

So far, what are the threats to the validity of the instruments I employ? For lagged annual rain-

fall, it is relatively straightforward – we are concerned if lagged rainfall is correlated with (i)

unobserved individual characteristics or (ii) city-year shocks. In the first case, the instrument

becomes problematic if migrants select by some unobserved characteristic; as well, it becomes

clear that my IV strategy cannot deal with the selection bias. As for the second case, Buri-

ram city is of particular concern because it is within 200 kilometers of Nang Rong and may

experience similar weather patterns, and has a substantial agricultural sector that may depend

on rainfall. I will deal with this issue in the next section by excluding Buriram city from the

sample.

The validity of village level proportion of net rice producers is slightly more complicated.

One threat to validity may be that the proportion of net rice producers may be correlated to

other unobservable village attributes that may affect city outcomes. This issue can be resolved

by controlling for village effects, which will be able to capture village level unobservables. In

terms of the strength of the instrument, if households respond to rainfall shocks by substitut-

ing their production away from rice to other crops that do not depend on rainfall, then the

proportion of net rice producers will be a weak instrument. However, this is probably not the

case as Sachchamarga and Williams (2004) argue that farm households are unresponsive due to

over-reliance on rice and the lack of sufficient knowledge to switch to other crops. Anecdotal

11I run IV regressions of school attainment on the village proportion of net rice producers, among other controls,and find that they are uncorrelated. To the extent that school attainment is a reasonable proxy for unobservedability, this provides support for the exclusion restriction.

101

evidence also suggests that Thai farm gate prices are reasonably stable owing to government

intervention, so rainfall variation should not affect rice consumers via price changes.12

To deal with the selection bias, an ideal solution would be to control for individual fixed

effects. To this end, I can run an individual fixed effects regression for a sub-sample of villagers

who are reported to be “migrants” in both surveys (1994 and 2000). However, this selected

group is hardly representative of all migrants, as return migrants are likely to be better users

of networks on average.13 Therefore, I will use the augmented IV model and conduct ancillary

tests for the absence of self-selection (see Section 3.6).

3.5 Empirical Analysis

Following the model discussed above, I perform the empirical analyses on the Nang Rong data

to identify network effects among the rural-urban migrants. I will first examine the instruments

and then go on to present the OLS and IV regression results. Standard errors are clustered

by year since aggregate annual rainfall provides very limited variation to identify network

effects.14

3.5.1 Examining Instruments

First of all, how many lags of rainfall should I use for my instruments? The existing litera-

ture suggests that established migrants provide a combination of information and trust, and

are thus relevant components in migrant networks (Munshi, 2003; Curran, Garip, Chung, and

12The Thai government supports rice producer prices through large-scale market intervention programs, basedon the paddy pledging scheme, operated by the Bank for Agriculture and Agricultural Co-operatives (BAAC), incollaboration with the Public Warehouse Organization (PWO) and the Marketing Organization for Farmers (MOF).As a result, rice is one of the few commodities that are subjected to market stabilization measures, and farm gateprices – what farmers receive for their produce at the location of the farm or the first point of sale – are evidentlystable, according to price data from the Association of Southeast Asian Nations (ASEAN) Food Security InformationSystem. Using the community surveys from the Nang Rong data, I also find that the price of rice per kilogramremains extremely stable at approximately 260 baht in 1994 and 2000.

13In fact, when I run these fixed effects regressions, I find that the estimated network effects are larger than theirIV counterparts, which suggests that the sub-sample of return migrants are indeed better users of networks, orthat there is negative selection at the individual level. Unfortunately, I cannot empirically distinguish one from theother.

14Following the suggestion of a referee, I also tried to block-bootstrap the standard errors of the coefficients ofthe interaction instruments (in the reduced-form and first-stage regressions), but find that it does not substantiallyalter the statistical significance of the interaction instruments.

102

Tangchonlatip, 2005), but it falls short of providing a precise cutoff for migrants to be con-

sidered “established”. In this study, I choose five lags of rainfall for my instruments as they

prove to be most empirically significant in influencing network size.15 In addition, I will also

demonstrate the robustness of my results by changing the number of lags in Section 3.6.3.

Next, valid instruments need to satisfy both the partial correlation condition as well as the

exclusion restriction. While it is empirically impossible to examine the exclusion restriction, I

argue that rainfall shocks are invariably exogenous so the restriction is automatically satisfied

for both (i) lagged rainfall and (ii) the interaction (of lagged rainfall and the village proportion

of net rice producers) instrument.

To examine the partial correlation condition, I first take two candidate measures of employ-

ment outcome: “Job within first month” and “Agricultural job” and regress them separately

on the two instruments, where each instrument includes five lagged periods (Table 3.3). For

instance, in the case of lagged annual rainfall, I use annual rainfall in year t, t− 1, t− 2, t− 3,

t− 4, and t− 5 where t refers to the year of migration. In each reduced-form regression, I also

control for the migrant’s age, gender, and school attainment, as well as village and city fixed

effects. City-year fixed effects are included when appropriate.

15To select the optimal number of lags, I begin with six lags of rainfall – a natural benchmark, following Munshi(2003) – before experimenting with varying numbers of lags. In each case, I note the first-stage statistical significanceof all rainfall lags and conduct the weak instrument test (Stock and Yogo, 2005). By comparing these first-stageresults, I find the optimal choice to be five lags, in which case all rainfall lags are highly significant (jointly andindividually), and the partial F-statistic is large, passing the weak instrument test (at 5% maximal IV bias). In fact,I find that the coefficient of network size in the second stage is rather robust to using six lags, but the first-stageresults are much weaker.

103

Table 3.3 ‐ Reduced‐Form Regressions

Dependent variable:

(1) (2) (3) (4)

Annual rainfall   (t) 0.007 0.032[0.027] [0.030]

Annual rainfall (t‐1) ‐0.038 ‐0.014[0.032] [0.013]

Annual rainfall (t‐2) 0.002 ‐0.007[0.018] [0.010]

Annual rainfall (t‐3) ‐0.047** 0.010[0.022] [0.017]

Annual rainfall (t‐4) ‐0.031 0.014[0.025] [0.011]

Annual rainfall (t‐5) ‐0.004 ‐0.024[0.023] [0.019]

Annual rainfall  (t)     x Village prop. of rice producers ‐0.348 ‐0.530[0.470] [0.599]

Annual rainfall (t‐1)   x Village prop. of rice producers 0.701* ‐0.308[0.347] [0.303]

Annual rainfall (t‐2)   x Village prop. of rice producers 1.097*** 0.891**[0.286] [0.259]

Annual rainfall (t‐3)   x Village prop. of rice producers 0.333 1.058**[0.537] [0.325]

Annual rainfall (t‐4)   x Village prop. of rice producers ‐0.561 0.278[0.456] [0.209]

Annual rainfall (t‐5)   x Village prop. of rice producers 0.327 ‐0.116[0.339] [0.416]

Partial F‐statistic 1.15 3.70 2.31 5.26[p‐value] [0.363] [0.009] [0.066] [0.001]

Migrant controls & village fixed effects Yes Yes Yes YesCity fixed effects Yes No Yes NoCity‐year fixed effects No Yes No YesNumber of observations 2279 2279 2279 2279R 2 0.07 0.12 0.04 0.13

Job within first month Agricultural job

Clustered standard errors in parentheses. * significant at 10%; ** significant at 5%; *** significant at 1%. The partial F‐statistics reflect the joint significance of the candidate instruments. ʺJob within first monthʺ = 1 if the migrant finds a jobwithin the first month of migration; 0 otherwise. ʺAgricultural jobʺ = 1 if the migrant is employed in the agricultural sectorat destination; 0 otherwise. Period t refers to the year of migration. Migrant controls include age, gender, and schoolattainment. 

 29

104

The odd-numbered columns show the reduced-form coefficients for lagged annual rain-

fall while the even-numbered columns show the coefficients for the interaction instrument.

Although individual lags are not always statistically significant, all lags of the interaction in-

strument are jointly significant at 1 percent. In those cases where the coefficients are significant,

they are negative in the odd-numbered columns and positive in even-numbered columns, sug-

gesting that rainfall may be affecting network size negatively and villages with lower propor-

tion of net rice producers are more adversely affected by low rainfall.

Next, we turn to the reduced-form regressions of network size on the instruments. Since

these are essentially first-stage regressions in the IV procedure, I report them with the OLS and

IV results, in the bottom panel of Table 3.4. In column (4), I instrument network size by using

lagged annual rainfall, which turns out to be a reasonably strong instrument with a first-stage

partial F-statistic of 11. In addition, all five lags of rainfall are negatively correlated to network

size, suggesting that higher rainfall discourages migration. As expected, rainfall in migration

year has no effect on network size.

While the first-stage results in column (4) are encouraging, collinearity between annual

rainfall and year dummies forbids the identification of year fixed effects. Thus, I introduce the

interaction instrument in columns (5), under which city-year fixed effects are included. No-

tice that the coefficients of all five lags of the interaction instrument are positively correlated

to network size, confirming the reduced-form results – that villages with a lower proportion

of rice producers are more adversely affected by low rainfall. In this specification, the partial

F-statistic has risen to 18.39, which implies that the interaction instrument passes the weak in-

strument test at around 5 percent maximal IV bias (Stock and Yogo, 2005).

105

Table 3.4 ‐ OLS & IV Regressions (Job Search)

OLS & IV RegressionsOLS (1) OLS (2) OLS (3) IV (4) IV (5)

Network size (multiples of 10) 0.007 0.001 0.011 0.021 0.079***[0.006] [0.006] [0.010] [0.013] [0.029]

Migrant controls & village fixed effects No Yes Yes Yes YesCity fixed effects No Yes No Yes NoCity‐year fixed effects No No Yes No Yes

First stage partial F‐statistic 11.00 18.39[p‐value] [0.000] [0.000]Mean of dependent variable 0.902 0.902 0.902 0.902 0.902

Number of observations 2279 2279 2279 2279 2279

First Stage Regressions

Instrument   (t) 0.046 ‐1.748[0.345] [2.097]

Instrument (t‐1) ‐0.766*** 4.346***[0.250] [0.914]

Instrument (t‐2) ‐0.685** 4.889***[0.295] [1.165]

Instrument (t‐3) ‐1.055*** 5.041**[0.357] [2.001]

Instrument (t‐4) ‐1.409*** 4.141**[0.319] [1.504]

Instrument (t‐5) ‐1.346*** 6.691***[0.325] [1.541]

Number of observations 2279 2279R 2 0.58 0.75

Dependent variable: Job within first month

Dependent variable: Network size

Clustered standard errors in parentheses. * significant at 10%; ** significant at 5%; *** significant at 1%. ʺJob withinfirst monthʺ = 1 if the migrant finds a job within the first month of migration; 0 otherwise. The IV regression incolumn (4) uses lagged rainfall as an instrument for network size. The IV regression in column (5) uses theinteraction of rainfall and the predicted proportion of net rice producers as an instrument. Migrant controls includeage, gender, and school attainment. In this sample, the mean and standard deviation of network size are both 1.16.

 30

106

To get a alternative perspective of the relationship between network size and the instru-

ments, I also plot the line-of-best-fit diagrams to show the correlation between them (see Fig-

ures 3.1 and 3.2). These diagrams suggest that (i) migration is higher in years of low rainfall

and (ii) migrants are more likely to come from villages with a lower proportion of net rice pro-

ducers, which are consistent with the signs of the first-stage coefficients. Having established

the fact that the instruments satisfy the partial correlation condition, I will now proceed with

the IV regressions to identify network effects.

Figure 3.1 ‐ Fitted Regression of Migration on Rainfall

Figure 3.2 ‐ Fitted Regression of Migration on Village Rice Production

19701971 19721973

19741975 19761977

19781979 198019811982 1983

1984

19851986

19871988

1989 1990

1991

1992

1993

1994

1995

19961997 1998

1999

2000050

100

150

Num

ber o

f mig

rant

s

.8 1 1.2 1.4 1.6 1.8Annual rainfall (metres)

Based on migration data 1970-2000. Correlation coefficient is -0.442 (p=0.0127).Fitted regression with 95% confidence interval shown, with observations weighted by the number of migrants.

Migration & Rainfall

2550

7510

012

515

0N

umbe

r of m

igra

nts

.5 .55 .6 .65 .7Village proportion of net rice producers

Based on migration data 1970-2000. Correlation coefficient is -0.2207 (p=0.3237).Fitted regression with 95% confidence interval shown, with observations weighted by the number of villagers.

Migration & Village Rice Production

 33

107

Figure 3.2 ‐ Fitted Regression of Migration on Village Rice Production

125

150

s

Migration & Village Rice Production

 34

7510

012

515

0N

umbe

r of m

igra

nts

Migration & Village Rice Production

2550

7510

012

515

0N

umbe

r of m

igra

nts

.5 .55 .6 .65 .7Village proportion of net rice producers

Based on migration data 1970-2000. Correlation coefficient is -0.2207 (p=0.3237).Fitted regression with 95% confidence interval shown, with observations weighted by the number of villagers.

Migration & Village Rice Production

2550

7510

012

515

0N

umbe

r of m

igra

nts

.5 .55 .6 .65 .7Village proportion of net rice producers

Based on migration data 1970-2000. Correlation coefficient is -0.2207 (p=0.3237).Fitted regression with 95% confidence interval shown, with observations weighted by the number of villagers.

Migration & Village Rice Production

 34

3.5.2 Instrumental Variables Regressions

I first consider the network effects on job search by looking at the relationship between the

probability of finding a job (within the first month of migration) and network size. The first

three columns in the top panel of Table 3.4 show the OLS estimates under varying sets of con-

trols, with column (3) being the preferred OLS specification which includes all available con-

trols. Although the coefficients of network size are positive, they are statistically insignificant.

By and large, these OLS estimates suggest little evidence of network effects.

Columns (4) and (5) in the top panel of Table 3.4 show the IV results by using the two

instruments discussed in Section 3.5.1. Estimates from column (4) suggest that there are no

network effects on the probability of finding a job when lagged rainfall is used to instrument

for network size, although this specification is seriously undermined by the fact that city-year

effects are omitted. Indeed, when I employ the interaction instrument and am able to include

city-year dummies, network effects turn out to be positive and statistically significant, and are

108

substantially larger than their OLS counterparts (0.079, as compared to 0.011), indicating either

(or both) of the following: (i) the presence of negative serial correlation in city-year shocks

that biases the OLS network effects downwards, and (ii) network size suffers from classical

measurement error (that biases network effects towards zero).16

Given that network effects on job search are positive, how do we interpret them? One way

to quantify the result is to say that a one standard deviation increase in the network size –

which is around 11.6 migrants in this sample – increases a migrant’s probability of finding a

job within the first month by around 9 percentage points (or 10 percent at the mean probability

of all migrants). Although it is impossible to say whether this estimate is reasonable, I find my

estimate to be rather similar to that of Munshi (2003) – that a one standard deviation increase

in the network size increases the likelihood of employment by 8 percentage points. In fact,

since Munshi (2003) uses “employment” rather than “employment within the first month of

migration”, the benefits of social networks are less salient in Munshi’s measure, so it is not

surprising that my network effects are larger.

Next, I examine network effects on job type. Using the agricultural job dummy as a proxy

for job type, one should expect to find that networks help new migrants enter the more attrac-

tive sector (agricultural or non-agricultural). The OLS estimates are presented in the first three

columns of Table 3.5 (top panel) and they show that network effects are non-existent, a result

which remains unchanged even when I use lagged rainfall to instrument for network size in

column (4). However, once I use the interaction instrument in column (5), the network effects

become positive and statistically significant.

16In fact, under comparable specifications – columns (2) and (4), and columns (3) and (5) – the IV estimates arestrictly larger than the OLS ones, and this result does not change even when village-year fixed effects are included(not shown). That said, one should note that the instruments only correct for classical measurement error in networksize, insofar as rainfall influences migration, but remains uncorrelated with the extent of any mismeasurement ofmigration.

109

Table 3.5 ‐ OLS & IV Regressions (Job Type)

OLS & IV RegressionsOLS (1) OLS (2) OLS (3) IV (4) IV (5)

Network size (multiples of 10) ‐0.003 0.004 0.006 0.000 0.069**[0.003] [0.003] [0.007] [0.007] [0.033]

Migrant controls & village fixed effects No Yes Yes Yes YesCity fixed effects No Yes No Yes NoCity‐year fixed effects No No Yes No Yes

First stage partial F‐statistic 11.00 18.39[p‐value] [0.000] [0.000]Mean of dependent variable 0.022 0.022 0.022 0.022 0.022Number of observations 2279 2279 2279 2279 2279

First Stage Regressions

Instrument   (t) 0.046 ‐1.748[0.345] [2.097]

Instrument (t‐1) ‐0.766*** 4.346***[0.250] [0.914]

Instrument (t‐2) ‐0.685** 4.889***[0.295] [1.165]

Instrument (t‐3) ‐1.055*** 5.041**[0.357] [2.001]

Instrument (t‐4) ‐1.409*** 4.141**[0.319] [1.504]

Instrument (t‐5) ‐1.346*** 6.691***[0.325] [1.541]

Number of observations 2279 2279R 2 0.58 0.75

Dependent variable: Agricultural job

Dependent variable: Network size

Clustered standard errors in parentheses. * significant at 10%; ** significant at 5%; *** significant at 1%.ʺAgricultural jobʺ = 1 if the migrant is employed in the agricultural sector at destination; 0 otherwise. The IVregression in column (4) uses lagged rainfall as an instrument for network size. The IV regression in column (5)uses the interaction of rainfall and the predicted proportion of net rice producers as an instrument. Migrantcontrols include age, gender, and school attainment. In this sample, the mean and standard deviation of networksize are both 1.16.

 31

110

In this case, positive network effects imply that a larger network size increases a migrant’s

likelihood of being employed in the agricultural sector. This stands in stark contrast to the

findings of several authors, including Aguilera and Massey (2003) and Munshi (2003), who

find that networks help migrants enter the higher-paying non-agricultural sector.17 Why then,

do I find positive network effects on being employed in the agricultural sector?

First of all, network effects on agricultural employment could be positive simply because

agricultural jobs are more attractive. I test this claim by repeating the IV procedure using wages

as the employment outcome but find no significant network effects.18 In fact, wages between

agricultural and non-agricultural jobs do not even seem to differ significantly.19 Secondly, it

could be the case that the capability of networks is higher in the agricultural sector. However,

the data tells us that 76 percent of non-agricultural workers receive help in finding a job while

the corresponding figure for agricultural workers is only 71 percent, so this explanation is far

from convincing.

Finally, the most compelling hypothesis lies in a well-known interpretation of IV estima-

tors – the local average treatment effect (LATE) – as articulated by Imbens and Angrist (1994).

Having instrumented networks using rainfall, I have inevitably estimated networks from the

segment of the population that is most affected by rainfall shocks, that is, the seasonal agri-

cultural workers, who are more likely to be working in agriculture. Consequently, it is not

surprising that these networks lure new migrants into the agricultural sector. Furthermore,

there is indirect evidence to support the LATE interpretation, as cohorts that move when there

is a decline in rainfall, tend to include a greater proportion of migrants with agricultural back-

ground (Figure 3.3).

17In fact, I find that a one standard deviation increase in network size increases a migrant’s likelihood of beingemployed in the agricultural sector by around 8 percentage points. In contrast, Munshi (2003) finds a large effectthat is opposite to my estimates. His estimates suggest that a one standard deviation increase in network sizedecreases the probability of working in the agricultural sector by 19 percentage points.

18Results for these IV regressions of wages are shown in Appendix Table 3.A.2. Note that the sample size de-creases significantly from 2,279 to 960 because wages are only reported in the 2000 survey but not 1994.

19Using a two-sample t-test, I find that agricultural wages are not significantly higher. The mean (standarddeviation) of agricultural wages is 24.96 (5.03) with a sample size of 20, while that of non-agricultural wages is20.87 (0.56) with a sample size of 940.

111

Figure 3.3 ‐ How Rainfall Affects The Type of Migrants

1973

19741975

1978

1979

1980

1981

1982

1983

1984

1985

1986

1987

1988

1989

1990

199119921993

1994

1995

1996

1997

1998

1999

-.75

-.5-.2

50

.25

.5.7

5C

hang

e in

ann

ual r

ainf

all (

met

res)

-.15 -.1 -.05 0 .05 .1 .15Change in proportion of migrants with agricultural background

Fitted regression with 95% confidence interval shown, with observations weighted by the number of migrants.A migrant's background is derived from the main occupation of the head of her origin household.

Figures reflect changes from previous yearRainfall & Migrants With Agricultural Background

 35

3.6 Robustness Checks

I run a series of checks in this section to confirm the robustness of my results. I will consider al-

ternative measures of the key variables, account for the possibility of self-selection, and address

any remaining econometric concerns that has not been dealt with hitherto.

3.6.1 Alternative Measures

One way to verify the robustness of my results is to consider various alternative measures of

some of the key variables.20 First, I replace the network size variable with the proportion of mi-

grants from the origin village and find that my estimates of network effects remain unchanged.

Then, apart from annual rainfall, I experimented with other potential instruments that capture

weather shocks. For instance, I use (i) deviations from mean historical rainfall, (ii) the variance

of rainfall across months and (iii) rainfall in the farming months. I end up using annual rainfall

20Some of the robustness results can be found in Appendix Table 3.A.3.

112

because it has the highest empirical power in predicting migration. In terms of village level

variation for IV estimation, the other candidates are: (i) the mean number of plots cultivated,

(ii) the mean size of cultivation, (iii) the proportion of singles (never married) and (iv) the dis-

tance from village to nearest highway; however, I find them to be weak instruments. Finally,

as is common in the literature, I switch the wage variable from levels to logs and the results

remain unchanged.

3.6.2 Selection Bias

As mentioned before, self-selection – of migrants into cities with large networks – is not ad-

dressed by the IV procedure. By opting out of running fixed effects regression on a (possibly)

biased sample, I am left with indirect means to try to refute the presence of selection. One

way to do this is to check the most common type of selection – by ability. To this end, I run

IV regressions of school attainment on network size to check if migrants who move to cities

with large networks have more or less schooling. I find that network sizes are uncorrelated

with school attainment, controlling for migrant characteristics, village and city-year effects. I

repeat these regressions, replacing school attainment with age, and reach the same conclusion

[columns (1) and (2), Table 3.6]. To the extent that school attainment and age are reasonable

proxies for unobserved ability, I take this as ancillary evidence against self-selection.21

Having said that, even if self-selection takes another form – by unobserved motivation, for

instance – that I cannot test, the estimated network effects can still be interpreted as a lower

bound of the true network effects, provided that the selection bias is negative.

21Another variant of this sort of selection may be that “better” households have members who are more or lesslikely to migrate, and, conditional on migrating, move to cities with larger or smaller networks. However, I amunable to check for this because variables that reflect household-level wealth may well be endogenous, to the extentthat migrants who benefitted from larger networks may accumulate more wealth and send them back to villages.

113

Table 3.6 ‐ Robustness Checks

Dep

ende

nt variable:

Scho

ol 

attainment

Age

IV (1

)IV (2

)IV (3

)IV (4

)IV (5

)IV (6

)IV (7

)

Network size (m

ultip

les of 10)

‐0.142

‐0.035

0.079***

0.082***

0.079**

0.104**

0.095***

[0.094]

[0.082]

[0.029]

[0.029]

[0.036]

[0.044]

[0.028]

First stage F‐statistic

18.39

13.54

18.48

15.06

17.12

[p‐value

][0.000]

[0.000]

[0.000]

[0.000]

[0.000]

Han

senʹs J‐s

tatistic

2.51

6.34

7.10

7.57

8.97

4.25

4.70

[p‐value

][0.868]

[0.386]

[0.214]

[0.271]

[0.110]

[0.514]

[0.454]

Mean of dep

ende

nt variable

6.453

25.548

0.902

0.902

0.912

0.904

0.902

Migrant con

trols & village fix

ed effe

cts

Yes

Yes

Yes

Yes

Yes

Yes

Yes

City‐year fixed effe

cts

Yes

Yes

Yes

Yes

Yes

Yes

Yes

Num

ber o

f observatio

ns2279

2279

2279

2262

2070

1275

2279

Colum

n (7): IV re

gression in colum

n (3), controlling fo

r average employ

ment o

utcome an

d scho

oling by village‐city.

Job with

in first m

onth

Colum

n (6): IV re

gression in colum

n (3), exclud

ing Ba

ngko

k.

Colum

ns (1

)‐(3): IV re

gression

s using the interaction instrument i.e. lagged rainfall x villa

ge rice produ

ction.

Colum

n (4): IV re

gression in colum

n (3), with six (instead of five) lags of rainfall.

Colum

n (5): IV re

gression in colum

n (3), exclud

ing Bu

riram city

.

Clustered

stan

dard

errors

inpa

rentheses.*sign

ificant

at10%;**sign

ificant

at5%

;***sign

ificant

at1%

.Th

eIV

regression

susetheinteraction

ofrainfallan

dthepred

ictedprop

ortio

nof

netrice

prod

ucersas

aninstrument.Five

lags

ofrainfallareused

unless

otherw

isespecified

.Migrant con

trols includ

e age, gende

r, an

d scho

ol atta

inment.                                                                      

 32

114

3.6.3 Other Econometric Concerns

Firstly, I check if my results are robust to the choice of lags of rainfall by running the IV regres-

sion with six lags instead of five [column (4), Table 3.6]. It turns out that the estimated network

effects are rather stable.

The next issue is regarding the validity of lagged rainfall as an instrument. Recall that the

exclusion restriction will be violated if lagged rainfall is correlated with city-year shocks, and

Buriram city is of particular concern because it is geographically close to Nang Rong and has

a substantial agricultural sector that may depend on rainfall. To address this concern, I first

conduct the Hansen overidentification test and find that the interaction instrument appears to

satisfy the orthogonality condition. Then, I exclude Buriram city from the sample and find that

the network effects remain unchanged [column (5), Table 3.6].

Thirdly, the high rate of attrition (of about 30 percent) could confound my estimates, es-

pecially since most of the attrition is due to non-traceability. Suppose migrants with lower

abilities tend to live in more obscure locations that are harder to locate, then my sample will

contain a distribution skewed towards the high-ability migrants, which will result in a negative

attrition bias if low-ability migrants benefit most from networks. While there is no obvious way

to check for this, I exclude Bangkok – a large metropolitan city that is most likely to suffer from

non-traceability – from my analysis and find that the new IV coefficient increases [column (6),

Table 3.6]. This suggests that one (or both) of the following may be true. Firstly, there may be

heterogeneous effects in the sense that migrants who went to Bangkok may be different from

other migrants. Secondly, there may, in fact, be attrition bias, in which case my previous results

are potentially underestimates of network effects.

Following the literature on peer effects, I also control for the average employment outcome

and school attainment, both of which may be influenced by lagged rainfall via migration and

could confound my estimates. In other words, we can think of the average employment out-

come and school attainment as omitted proxies for the quality of networks that could well be

captured in my estimates of network effects. By looking at column (7) of Table 3.6, however,

115

we can see that the inclusion of these controls actually increases, not decreases my IV estimate.

Next, I address the issue of recall bias. In the construction of network size, I rely heavily

on the accuracy of migrant life histories. Therefore, if migrants systematically report migration

year with a positive (or negative) error, my estimates of network effects will be biased due to

the omission (or inclusion) of lags. To check that there is no recall bias of this sort, I use the

first-stage regressions to conduct a falsification test. For instance, if migrants systematically

report migration year with a negative error of one year (e.g. they report 1990 instead of 1991),

then rainfall in year t is actually rainfall in year t − 1, and the first-stage coefficient should

have been negative. However, from column (4) of Table 3.4 (bottom panel), we see that the

coefficient of rainfall in year t is not statistically different from zero, which leads us to believe

that this type of misreporting is absent. On the other hand, if migrants systematically report

migration year with a positive error of one year (e.g. they report 1992 instead of 1991), then

rainfall in year t− 1 is really rainfall in year t, and the first-stage coefficient should have been

zero. Again, we see that the coefficient of rainfall in year t− 1 is negative and highly significant,

so this type of misreporting is also absent. Therefore, the first-stage regression turns out to be

a convenient falsification test, and the results suggest an absence of recall bias that is due to

systematic misreporting.

Finally, I address the issue of non-response in the two employment outcomes. To make

sure that I do not have a biased sample that could confound my results, I run OLS regressions

of non-response on network size and the interaction instrument separately, and IV regressions

of non-response on network size, conditional on migrant characteristics, village and city-year

fixed effects (see Appendix Table 3.A.4). From columns (2) and (3), we see that non-response

in job search duration is uncorrelated with the interaction instrument and the instrumented

network size. However, columns (5) and (6) indicate that non-response in job type may be

correlated with the interaction instrument, although there is still no correlation with the instru-

mented network size. As such, we can only rule out non-response bias in job search duration,

but not job type.

116

3.7 Conclusions

In this study, I explain the importance of social networks to rural-urban migrants who leave

home in search of better employment, and attempt to identify empirically the network effects

by using data collected from the district of Nang Rong, Thailand. Through the use of het-

erogeneous migration responses to regional rainfall shocks (due to variation in the village-

level involvement in rice production) as exogenous variation affecting network size, I attempt

to address the econometric issues that plague the empirical literature on the identification of

network effects. My empirical results suggest that networks are important in the job search

process, and in particular, a one standard deviation increase in the network size increases the

likelihood of finding a job within the first month of migration by approximately 9 percentage

points. Surprisingly, I also find that networks draw new migrants into the agricultural sector.

However, I argue that this is because my estimates are essentially local average treatment ef-

fects that are estimated off agricultural workers who are most affected by rainfall shocks, and

should not be interpreted as average network effects.

While several empirical estimates of the network effects have emerged in recent years, these

are the first, to my knowledge, to (i) emerge from a rural-urban migration data set and (ii) reflect

network effects at the village level, and will contribute to the general literature in ascertaining

the importance of social networks. Given that network effects prove the existence of social

externalities, and that rural-urban migration is a concomitant of economic modernization, this

study also provides estimates that are imperative to the formulation of development policies.

Future work should examine other mechanisms that may work through migrant networks.

In particular, the establishment of networks may not only affect employment outcomes of new

migrants, but also the behavior of potential migrants. Given the rich set of data that is available

from Nang Rong and the importance of rural-urban migration in developing economies, a

further investigation is possible and certainly warranted.

117

Appendix

Table 3.A.1 ‐ Constructing Network Size

YearMigrant

village village city city 1992 B,D,E 3village city village city 1993 A,C,D,E 4village village city city 1992 B,D,E 3village city city city 1991 E 1city city city city ‐ ‐ ‐

Note: Network size excludes the migrant herself. In addition, I cannot compute migration year ornetwork size for migrants who made their last trip earlier than the beginning of the life history data. Forinstance, I cannot determine migrant Eʹs migration year because she must have moved before 1991.

A

1993 19941991 1992

E

Network members

A simple example of how I determine migration year and construct network size from migrantʹs lifehistory data. In this example, assume that there are only five migrants from a single village to one citydestination:

BCD

Migration year

Network size

 36

118

Table 3.A.2 ‐ OLS & IV Regressions (Wages)

OLS & IV RegressionsIV (1) IV (2)

Network size (multiples of 10) ‐0.846 ‐0.646[1.495] [3.886]

Migrant controls & village fixed effects Yes YesCity fixed effects Yes NoCity‐year fixed effects No Yes

First stage partial F‐statistic 7.12 13.23[p‐value] [0.000] [0.000]Mean of dependent variable 20.954 20.954

Number of observations 960 960

First Stage Regressions

Instrument   (t) 0.611 ‐2.572[0.486] [2.528]

Instrument (t‐1) ‐0.616* 8.807***[0.323] [1.577]

Instrument (t‐2) ‐0.444 5.968***[0.291] [1.120]

Instrument (t‐3) ‐0.800 3.270[0.474] [2.449]

Instrument (t‐4) ‐1.249** 2.405[0.460] [2.938]

Instrument (t‐5) ‐1.537*** 7.624***[0.444] [2.132]

Number of observations 960 960R 2 0.58 0.78

Dependent variable: Wages from first job

Dependent variable: Network size

Clustered standard errors in parentheses. * significant at 10%; ** significant at 5%; *** significant at1%. ʺWages from first jobʺ measures the migrantʹs hourly wages (in Thai baht) from her first job,deflated by consumer price indices using 2000 as the base year. The IV regression in column (1)uses lagged rainfall as an instrument for network size. The IV regression in column (2) uses theinteraction of rainfall and the predicted proportion of net rice producers as an instrument.Migrant controls include age, gender, and school attainment. In this sample, the mean andstandard deviation of network size are 1.37 and 1.29 respectively.

 37

119

Table 3.A.3 ‐ Alternative Specifications

Dependent variable:

IV (1) IV (2) IV (3) IV (4)

Network size (multiples of 10) 0.079*** ‐0.646 ‐0.057[0.029] [3.886] [0.138]

Proportion of migrants from the same village 1.127**[0.481]

First stage F‐statistic 18.39 16.65 13.23 13.36[p‐value] [0.000] [0.000] [0.000] [0.000]Hansenʹs J‐statistic 7.10 6.83 8.62 7.61[p‐value] [0.214] [0.233] [0.125] [0.179]Mean of dependent variable 0.902 0.902 20.954 2.772

Migrant controls & village fixed effects Yes Yes Yes YesCity‐year effects Yes Yes Yes Yes

Mean of network size 1.16 0.10 1.37 1.37Standard deviation of network size 1.16 0.09 1.29 1.29Number of observations 2279 2279 960 958

Clustered standard errors in parentheses. * significant at 10%; ** significant at 5%; *** significant at 1%. ʺJob within firstmonthʺ = 1 if the migrant finds a job within the first month of migration; 0 otherwise. ʺWages from first jobʺmeasures themigrantʹs hourly wages (in Thai baht) from her first job, deflated by consumer price indices using 2000 as the base year.The IV regressions use the interaction of rainfall and the predicted proportion of net rice producers as an instrument.Migrant controls include age, gender, and school attainment. I lose two observations in column (4) due to the logarithm ofzero wages, which is undefined.

Job within first month

Job within first month

Wages from first job

Log (wages from first job)

 38

120

Table 3.A.4 ‐ Non‐Response

Dependent variable:

OLS (1) OLS (2) IV (3) OLS (4) OLS (5) IV (6)

Network size (multiples of 10) 0.025** 0.063 ‐0.011 ‐0.034[0.008] [0.055] [0.008] [0.043]

Annual rainfall  (t)     x Village prop. of rice producers ‐0.523 0.057[0.560] [0.353]

Annual rainfall (t‐1)   x Village prop. of rice producers 0.588 ‐0.482[0.521] [0.539]

Annual rainfall (t‐2)   x Village prop. of rice producers ‐0.171 ‐0.232[0.527] [0.406]

Annual rainfall (t‐3)   x Village prop. of rice producers 0.178 0.646[0.411] [0.415]

Annual rainfall (t‐4)   x Village prop. of rice producers 0.705* ‐0.178[0.323] [0.705]

Annual rainfall (t‐5)   x Village prop. of rice producers 0.87 ‐0.81[0.676] [0.407]

Partial F‐statistic 1.32 3.42[p‐value] [0.285] [0.013]

Household and migrant controls Yes Yes Yes Yes Yes YesVillage and city‐year fixed effects Yes Yes Yes Yes Yes YesNumber of responses 2279 2279 2279 2279 2279 2279Number of non‐responses 598 598 598 598 598 598Number of observations 2877 2877 2877 2877 2877 2877

Clustered standard errors in parentheses. * significant at 10%; ** significant at 5%; *** significant at 1%. The IV regressions in column(3) and (6) use the interaction of rainfall and the predicted proportionof net rice producers as an instrument. Migrant controls includeage, gender, and school attainment.

Job within first month Agricultural jobNon‐response of: Non‐response of:

 39

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