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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
tow
aro
rn
ot)
isa
du
mm
y
that
equ
als
on
ew
hen
the
ind
ivid
ual
rep
ort
sd
isab
ilit
y.
So
me
ob
serv
atio
ns
are
lost
du
eto
un
rep
ort
edh
ealt
hm
easu
res.
Th
em
ean
and
stan
dar
d d
evia
tio
n o
f th
e w
ar c
asu
alty
rat
e in
co
lum
ns
(1)-
(5)
are
0.01
8 an
d 0
.027
res
pec
tiv
ely
.
Su
bje
ctiv
e
hea
lth
War
tra
um
aD
epre
ssio
nP
hy
sica
l
dis
abil
ity
War
dis
abil
ity
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.
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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.
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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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