Does compulsory schooling prevent child labour? : evidence from 35 quasi-experiments in Africa and Asia

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Does Compulsory Schooling Prevent Child Labour? Evidence from 35 Quasi-Experiments in Africa and Asia

Hayaan-Diriye Abdi Nur University of Amsterdam

August 2017

Author Note

Univeristy of Amsterdam, School of Economics.

Master Thesis, MSc Economics 2016/2017 academic year, Track Development Economics.

Supervisor: Prof. Dr. Hessel Oosterbeek, University of Amsterdam, Amsterdam School of Economics

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Abstract

Child labour remains a widespread phenomenon. Most policy actors agree that compulsory schooling, which today most countries prescribe, significantly reduces child labour. Empirical support for this assertion employing counterfactual methods is still missing and theories are at odds. This study constructs 35 quasi-experiments in Afirca and Asia to assess the impact of compulsory schooling on child labour. Non-parametric fuzzy regression discontinuity designs on a sample of 200 000 children aged five to nine are performed. Age in months is the running variable, school attendance the first stage dependent variable, and child labour the second stage dependent variable. Three sets of discontinuity points are tried: Presumed legal offs, offs identified with a data-driven search procedure and visually identified cut-offs. Only in the latter, nine cases were identified, where schooling rules are relevant for school attendance. Two-Stage-Least-Squares estimates for those nine cases find no evidence that compulsory schooling reduces child labour: The preferred point estimate for total labour is slightly positive (an increase of 0.78 hours per week) with narrow confidence intervals (+/- 1.77 hours per week). This result is coherent with naïve OLS estimates that control for gender and age. I conclude that there is no empirical support for the notion that compulsory schooling notably reduces child labour for young children.

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Statement of Originality

This document is written by Student Hayaan- Diriye Abdi N ur who declares to take full responsibility for the contents of this document.

I declare that the text and the work presented in this document is origina l and that no sources other than those mentioned in the text and its references have been used in creating it.

The Faculty of Economics and Business is responsible solely for the supervision of completion of the work, not for the contents.

Acknowledge me nts

To my mother, Elisabeth N ur. I studied the enhancement of opportunities, but I owe all my opportunit ies to her. Special thanks also go to Lena Weingaertner for the support throughout the process and the last years.

Hessel Oosterbeek always provided me with the right comments. I never had anybody reading my work with such a sharp eye and giving me constructive evaluations of that quality before.

Volker Loewer regularly found words that lifted my spirits. Ina-Makiya N ur, as well as Otto and Ingeborg Welte were there to lend me an open ear and t o check my narratives against non-economists’ realities.

I would like to thank my fellow Development Economics and Public Policy students for their feedback and friendship. Thanks also go to the Newtons, my International-Development-Studies-Friends and their philosophical comments on my ideas, as well as my extraordinarily supportive friends that I made in Amsterdam during the last two years. I will miss Amsterdam and my studies.

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Section 1: Introduction

Though child labour has been declining sharply, the International Labour Organization (ILO) estimated that in 2012 more than 250 million children were still in employment (Diallo, Etienne, & Mehran, 2012). More than 37 million of these children were younger than 12 years old (Diallo et al., 2012). The economic activity of children, even very young ones, remains a widespread phenomenon. Child labour has been receiving considerable attention throughout the history of economics, and has seen a recent proliferation of empirical work (Edmonds, 2008). This study contributes to this positive, empirical field of inquiry on child labour. It assesses the impact of compulsory schooling on the amount of labour children perform.

Compulsory education laws have spread around the world. Today most countries have some form of compulsory education legislation. The last large country to introduce such a law was India, which made education compulsory for children aged 6 to 14 in 2009 (Dubey, 2010). There is a rich tradition of employing compulsory schooling laws as a source of exogenous variation to assess the impacts of education in the United States a nd Europe. The exogenous variation caused by compulsory education laws has been used to estimate the effect of education on labour market outcomes (Aakvik, Salvanes, & Vaage, 2010; Angrist & Krueger, 1991), on crime (Hjalmarsson, Holmlund, & Lindquist, 2015; Locher & Moretti, 2004), on health (Gathmann, Jürges, & Reinhold, 2015; Lleras-Muney, 2005) and on social behaviour (Black, Devereux, & Salvanes, 2008; Meyer, 2015). More recently the first working papers exploiting those laws as instruments in middle income countries have emerged (Dincer & Erten, 2015; Singh, 2016).

There has been significant scholarly debate concerning what the effect of compulsory education on child labour is. For example, Weiner (1991) argues that a child labour ban is

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more easily monitored and therefore more easily enforced through compulsory schooling. Furthermore, compulsory schooling makes it difficult for a child to work because substantial amounts of its time are occupied by education. Other authors, however, note that child labour might actually help children go to school by giving families the necessary resources (Patrinos & Psacharopoulos, 1997).

These opposing views are also reflected in more general theoretical approaches to child labour. Some authors pursue an extra- household bargaining approach (Basu, 1999). These authors stress that children have negligible agency in the decision to work. Child labour arises in a bargain between an employer and the parents when the preference of parents for the child’s welfare is low. Introducing mandatory schooling in such a setting would lead to a decrease in child labour since parents have less of the child’s time to sell.

The assumption that parents internalise the welfare of the child only to a small degree strikes other authors as implausible (Basu & Van, 1998). They explain child labour with a need for household survival. In their modelling, some households are close to the survival line where the marginal utility for more consumption becomes infinite. While parents are the decision makers and internalise the child’s welfare, they are left with no choice but to send the child to work because the household would not survive otherwise. In this framework, the introduction of mandatory schooling has no effect on child labour (presuming the household is to survive), because the need for household survival persists. A positive effect can even be hypothesised since schooling potentially increases the need for income.

Some of this scholarly work has been picked up by policy actors. For instance, the ILO website on Child Labour and Education for All reads that “[i]t is widely accepted by many organizations, including UNICEF, the World Bank, UNESCO and the G8 Education Task Force, that education – and in particular, free and compulsory education […] - is a key element in the prevention of child labour” (ILO, 2017). In some publications this perspective

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is directly linked to Weiner (1991) (Fyfe, 2005). Since most large policy shapers working on child labour seem to subscribe to the view that compulsory schooling reduces child labour and since both child labour and compulsory schooling are widespread phenomena, it is important to know the precise effectiveness of this tool. Nevertheless, empirically rigorous studies in the form of experimental or quasi-experimental evidence are largely missing. Only one conference paper was identified that directly investigates this link on a sample of Turkish 15 to 18 years-old teenagers.

This study considers substantially younger children and expands on the geographical scope of previous work. It builds on a sample of over 200 000 children between the ages of five and nine in all African and Asian locations where UNICEF Multiple Indicator Cluster Surveys (MICS) round four or five were held (UNICEF, 2012, UNICEF, 2013). I first construct all estimates separately for each of the 35 samples and then aggregate indicators with tools common in meta-analysis. This paper presents a regression discontinuity design with the age of children as the running variable and the age where children are eligible for compulsory schooling as the cut-off. In a first step, school attendance is chosen as the dependent variable. This method shows whether compulsory schooling laws are relevant, meaning whether they dictate whether and when children attend schools in practice. I generally do not find a significant regression discontinuity at the legally mandated points. I conclude that compulsory schooling laws are generally not determining whether children attend schools in developing countries.

Therefore, a search procedure is trialled to test whether the cut-off point is wrongly specified. It could well be that other strict rules govern whether children attend schools. Due to combinatorics limitations, only very simple rules can be identified with this search procedure. Generally, I do not detect significant regression discontinuities.

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In a last step, cut offs are visually identified. The resulting regression discontinuities are generally so large and significant that I assume that they arise from some sort of institution. Whether those have to be interpreted as societal norms or formal institutions cannot be determined. A fuzzy, non-parametric regression discontinuity design is devised. The first stage, again, is school attendance over children’s age as the running variable with the visually found cut-off as the discontinuity. The second stage has child labour as the dependent variable. I generally find no significant change in the amount that children work in response to schooling. This is true for all forms of labour: total labour, market labour and domestic labour. The preferred point estimate for total labour is slightly positive (an increase of 0.78 hours per week) with relatively narrow confidence intervals (+/- 1.77 hours per week). Therefore, the results are not decisive in determining whether schooling increases or decreases the provision of child labour. However, we can reject less nuanced hypotheses on the relationship based on the results presented in this paper. Even moderately negative impacts, as well as strongly positive impacts can be rejected. While this association is not coherent with naïve correlations between child labour and schooling, I find similar results when regressing schooling on child labour, controlling for age and gender. There is no evidence that compulsory schooling is a key tool for the prevention of child labour. However, there is also no evidence that child labour finances schooling at scale.

In the following section 2 presents a literature review, which provides a definition of child labour, an overview over the theoretical approaches and presents relevant empirical estimates. Section 3 lays out a simple model that is used as an analytical heuristic. Section 4 discusses the empirical design of this study. Section 5 introduces the dataset and gives an overview over the data. Section 6 presents the results and Section 7 concludes.

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Section 2: Literature Review

Definitions

To assess the impact of compulsory schooling on child labour, first a definition of compulsory schooling and child labour is required. In the case of compulsory schooling, this is relatively straight forward: it is defined by legislation that mandates children with certain characteristics (in this case a certain age) to attend school. All countries in the sample have such a law in place, just as the majority of countries worldwide. O ften, these laws are coupled with the free government provision of schooling.

The definition of child labour is more contentious. Edmonds (2008) gives an introduction into the terminology. While normative work is concerned with only defining activities that are harmful to the child as child labour, the positive economic study of child labour is more interested in the allocation of time as a resource for a child to do certain activities in. This study follows the latter tradition and defines child labour broadly as all activities that produce a good or service. Focussing on a more limited set of activities would bias the understanding of child labour. I take a hypothetical family as an example that comprises of a child and an adult. The family does household chores for an employer against payment and it has to do household chores in its own household. I treat the situation equally where the child performs household chores in its own household to the parent doing work against payment, and vice versa. In the end, both scenarios involve the same activities for the child, just in different places.

Because this definition deviates from what is popularly referred to as child labour, the analysis is subsequently broken down into market work and domestic work, as defined in Edmonds (2008). Market Work is any work that produces a good or a service that is being sold and is therefore closer to the popular conception of child labour. It includes unpaid work like helping out in a parent’s shop or working on relatives’ farms. However, it excludes the

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production of goods and services that are exclusively consumed by the household, regardless of the work intensity. Domestic work includes all work except for market work. It therefore includes activities like fetching water, gathering firewood and cleaning.

Often Unconditional Worst and Hazardous Forms of Child Labour are also distinguished (for instance in Edmonds (2008) and Diallo et al. (2012)). However, this study does not differentiate between it and Market Work as a result of the specific age group it looks at. Unconditional Worst and Hazardous Forms of Child Labour are usually defined, because one wants to distinguish child labour for abolition from permissible child labour. Permissible child labour includes light work for teenagers, for example. However, for children under the age of 12 all market work is conventionally regarded as child labour for abolition (Hilowitz, 2004), with only few exceptions. To avoid convolutedness of the analysis and because market work typically represents child labour for abolition, no further breakdowns of activities are introduced in this paper.

Theoretical Work

The theoretical approaches used today in the economic analysis of child labour were already largely present in the late 1990s. Therefore, Basu (1999) gives an excellent overview of the principle views. Cigno and Rosati (2005) take a more encompassing approach, creating models that incorporate most previo us models and models that formalise ideas about child labour. This study takes a more narrowly defined view, as it is only assessing the impact of compulsory schooling on child labour, holding all other variables constant through a quasi-experimental approach. Therefore, all variables that are separable in the decision- making process around child labour are disregarded. This paper particularly omits the demand side for child labour and general equilibrium considerations.

Furthermore, the class of theories that is referred to as Intra-Household Bargaining Models by Basu (1999) is not taken into consideration. This stream of thought sees children

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as the agent that makes decisions over their provision of labour. While there is some evidence that child preferences might play a role, this seems implausible in the cases this study is concerned with. The children considered here are nine years old or younger. Even if the household is not a single conflict- free entity, their voice on important decisions can be assumed to be negligible (Humphries, 1999).

When additionally excluding non- formalised approaches, this leaves us with two versions of the Extra-Household Bargaining Model. In Extra-Household Bargaining models, the child is effectively an instrument for the parent’s maximisation effort (Basu, 1999). In the classical version, as described by Gupta (2000), parents are furthermore entirely selfish and not interested in the child’s welfare. Parents therefore try to sell as much of their child’s labour as possible. Variation in child labour occurs through the introduction of efficiency wages and a bargaining situation with an employer. Only when the bargain fails, the child does not work. This approach ultimately equates child labour with child abuse.

Different scholars (including Basu (1999) and Basu and Van (1998)) noted that these assumptions, made by Gupta (2000) and others, seem empirically implausible. Especially the argument that parents do not internalise their children’s welfare is contested. Prima facie evidence mentioned to support the assertion that parents are interested in their children’s welfare is that children in wealthy countries and children in wealthy households in developing countries rarely work. The following subsection discusses further empirical evidence questioning this assumption. However, as will be shown in Section 3 (Theory), the assumption that parents do not substantially internalise their children’s welfare is necessary to predict a negative impact of compulsory schooling on child labour under standard assumptions. Notable scholars, such as Weiner (1991) and all major international organisations predict such a negative impact and therefore implicitly subscribe to this assumption.

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Critiquing classical Extra-Household Bargaining models, Basu and Van (1998) introduce a model where parents are the decision making agents, where child labour is harmful to children’s welfare, where adults can do the work children do (substitution between child and adult labour) and where parents highly internalise the children’s welfare. To allow for child labour under this parametrisation, Basu and Van (1998) introduce the luxury axiom. The luxury axiom states that a household would not send its children out to work if its income from non-child labour sources were sufficiently high. This axiom implicitly introduces a survival line. Technically, a survival line is a level of consumption under which consumption is not allowed to drop for welfare to be defined. Practically, it defines a minimum level of consumption for families to survive. Therefore, this specific parametrisation will be called the Household Survival model, whereas Gupta’s (2000) parametrisation (where parents do not internalise their children’s’ welfare) will be referred to as the Extra-Household Bargaining model. The Household Survival model and the Extra-Houshold Bargaining model will be the ones discussed in Section 3 (Theory) and are tested against each other in this paper.

Empirical Estimates

Edmonds (2008) notes that schooling and child labour decisions are joint outcomes out of a single time allocation problem. He further states that it is impossible to identify a causal impact of schooling on child labour (and the other way around) without knowing the shadow value of the child’s time. He deducts this assertion from the impossibility of a situation where only the allocation of time to one activity is affected exogenously. This study circumvents this problem with its principle innovation: It employs compulsory schoo ling laws as a source of exogenous variation in the amount of schooling a child receives.

Only a single empirical estimate was identified that uses exogenous variation in the amount of schooling a person receives to estimate the effect on its labour supply. It stems from a conference paper by Dincer and Erten (2015). They use an expansion of mandatory

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schooling in Turkey in 2012 as a source of exogenous variation. Dincer and Erten (2015) construct a non-parametric fuzzy regression discontinuity design with age as the running variable, school attendance as the first stage dependent variable and labour supply as the second stage dependent variable. They find that the reform increased high school attendance by 3.7 percent and decreased the hours worked by 19 percent.

While similar in its identification approach, Dincer's and Erten’s (2015) work differs in several important ways from this study. First of all, they are looking at teenagers aged 15 to 18, whereas this paper is concerned with children aged five to nine. Second, Dincer and Erten (2015) focus on legal labour, whereas most of the labour analysed in this study constitutes illegal labour. Furthermore, Dincer and Erten (2015) look at a country that was classified as a upper- middle income economy on the verge of becoming a high- income economy according to the world bank in 2012 (The World Bank, 2017). This paper looks at low- income and lower-middle income economies.

While there is a broad field of literature that employs the exogenous variation created by compulsory schooling laws in Europe and the United States, there are few empirical estimates that employ these in a developing country context. Labour market outcomes, such as the returns to schooling, are probably the most well-known examples where compulsory schooling laws are employed in this way (Aakvik et al., 2010; Angrist & Krueger, 1991). Furthermore, other authors studied additional outcomes of schooling with similar identification techniques. Examples include Hjalmarsson et al. (2015) and Locher and Moretti (2004) on the effect of schooling on crime, Gathmann et al. (2015) and Lleras-Muney (2005) on the effect of schooling on health and Black et al. (2008) and Meyer (2015) on the effect of schooling on social behaviour, such as voting. Outside of Europe and the United States, I could only identify two studies that work with this technique: Singh (2016) on the

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productivity of schooling and the earlier cited study on the effect of compulsory schooling on child labour (Dincer & Erten, 2015).

Other studies that examine the connection between schooling and child labour either focus on the correlation between child labour and schooling or assess inter ventions that influence the shadow value of the child’s time to make inferences about child labour and schooling. Many authors make note of a negative correlation between school attendance and child labour (Dincer & Erten, 2015; Edmonds, 2008; Psacharopoulos, 1997; Ray & Lancaster, 2005). It has been shown that children of the same age that work more are less likely to attend a school. However, the negative correlation between child labour and schooling can hardly be given any causal interpretation. Confounding factors, such as family income, can be assumed to play a significant role.

Studies that influence the shadow value of a child’s time in one way or another generally show that more child labour leads to less school attendance (Edmonds, 2008). They usually employ direct exogenous variation in the child’s wage, exogenous variation in the costs of schooling, or variation in the marginal utility from child labour through cash transfers. A negative impact of child labour on schooling does however not necessarily mean that more schooling also leads to less child labour.

We know that having more money at hand leads to less child labour. All 19 studies reviewed in Bastagli et al. (2016) show a significant decrease in the amount of child labour in response to a cash transfer. At the same time, in the vast majority of cases, cash transfers have a positive impact on school attendance (Bastagli et al., 2016), even when not making school attendance a condition (Baird, McIntosh, & O zler, 2011; Benhassine, Devoto, Duflo, Dupas, & Pouliquen, 2015). Edmonds and Shrestha (2014) and Ravallion and Wodon (2000) show that the same holds true when subsidising school attendance. This is consistent with the

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Household Survival model but would need strong additional assumptions in the Extra-Household Bargaining model.

Studies have also shown that increasing child wages or reducing costs associated with child labour increases child labour while simultaneously reducing school attendance (Boozer & Suri, 2001; Gunnarsson, Orazem, & Sánchez, 2006). However, we cannot conclude from these estimates that when fixing school attendance at a higher level, child labour would drop. It is, for example, perfectly consistent with the Household Survival model that children work more in times of higher wages and reduce their time in school to receive optimal levels of rest and play. As can be seen in Section 3 (Theory), a Household Survival model, at the same time, predicts no, or even a positive change in child labour in response to an exogenous increase in schooling.

Generally, empirical evidence tends to be more supportive of a Household survival approach than of modelling child labour in Extra-Household Bargaining models. However, there is no direct evidence on the response of young children to compulsory schooling. Additionally, conclusive evidence cannot be easily deducted from existing findings and joint decision-making on child labour and other activities poses a challenge to identification.

Section 3: Theory

In this paper, I use a model that is adapted from Edmonds (2008). It does not contain many details, but focusses on the core elements needed to deduct child labour responses to compulsory schooling1. In the simple model presented here, the allocation of a child’s time is modelled. The child has a budget of time that is standardised to unity. This time can be allocated to education (E), work (W) or play (P).

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For richer mode ls, consult Cigno and Rosati (2005), who’s chapter three focusses on the child labour-education relationship.

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𝐸 + 𝑃 + 𝑊 = 1 (1)

Play (P) includes all activities that are neither education nor work and thus typically includes activities like sleep, playing and grooming. Education (E) includes both, schooling and studying. I will assume, however that they have a fixed ratio. This means, for instance, that an exogenous increase in schooling is not offset by proportional decrease in studying. Work consists of both, market work and domestic work, a simplification from the model presented by Edmonds (2008).

A child's welfare, in this model, solely depends on how much time is allocated to each of the activities. Since equation 1 has to hold, one of the variables can be dropped from the function, yielding:

𝐺(𝐸, 𝑃) (2)

Education might not immediately benefit the child but pay off later in life. However, intertemporal decision- making is not the focus of this paper. Therefore, we can abstract from time and interpret the welfare as all current and future benefits and harms a child has from the allocation to each of the activities.

Parents are the decision making agent in this model. They have an objective function (u) that solely depends on the family's consumption and the child’s welfare. The consumption is determined by an exogenous amount (Y) that the parents earn, by the child’s earnings and by the costs of education. The child’s wage is set to w. It does not reflect any stochastic elements and has no interactions. This is justified because the demand side is fixed in the empirical analysis through the quasi-experimental method. The costs of education consist of the unit costs for education (e) and the amount of education (E). Combined this yields the following optimisation problem:

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max

𝑊,𝑃 𝑢[𝐹(𝑌 + 𝑤 ∗ 𝑊 − 𝑒 ∗ 𝐸), 𝐺(𝐸, 𝑃)] (3)

𝑠. 𝑡. 𝐸 + 𝑃 + 𝑊 = 1

𝑊 ≥ 0, 𝑃 ≥ 0, 𝐸 ≥ 0

This is the simplest possible set-up that can unify the Extra-Household Bargaining model and the Household survival model for an analysis of the effect of an exogenous change in schooling on child labour. The Extra-Household Bargaining model implies that parents do not consider the child’s welfare. Therefore 𝜕𝑢 𝜕𝐺 = 0⁄ . The Household survival model implies a slightly more complex parametrisation. First, parents do value their child’s welfare. Therefore 𝜕𝑢 𝜕𝐺 > 0⁄ . Then we have to formalise the luxury axiom. The luxury axiom states that a household would not send its children out to work if its income from non-child labour sources were sufficiently high. This implies2:

𝜕𝑢 𝜕𝐶 > 𝜕𝑢 𝜕𝐺 𝑖𝑓 𝐶 = 𝐶𝑚𝑖𝑛 (4) 𝜕𝑢 𝜕𝐶 < 𝜕𝑢 𝜕𝐺 𝑖𝑓 𝐶 > 𝐶𝑚𝑖𝑛 (5)

However, as the name suggests, the situation where 𝐶 < 𝐶_𝑚𝑖𝑛 is not allowed for, because then the household would not survive. u becomes undefined if C drops below 𝐶_𝑚𝑖𝑛.

Now, the behavioural responses to an exogenous change in E can be deducted. First, we consider the Extra-Household Bargaining parametrisation. Since 𝜕𝑢 𝜕𝐺 = 0⁄ , the optimisation effort maximises F. F is maximised by maximising W. W is constrained by the time budget constraint. Therefore, W drops in unity with an increase in E. We can deduct the following qualitative hypothesis :

2

The substitution axio m that is central to the analysis in Basu and Van (1998) is not pic ked up in this analysis, because it is not necessary. Basu and Van (1998) a lso state the luxury a xio m. Ho wever, in their mode l, parents’ labour supply can still vary through general equilibriu m e ffects, wh ich are e xc luded fro m the analysis in my design.

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H1: An increase in E leads to a decrease in W

In the Household Survival parametrisation we have to distinguish three cases. The first case is when 𝐶 < 𝐶𝑚𝑖𝑛 and remains so after the increase of the amount of schooling

without any behavioural response. Then W remains at the same level, 0. The second and third case is when C drops below 𝐶_𝑚𝑖𝑛 due to the costs of education (𝑒 ∗ 𝐸 ) and triggers a behavioural response. In the second case the time budget constraint allows for C to increase to 𝐶_𝑚𝑖𝑛 with an increase in W. Therefore, W increases by 𝑒 ∗ 𝐸 . In the third case the time budget constraint does not allow for W to adjust upwards far enough for u to be defined. The household does not survive. We can deduct the following qualitative hypothesis:

H2: An increase in E leads to an increase in W or W stays the same

Section 4: Empirical Design

The analysis in this paper is split into three parts. In the first part I investigate whether the legal cut-off at which a child is mandated to go to school constitutes a regression discontinuity. Because I generally do not find significant discontinuities, in a second part a search procedure is employed to search for discontinuities at other points than the ones mandated by law. In a third part, nine cases are analysed separately where a regression discontinuity was visually identified to make inferences about child labour. Its result are benchmarked against naïve regressions.

I chose the regression discontinuity design as an analytical method, because it allows the identification of causal effects with relatively simple, cross-sectional data. This is one of the reasons, why we see a large and increasing number of studies employing regression discontinuity designs since the late 1990s (Imbens & Lemieux, 2008). Furthermore, being able to make inferences from observational, cross-sectional data is especially relevant in this case, because data on child labour tends to be sparse (see Sectio n 5: Data) and because a

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randomised experiment, where schooling is assigned randomly to children, is likely to be seen as unethical.

The running variable will always be age in months. Age has the advantage that it cannot be easily manipulated, one of the main threats to interpretability of regression discontinuity designs (McCrary, 2007). Age, as recorded in the data, can be more easily manipulated. A discussion on how likely this is in this case can be found in Section 5 (Data). Furthermore, tests are undertaken which are designed to judge likelihood of manipulation in the running variable.

In the first part of the analysis, school attendance is the outcome. Legal schooling age is chosen as the discontinuity point. The assumption on which identification rests in this case is that children that are just too young to be forced to go to school by law and children that are just old enough to be affected by compulsory schooling are statistically similar. This means that it is random if one ends up just right or just left of the discontinuity point. What is estimated is, whether compulsory schooling laws decide whether children go to school in practice. If nobody abides to those laws, we would expect a zero-estimate. Otherwise, we would expect an effect on compliers. In this case, compliers are the people who comply with the compulsory schooling law and at the same time compliers in the statistical sense. They are those people for whom the compulsory schooling law makes a difference. There might be both “always takers” and “never takers” (as defined in Angrist and Pischke (2008)) . The former are children that attend school, whether or not this is mandated by law. The la tter are children that do not go to school, regardless of the legal environment. Note that children who would have gone to school in any case but choose to start attending when they reach the exact age that is determined in the compulsory schooling law, are also compliers and not “always takers”. The regression discontinuity estimate presented here is an estimate of the share of compliers.

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Generally in this paper, regression discontinuity estimates follow the procedure described by Imbens and Kalyanaraman (2012). This means that the preferred point estimate is generated using local linear regression. Local linear regression as a non-parametric3 procedure has been shown to be rate optimal (Porter, 2003). In contrast to the more traditional parametric regression discontinuity designs, this method recognises that cases have differing predictive power, depending on how far on the running variable they are from the discontinuity point. Cases that are close to the discontinuity on the running variable are weighted more to generate a prediction in the discontinuity point. Triangular kernels were used for estimation. Triangular kernels are the most commonly used kernels in local linear regression discontinuity designs (when disregarding uniform kernels that would constitute a linear O LS fit). Local quadratic regression estimates (otherwise using the same parameters) are reported as well in order to check for robustness towards specification. However, as Gelman and Imbens (2014) note, high order polynomials are not very suitable in regression discontinuity designs, as they tend to produce noisy, sensitive and imprecise estimates.

Data dependent bandwidths were chosen, based on the procedure suggested in Imbens and Kalyanaraman (2012). This rule minimises the mean squared error in the point estimate under parsimonious assumptions. Calonico, Cattaneo, and Titiunik (2014b) have suggested potential improvements to Imbens' and Kalyanaraman’s (2012) rule. I disregarded these suggestions, more on practical grounds than on theoretical ones. As Calonico et al. (2014b) note, their procedure produces strictly smaller confidence intervals than the Imbens and Kalyanaraman (2012) procedure. This became a problem in the estimation of some discontinuities. Both rules chose bandwidths that are decreasing in the number of cases and dependent on the variance around the cut off. Since the number of cases was often large and

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The term non-para metric may be seen as misleading, in this case. As suggested by the word “linear” in the term, a linear fit is decided on as a para meter, as we ll as a kerne l. The estimating procedure for the discontinuity is the same as in a ce rtain weighted OLS regression. Nevertheless, I will abide to the co mmonly used terminology.

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due to certain constellations in the variance around the cut-off, the Calonico et al. (2014b) rule suggested very narrow bandwidths, sometimes narrower than one month. These bandwidths were not practical, because age was recorded in months, so sometimes the bandwidth suggested by the Calonico et al. (2014b) procedure did not include any data. Both the Calonico et al. (2014b) and Imbens and Kalyanaraman (2012) rules assume fully continuous variables as running variables. While formal proof is still missing, not fully continuous running variables might demand larger bandwidths than suggested before.

To be coherent, the bias correction term, suggested by Imbens and Kalyanaraman (2012), was also incorporated into the point estimates. The polynomial order of the bias correction term was always chosen one order higher than the polynomial order of the main estimate, as proposed by Calonico, Cattaneo, and Titiunik (2014a). All estimates were generated with the rdrobust Stata package, using the procedure referred to as the IK procedure in the accompanying paper (Calonico et al., 2014a).

Because the data employed is intended to infer general population attributes, the number of cases that are very close to the discontinuity are generally low. Furthermore, the variability of schooling (the dependent variable in the first part) and even more so of child labour (the dependent variable in the third part) is high. To increase the precision of the estimates, 35 different samples are analysed. These different samples are each analysed as a distinct quasi-experiment. To infer what the general impacts are, these estimates are then aggregated employing techniques from meta-analysis. One aggregate presented is the weighted average of the single point estimates, weighted by their sample fractions, as in Card and Sullivan (1988) and Leuven and Oosterbeek (2012). However, these weights are not statistically efficient. Therefore, also aggregate estimates are presented where the inverse of the variance is the weight, as in Leuven and Oosterbeek (2012). These weights minimise the variance of the weighted average. The efficiently weighted aggregates are preferred due to

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their higher precision. However, as will be seen, they do not qualitatively differ from the sample size weighted averages.

Because generally no statistically significant discontinuity is found, a search procedure is devised to look for other discontinuity points. Discontinuity points may be found in other than the suggested places, either because the data on compulsory schooling laws is wrong, or because discontinuities are drive n more by social norms than laws. The latter is likely, because developing countries are analysed. As for instance Acemoglu, Johnson, and Robinson (2001) note, developing countries also tend to have weak formal institutions. However, in situations where there is a need for rules (s uch as to determine when a child should attend a school), but no formal institutions, often informal institutions emerge (Ostrom, 2010).

To find a point estimate of the discontinuity point, a simple search procedure is employed. A detailed description of the search procedure and its results can be investigated in Appendix 1 (Search Procedure).

Since this approach does generally not find significant regression discontinuities either, extensive visual analysis was conducted. In some cases, such as Vietnam, other authors had identified large, significant discontinuities (Singh, 2016). Therefore, it seemed unlikely that I could not find any discontinuity at all. Repeated plotting of age at the time of the interview, age at the beginning of the school year and school attendance against each other helped to identify nine of the 35 cases, where a large, significant discontinuity could be found. An intuition of how the procedure works can be gained in Appendix 2 (Visual Identification). It features the general approach and examples. This procedure has no safeguarding mechanism against overfitting. Therefore, discontinuities that arise by chance could have been identified. However, I will argue that the regression discontinuities are so large and significant, while other signs of overfitting are missing, that this is unlikely.

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Only these nine cases are then used to identify the effect of schooling on child labour in a fuzzy regression discontinuity design. As Angrist and Pischke (2008) describe, a fuzzy regression discontinuity design essentially is an instrumental variable design. The estimation method employed is two stage least squares. All other model specifications (age as the running variable, local linear regression fit, mean squared error criterion and so forth) are the same as in previously described models. The dependent second stage variable are the child labour outcomes. These are all work and, because it became conventional in the child labour literature to report them separately, domestic work and market work. These are reported in hours per week.

The first stage in this design, again, allows identifying the effectiveness of schooling rules. The chosen cut-off generally is not at the legally mandated point as ide ntified in the data, it is not possible to interpret these cut-offs as the effect of compulsory schooling legislation. Rather, it has to be interpreted as the effect of formal or informal compulsory schooling institutions. Nevertheless, these cut-offs serve as exogenous variation in the amount of schooling children receive. It cannot be closely manipulated whether a child is born in one month or the next month. Together with the smoothness assumptions, this is the identifying assumption in the fuzzy regression discontinuity design (Imbens & Lemieux, 2008). These assumptions state that the only observable and unobservable characteristic that abruptly changes at the cut-off is whether a child is affected by schooling institutions. This assumption appears to be plausible, both with regard tests performed on the identifying assumptions and theoretically. It seems hard to come up with a reason why, e.g. children in Vietnam who were five years and eight months old on 1 July are systematically different from children that were five years and nine months old on the same date. The reduced form therefore is a causal estimate of the effect of compulsory schooling institutions and norms on child labour. The

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Two-Stage Least Squares estimates5 report the causal impact of school attendance on child labour.

Two limitations of these estimates have to be mentioned, namely the locality of the estimate and the treatment group. This estimate, such as all regression discontinuity estimates, is local (Angrist & Pischke, 2008). This means that it estimates the effect of compulsory schooling on child labour in children that are right at the cut-off. If we, for instance, assume that these children are children that are six and a half years old, we receive an estimate for children that are exactly six and a half years old. The effect on nine year olds may be different. However, we cannot estimate the effect on nine year olds in this regression discontinuity design. Furthermore, the two stage least square estimates do only report the effect on compliers (Angrist & Pischke, 2008). It may, for example, be the case that all children that never work comply with compulsory schooling, whereas all children that work do not comply with compulsory schooling. In such a scenario, we would estimate the effect of compulsory schooling on the children that never work. Since they never work, this effect would be zero. We would have no opportunity to estimate the effect on children that work. Furthermore, we do not know who the compliers are. Therefore, this paper is titled “what is the effect of compulsory schooling on child labour?”, rather than “what is the effect of schooling on child labour”. The design does not allow to estimate a general average treatment effect, but only a local estimate of the average treatment effect on the compliers. This, however, is only partially a drawback. If one is interested in the effect that compulsory schooling has in practice, rather than some hypothetical situation where all children suddenly attend schools, the estimated effect is the more interesting one.

Naïve regression estimates do not suffer from drawbacks like locality and a limited set of compliers. However, as for instance Edmonds (2008) argues, they are likely to be

5

Only Two -Stage Least Square estimates are presented in this paper. However, the reduced form point estimates can be easily attained through scaling by the first stage estimates.

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confounded. Wealthier families, for example, can be hypothesised to be more likely to send their children to school and at the same time have their children perform less child labour. I report a summary of correlational estimates as a benchmark. Both, uncontrolled OLS estimates (i.e. correlations), as well as estimates that are controlled for age, age squared and gender are presented. Contrasting the resulting figures with the causal estimates that we gained in the regression discontinuity design allows us to gauge whether correlational estimates can lead us to draw wrong conclusions.

Two kinds of test on the validity of the identifying assumptions of these estimates are performed. The first one is a test on whether the density of cases changes around the cut-off, as suggested by McCrary (2007). A change in the density of cases around the cut-off would be an indication that subjects are able to manipulate the running variable and therefore would compromise the validity of the design. The other test that is performed is a test on whether the gender composition changes around the cut-off. It is common practice to test whether other determinants of the outcome significantly change around the cut-off (Athey & Imbens, 2016). If a significant change is detected, this is an indication that the estimate is biased towards the correlation rather than the causal impact. As can be seen in Section 5 (Data), there are not many determinants of child labour in the data that are not at the same time potentially outcomes of child labour. However, the gender of a child does not change in response to child labour, whereas multiple authors note that gender influences both the amount and kind of work that children perform (Assaad, Levison, & Zibani, 2007; Edmonds, 2008).

Section 5: Data

As many studies on child labour before (see Edmonds (2008)), I will draw data from UNICEF’s Multiple Indicator Cluster Survey (MICS) (UNICEF, 2012, UNICEF, 2013). This choice was based on scope of the MICS, rather than on its quality.

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The first necessity of the regression discontinuity design is many cases close to the cut-off. Therefore, all datasets that survey the general population or children of all ages with only standard sample sizes of a few thousand cases could not be used. UNICEF’s MICS, often have increased sample sizes to ensure representativeness in subgroups. The generally larger sample sizes also ensure that there are more cases around the cut-offs. Furthermore, MICS carried out 294 surveys in 107 countries employing a comparable methodology (UNICEF, 2013). Therefore, in theory, 294 single estimates can be created. The large sample sizes together with the large collection o f comparable surveys make the MICS the only suitable dataset to create the proposed estimates.

The proposed estimating procedure demands these large numbers of cases because of three reasons. First of all, as already mentioned, regression discontinuity designs, especially non-parametric ones, demand many cases around the cut-off (Angrist & Pischke, 2008). Second, precise fuzzy regression discontinuity designs demand large numbers of cases. Even experienced researchers are often surprised by how little power regression discontinuity designs have (McKenzie, 2016). It is not uncommon to require sample sizes in a different order of magnitude in fuzzy regression discontinuity designs than in a randomised controlled trial. Third, the prevalence of child labour at young ages and effective institutions at the same time is rare. As it was often noted, child labour is strongly linked to poverty (Edmonds, 2008). At the same time, effective institutions are strongly linked to wealth (Acemoglu et al., 2001). This makes most countries fall into one of the two categories: Either compulsory schooling laws are effective but there is a low prevalence of child labour. Or the prevalence of child labour is high but institutions are weak and therefore compulsory schooling laws are not strongly enforced. There are only few notable exceptions, such as Peru, where compulsory schooling laws are effective (Singh, 2016) and where child labour is relatively prevalent (ILO & MTPE, 2016). However, for these cases, no data could be acquired at the necessary scope.

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Therefore, the strategy chosen to achieve precise estimates was to use data with large sample sizes.

The drawback of the MICS is the quality of the data. These surveys are not intended as a basis for complex inferential studies like this one. Their main purpose is to inform policy makers about core statistics, mainly on women and children. For example, MICS was a major source of data for the Millennium Development Goals indicators. However, it provides little contextual data, such as indicators on income, expenditures or consumption. Some of the variables might also not be recorded in the most scientifically sound way. For instance, child labour was recorded by asking the household head about child labour activities with a recall period of one week. There have been complaints that data on child labour generally is not recorded in optimal ways (Edmonds, 2008). However, as Dammert and Galdo (2013) note, the chosen method is likely to underreport child labour, because household heads perceive it to be socially desirable to report a lower incidence of child labour. Furthermore, no internal consistency checks are made. For example, there is no indication (neither provided theoretically, nor through varying survey items) how robust the data is to altering the respondent or the recall period.

In addition, school attendance is not described in a detailed way in the data. The item that will be used for the variable schooling in this paper, simply asks whether somebody ever attended the first class of primary school. There is no data on the intensity of school attendance. Furthermore, there again is no indication on the robustness of the item.

To use the full MICS data would not have been feasible within the limits of the thesis project. Therefore, a preselection based on geography, time and age of children was undertaken. Only countries in Asia and Sub-Sahara Africa were considered. I made this choice, because the prevalence of child labour is the highest on those two continents. Furthermore, only MICS of round four and five were considered, the last two ro unds that are

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publicly available. The data for these two rounds was collected between 2010 and 2014. This time period follows the quick expansion of primary schooling in developing countries. Therefore, I hoped to find more pronounced effects of mandatory schooling laws. Furthermore, I restricted my sample to children of the age five to nine. The lower bound of five years old was dictated by the data. The MICS administer the child labour item to children which are five years old or older. The upper bound of nine was deducted to be a good high cut-off. A restriction of the sample was necessary, because otherwise it would have become too large for computationally efficient estimation. This is especially true for the search procedure, where many candidate regression discontinuities are estimated in each country. If the legal mandatory schooling age is seven, the maximum observed, children that are just not yet affected by it are at most eight years old at the time of the interview. To this another year was added for the bandwidth of the regression discontinuity estimate, yielding a sample restriction of nine years old at the top.

Table one and figure one give an overview over the geographical scope and timing of the data collection. In total samples of 35 location-years are included. Most of them are national in their representation, with some of them only being representative at a lower administrational level. 15 of the 35 samples are from Asia. The total number of cases is in excess of 200 000 with almost precisely half of them being African. The single samples are vastly different in size. While the sample for Punjab in Pakistan contains more than 50 000 cases, the Turkana province in Kenya is only represented by 155 cases.

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Table 1: Sample List

CID Country Representation Year N

BT10 Bhutan National 2010 3858 CF10 Central African Republic National 2010 7878 TD10 Chad National 2010 8718 CD10 Congo-Kinshasa National 2010 9051 CM14 Cameroon National 2014 2063

GH(AC)10 Ghana Accra 2010 425

GW14 Guinee-Bissau National 2014 1744

ID(PA)11 Indonesia Papua province 2011 1404

ID(WP)11 Indonesia West Papua

province

2011 1467

KE(BU)13 Kenya Bungoma province 2013 286

KE(KA)13 Kenya Kakamega

province

2013 248

KE(TU)13 Kenya Turkana province 2013 155

ML09 Mali National 2009 13022

MG(SO)12 Madagascar South 2012 1908

MW13 Malawi National 2013 6666

MR11 Mauritania National 2011 5344

MN10 Mongolia National 2010 3387

MN13 Mongolia National 2013 2518

MN(KA)11 Mongolia Khuvsgul Aimag

province

2011 655

MN(NA)11 Mongolia Nalaikh province 2011 316

NP14 Nepal National 2014 1491

NP(WE)10 Nepal Mid Far Western

region

2010 4252

NG11 Nigeria National 2011 20254

PK(BA)10 Pakistan Balochistan 2010 5090

PK(PU)11 Pakistan Punjab 2011 51099

PK(PU)14 Pakistan Punjab 2014 6049

PK(SI)14 Pakistan Sindh 2014 3675

SL10 Sierra Leone National 2010 7750

SZ10 Swaziland National 2010 2706

ST14 Sao Tome and

Principe

National 2014 755

SO(NE)11 Somalia Northeastern

region

2011 4601

SO(SL)11 Somalia Somaliland 2011 4104

TG10 Togo National 2010 4485 VN10 VietNam National 2010 3093 VN13 VietNam National 2013 15060 N-weighted Average: 2011 Sum: 205578 of which 102164 are African

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Figure 1: Sample map

Table 2 presents an overview over the children in the sample. O n average they are seven years and three months old. Slightly more than half of the children attend a school and slightly more than half perform any work. A bit less than half are female. Most of the children that do any work, do household work (98 percent). O nly 9.4 percent of children in the sample perform market work. O n average, a child in the sample works for 4.2 hours per week, of which 3.3 are household work and 0.9 are market work. However, as the high standard deviations indicate, the work is concentrated among a subset of children.

Children that are close to the deducted cut-off are more than a year younger, less likely to be in school, more female and work less in all categories. Children that are in the subsample of the nine countries that were analysed in the third part are almost a year younger than the sample average, attend school more often and work less in all categories, except for the incidence of market work.

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Table 2: Summary Statistics Sample mean (SD)

+/- 3 months from deducted cut-off

+/- 3 months from cut-off in Two-Stage Least Squares estimates

Age 87.98 (17.06) 72 (7.21) 76.85 (9.01) In School 54.87 (49.76) 39.6 (48.91) 61.67 (48.63) Female 48.6 (50.0) 49.03 (50.0) 48.65 (50) Doing any work 52.91 (49.91) 39.59 (48.9) 39.96 (48.99) Hours per week 4.18 (8.72) 2.5 (6.65) 2.76 (8.42) Doing market work 9.39 (29.17) 6.34 (24.36) 10.1 (30.14) Hours per week 0.85 (4.3) 0.48 (2.97) 0.55 (2.83) Doing HH work 51.71 (49.97) 38.69 (48.7) 38.9 (48.76) Hours per week 3.33 (6.76) 2.03 (5.38) 2.21 (7.11)

Table 3 presents the discontinuity points that were used in the first two parts of the analysis. The deducted discontinuity points were taken from EPDC (2014). The discontinuity points that were deducted do not conform to a specific age at the time of the interview, because the interviews took place over a period of time. In most countries, compulsory schooling sets in at the beginning of a school year if a child is six years old at this point in time. This is also the system prevalent in France, the United K ingdom and Italy ("Family,"; Government Digital Service, 2017; Service Public, 2017). Most countries in the sample have been colonised by one of the three and largely copied general features of their educational system. I tried finding the specific enrolment guidelines for each country. However, I was usually not able to find them. For some countries they are not precisely specified by law (e.g. Chad, where only the constitution mandates compulsory schooling in general ways), whereas some countries have official languages that I do not understand and where no secondary sources were identifiable through a web-search (e.g. Bhutan). For some countries I was able to interview sources (e.g. Somalia and Indonesia) that could confirm that the official guidelines are ones where the age at the beginning of the school year determine the compulsory schooling status. Therefore, I assumed the probably most common way to assign

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compulsory schooling, meaning that a child which is of mandatory schooling age at the start of the school year has attend a school.

There are two other systems in use to determine compulsory schooling. O ne is revolving enrolment, such as in the Netherlands for instance, and one is a shifted reference date compared to the start of the school year, such as identified in Vietnam. While the formerly stated approach is not able to identify them, the other two search techniques are reliably showing pronounced discontinuities. Revolving dates are captured by the search procedure. If any child who just turned six has to attend a school, regardless of the time in the school- year, for instance, we expect to see a cut-off in school attendance over age at the time of the interview (such as in Guinee-Bissau). The other situation is when the reference date is another one than the start of the school year. In Vietnam, for instance, the reference date seems to be the turn of the year. These rules are reliably identified with visual identification.

In some countries, this compulsory schooling age is five or seven years instead of six years. Compulsory schooling ages of five may be problematic, because the discontinuity may be close to the lower end of the range of the data. Fortunately, the low compulsory schooling ages were primarily found in countries with large sample-sizes, where a small bandwidth is sufficient for estimation.

The detected discontinuities are the result of an estimation procedure, the results of which are described in more detail in Appendix 1 (Search Procedure). At this point, one can note that the detected points are spread across almost the whole range of possible candidate discontinuities and that they are not robust to the polynomial fit employed for estimation. Only in four of the 35 cases both fits return the same discontinuity.

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Table 3: Regression Discontinuity Points Part One and Two CID Mandatory schooling age Start of school year Found discontinuity first order polynomial at age Found discontinuity second order polynomial at age BT10 6 February 6.00 6.42 CF10 6 October 8.67 6.25 TD10 6 October 7.00 8.58 CD10 6 September 8.83 8.67 CM14 6 September 5.58 5.58 GH(AC)10 6 September 5.56 5.83 GW14 6 October 8.42 8.75 ID(PA)11 7 July 6.67 5.83 ID(WP)11 7 July 6.00 6.00 KE(BU)13 6 January 8.17 0.00 KE(KA)13 6 January 8.08 7.25 KE(TU)13 6 January 7.00 7.67 ML09 7 October 8.83 6.58 MG(SO)12 6 October 6.75 5.67 MW13 6 September 7.92 6.67 MR11 6 October 7.00 7.50 MN10 6 September 6.75 6.33 MN13 6 September 5.83 6.25 MN(KA)11 6 September 6.58 7.08 MN(NA)11 6 September 6.42 6.42 NP14 5 May 7.00 6.67 NP(WE)10 5 May 7.00 9.00 NG11 6 September 8.58 5.75 PK(BA)10 5 April 7.00 8.50 PK(PU)11 5 April 9.17 0.00 PK(PU)14 5 April 6.25 6.92 PK(SI)14 5 April 6.58 7.50 SL10 6 September 8.92 7.50 SZ10 6 January 5.92 5.67 ST14 6 October 6.42 7.00 SO(NE)11 6 October 8.00 5.83 SO(SL)11 6 October 8.50 5.42 TG10 6 September 5.67 0.00 VN10 6 September 7.00 7.00 VN13 6 September 7.08 7.50

Table 4 presents the discontinuity points that were visually identified. A detailed description of the procedure can be found in Appendix 2 (Visual Identification). The same discontinuity points were employed for the same country. Otherwise there is little similarity between the rules.

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Table 4: Regression Discontinuity Points Part Three

CID Rule

BT10 Found cut-off from search procedure (six years old)

GW14 Found cut-off from search procedure (eight years and five months old) KE(KA)13 Legal cutoff

MN10 Mandatory schooling age of five years and ten months simulated, otherwise legal cutoff

MN13 Mandatory schooling age of five years and ten months simulated, otherwise legal cutoff

MN(KA)11 Mandatory schooling age of five years and ten months simulated, otherwise legal cutoff

ST14 School start in December simulated, otherwise legal cutoff

VN10 Mandatory schooling age of five years and nine months simulated, otherwise legal cutoff

VN13 Mandatory schooling age of five years and nine months simulated, otherwise legal cutoff

Section 6: Results

Deducted Cut-Offs

Table 5 shows that generally no significant regression discontinuity can be found at the deducted compulsory schooling cut-off. The aggregated estimate, across specifications, is close to zero with confidence intervals as small as four percentage points. Ten of the 35 single estimates are large and significantly negative in the first order polynomial. There are three explanations why this could be the case. Either, (1) there is a true negative effect, (2) the effect occurred by chance or (3) the negative estimated effect is due to misspecification. There is no reasonable explanation for why these estimates are negative. Therefore, a true negative effect seems unlikely. Furthermore, too many of the estimates are too significantly negative to occur by chance alone. We would expect one out of the 35 estimates to be significantly negative by chance alone. Ten estimates, generally being significant at even lower levels than the conventional 95% confidence is extremely unlikely. Therefore, I conclude that the negative estimates are mainly the result of misspecification. The visual investigation of three exemplary cases in figure 2 confirms this intuition. In the graphical representation, estimates seem less negative than in the table, because it does not incorporate bias correction. The bias

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correction term makes the estimates more negative (Calonico et al., 2014b), sometimes substantially so. However, the applied procedure proposed by Imbens and Kalyanaraman (2012) does not adjust confidence intervals to the bias correction. Calonico et al. (2014a) propose to inflate the confidence intervals according to their bias correction, which would particularly decrease the significance of the estimates that are found to be statistically significantly negative here.

Furthermore, the significantly negative estimates are typically not robust to changing the polynomial order. O nly three second order polynomial estimates of the significantly negative first order polynomial estimates are also significantly negative and within the confidence interval of the first order polynomial estimate.

Four estimates are significant and carry the expected positive sign. However, these estimates, are also not coherent with their second order polynomial specification. Bandwidths are generally within the expected range. In the preferred aggregated estimate, which is the first order polynomial, efficiently weighted estimate, the mean bandwidth is 5.6 months. Due to the non-parametric procedure, this means that the difference between the children one month too old and one month too young to be affected by the mandatory schooling law receive close to 25% of the weight. This also explains why only slight deviations from the actual enrolment rule can lead to insignificant or even counter- intuitive results. I conclude that there is no indication that, generally, the legally stated compulsory schooling rule has a significant effect on school attendance. Therefore, either compulsory schooling legislation is not strictly adhered to or the data on compulsory schooling laws provided by EPDC (2014) or the interpretation of this data is faulty.

Does compulsory schooling prevent child labour? : evidence from 35 quasi-experiments in Africa and Asia

Contents

Section 1: Introduction

Section 2: Literature Review

Section 3: Theory

Section 4: Empirical Design

Section 5: Data

Section 6: Results