## Abstract

This paper uses a natural experiment from Egypt to examine the effect of extending compulsory schooling on long-term educational and labor market outcomes. Beginning in school year 2004–05, the Egyptian government extended primary education from five to six years, moving from an eight-year compulsory schooling system to a nine-year system. Using a regression discontinuity design, I examine whether the compulsory schooling expansion affects years of schooling, literacy and cognitive skills, post-primary attendance, and labor market outcomes of individuals born just around the 1992 school entry cutoff. The results suggest that an extra year of compulsory education increases total years of schooling by 0.6 to 0.8 years. This effect, however, is concentrated among male individuals. In particular, I find that the school reform increases the schooling gap between male and female students by somewhere between 0.30 and 0.48 years. I also find no effect of expanding compulsory education on individuals’ literacy skills, schooling beyond the primary education level, or labor market outcomes. There is some evidence, however, that the school reform has improved reading and self-reported writing skills among male individuals.

## 1.  Introduction

Over the last few decades, many developing countries have experienced substantial increases in school enrollment. Between 1999 and 2009, for example, the number of children attending primary education has risen by 59 percent in sub-Saharan Africa, 28 percent in South and West Asia, and 17 percent in the Arab states (UNESCO 2011). These large gains in enrollment, however, were not accompanied by comparable improvements in educational attainment or learning outcomes (UNICEF 2016; World Bank 2017). For instance, between 2009 and 2015, 74 percent of children of primary school age in sub-Saharan Africa, 80 percent in South Asia, and 90 percent in the Middle East and North Africa (MENA) region attended primary school. However, during the same period, only 58 percent of children aged three to five years above primary graduation age in sub-Saharan Africa, 67 percent in South Asia, and 80 percent in the MENA region have completed primary education (UNICEF 2016). Overall, the current levels of educational attainment in developing countries resemble those in developed countries in the late 1960s (Barro and Lee 2013).

To address this enrollment-attainment gap, policy makers in developing countries have adopted a wide range of policy interventions (Orazem and King 2007; Glewwe et al. 2011). Some of these interventions focus on the demand side for schooling, such as conditional cash transfers and school vouchers (Rawlings and Rubio 2005; Angrist, Bettinger, and Kremer 2006; Lagarde, Haines, and Palmer 2009), whereas others rely on supply-side policies such as school construction and teacher training (Duflo 2001; Glewwe 2002; Glewwe et al. 2011). A third group of policies includes extending compulsory education (Spohr 2003; Tsai et al. 2009; Kirdar, Dayioğlu, and Koç 2016).

Although the evidence on both demand-side and supply-side policies is extensive, little is known about the effects of extending compulsory schooling in developing economies. The majority of the existing literature on compulsory education focuses on developed countries. The findings from this literature suggest that expanding compulsory school raises educational attainment (Lleras-Muney 2002; Oreopoulos 2006), increases earnings (Angrist and Krueger 1991) and lifetime wealth (Oreopoulos 2007), reduces wage inequality (Brunello, Fort, and Weber 2009), and improves nonpecuniary outcomes (Lochner and Moretti 2004; Grossman 2006; Black, Devereux, and Salvanes 2008).

The extent to which extending compulsory schooling in developing countries produces similar effects to those estimated for developed countries is unclear. On one hand, human capital is scarce in developing countries because of the low levels of educational attainment, therefore, the return to education expansion is expected to be larger. That is, raising the number of compulsory school years may have a larger effect on educational attainment in developing countries. Furthermore, expanding compulsory education may improve the knowledge and cognitive skills of individuals in a way that increases their preparedness to pursue higher levels of education. On the other hand, the literature on compulsory schooling in developed countries suggests that most of those affected by expanding the compulsory education are individuals at the low end of the education distribution. If the same conclusion holds for developing countries, then extending compulsory education would have little effect on long-term educational attainment. Furthermore, given the low quality of education in many developing countries (Chaudhury et al. 2006), expanding compulsory education may not generate large improvement in students’ knowledge or cognitive skills, and, as a result, the long-term effects on attainment would be minimal. Also, related to the previous point, if expanding compulsory schooling was not accompanied by increasing school resources that enable schools to hire more teachers or build new classrooms to accommodate the increasing number of students, then it would have adverse effects on school quality.

In this paper, I use a natural experiment from Egypt to investigate the effect of extending primary schooling on long-term educational attainment and labor market outcomes in addition to other nonpecuniary outcomes. Beginning in the school year 2004–05, the Egyptian government increased the number of primary school years from five to six, moving from an eight-year compulsory education system to a nine-year system. This policy reform was mandatory, affecting all individuals who were born on or after 1 October 1992. Using a regression discontinuity design, I compare educational attainment and labor market outcomes of individuals born just before and just after that date. Results suggest that extending compulsory education has a large positive effect on educational attainment. Individuals who received an extra year in compulsory education have completed, on average, 0.6 to 0.8 more years of schooling than those who were not affected by the compulsory school reform. This effect, however, is greater for male than female individuals. In particular, I find that the school reform increases the gap in total years of schooling between males and females by somewhere between 0.30 and 0.48 years of schooling, depending on model specification. I also find no effect of expanding compulsory schooling on individuals’ literacy skills, schooling beyond the primary education level, or labor market outcomes. There is some evidence, however, that the school reform has improved reading and self-reported writing skills among male individuals.

This paper contributes to the existing literature on expanding compulsory education in three main ways. First, the paper is one of the few studies that examines the effects of expanding compulsory education in developing countries. Although there is a large body of evidence on returns to compulsory education in developed countries, the generalizability of this evidence to developing countries is questionable. The reason is that, as discussed before, differences in school quality, educational attainment, and levels of compliance with the compulsory education laws between developed and developing countries would affect the extent to which compulsory school expansion produces similar results. Second, the existing evidence on the effects of expanding compulsory schooling in developing countries relies mainly on total years of education to measure the schooling effects resulting from expanding compulsory education. Although total years of schooling is an important measure of educational attainment, it does not capture the effect of compulsory education on student learning outcomes. In fact, the large gains in school enrollment in developing countries over the last few decades have not been translated into comparable improvements in learning outcomes. For example, in a recent report, the World Bank estimates that “more than 60 percent of primary school children in developing countries still fail to achieve minimum proficiency in learning” (World Bank 2017, p. 8). This paper uses a rich data set that allows one to estimate not only the effect of expanding compulsory education on total years of schooling, but also its effects on learning outcomes, such as literacy skills and performance in high school. Third, the paper examines the effects of the 1999 Egyptian school reform, which differs from other compulsory school reforms in developing countries in two ways. First, the Egyptian school reform created an additional year of primary schooling that did not exist before. This is different from other compulsory school reforms in countries such as Turkey and Taiwan, which expanded compulsory education by including school years from the post-compulsory level as part of compulsory education.1 In particular, this paper focuses on estimating the long-term effects of adding a sixth year to primary education. Second, unlike other compulsory school reforms, the 1999 school reform affected not only individuals at the margin of dropping out of compulsory education, it also affected individuals who are pursuing post-compulsory education. The reason is that the reform increased the total number of years required to obtain general secondary education from eleven to twelve years and college education from fifteen to sixteen years.

The paper is organized as follows. Section 2 reviews the existing literature on the returns to extending compulsory education. Section 3 describes the Egyptian education system. Section 4 presents descriptive statistics for the sample, and section 5 introduces the identification strategy. In sections 6 and 7, I discuss the baseline results and examine whether the effects of the school reform vary by gender and place of residence. In section 8, I test the sensitivity of the results to multiple robustness checks, and section 9 discusses the nonpecuniary returns to expanding compulsory schooling. Section 10 concludes.

## 2.  Returns to Expanding Compulsory Schooling

The basic human capital model views education as an investment decision. According to the model, individuals invest in schooling as long as the present discounted value of anticipated benefits from attending an extra year of education exceeds the anticipated costs (Becker 1962). From this perspective, enforcing a minimum level of schooling, either in the form of imposing a minimum school-leaving age or forcing individuals to attend school for a certain number of years, may result in private and social welfare losses. The reason is that compulsory education forces individuals who would otherwise invest in a smaller number of years of schooling to stay in school longer. However, imposing a minimum level of education is often justified based on three main rationales: positive externalities, bounded rationality, and equity (Boissiere 2004). First, investing in compulsory education creates large spillover effects that extend beyond the individual return to schooling, such as creating an educated workforce, improving public health, and enhancing civic and democratic values. Second, government intervention in compulsory education can also be justified based on the notion that some individuals may irrationally underestimate the benefits of schooling because they lack information about these benefits, they are more present-oriented, or for a variety of other reasons. Finally, many policy makers believe that the government should provide equal access to a minimum level of education for each individual.

Whether extending compulsory education results in long-term gains (which represents the justification for government intervention) or leads to private and social welfare losses as predicted by the human capital model is an empirical question. The existing evidence from developed countries on returns to compulsory schooling, however, is mixed. Some prior research suggests that expanding compulsory education leads to substantial gains in schooling, earnings, and other long-term outcomes. For example, Angrist and Krueger (1991) and Acemoglu and Angrist (2000) found that staying a year longer in school increases annual earnings by 10 percent. Similarly, Oreopoulos (2006, 2007) found that an extra year of compulsory education increases lifetime wealth by 15 percent. His findings also suggest that students compelled to stay in school are also less likely to report being in poor health, unemployed, and unhappy. Evidence from recent literature, however, shows that returns to compulsory schooling in developed countries are either nonexistent or much smaller, in terms of magnitude, than those reported in the previous literature (Devereux and Hart 2010; Stephens and Yang 2014). Stephens and Yang (2014), for instance, found that the significant effects associated with compulsory education on earnings and employment disappear once they control for state-specific trends. In addition, Devereux and Hart (2010) were not able to replicate the large returns to compulsory schooling in the United Kingdom, as reported by Oreopoulos (2006). Instead, their findings suggest that returns to compulsory schooling are smaller among men (between 4 and 7 percent) and zero among women.

In contrast to the large literature on developed countries, few studies have examined the effect of expanding compulsory education on schooling and labor market outcomes in developing countries. For example, Spohr (2003) found that the 1968 expansion of compulsory education in Taiwan from six to nine years has increased total years of schooling by 0.4 for men and 0.25 for women. His results also show that an additional year of schooling increases annual earnings by 5.8 percent for men and 16.7 percent for women. Tsai et al. (2009) investigate the effect of the same reform on the gender disparities in the labor market in Taiwan. They found that an additional year of schooling increases the probability of women's employment in sectors such as manufacturing and commerce by 6 percent, with a roughly comparable reduction in the probability of employment in the agricultural sector. The findings from Tsai et al. (2009) also suggest that more than one third of the change in the gender employment gap in the agricultural, manufacturing, commerce, and private sectors is attributed to the 1986 school reform. Kirdar, Dayioğlu, and Koç (2016) examine the effects of expanding compulsory education in Turkey from five to eight years on gender and regional disparities in educational attainment. They found the compulsory school reform has reduced the rural–urban gap in completed years of schooling by 0.5 years for men and by 0.7 to 0.8 years for women. There is no evidence, however, that the reform has affected the gender gap in schooling.

Several other studies have focused on the non-labor market returns to compulsory schooling such as women's fertility and children's outcomes (Chou et al. 2010; Dincer and Erten 2015; Grépin and Bharadwaj 2015; Ali and Elsayed 2018; Ali and Gurmu 2018). For example, Dincer and Erten (2015) use the 2012 expansion of compulsory education from eight to twelve years in Turkey to examine the effect of high school attendance on child labor and idleness. Their results suggest that the compulsory school reform increased high school attendance by 3.8 percent and reduced the likelihood of working for a wage, especially in the nonagricultural sectors and in jobs that are seasonal or temporary in duration. Gunnarsson, Orazem, and Sanchez (2006) use the cross-country variation in compulsory school laws to examine the effect of child labor on student achievement in Latin American countries. Their findings suggest that child labor significantly reduces student performance in mathematics and language. Ali and Gurmu (2018) examine the effect of maternal education on fertility in Egypt using the 1988 school reform, which reduced the length of primary school from six to five years, as a source of exogenous variation in maternal education. They found that maternal education reduces the number of children born per woman. Following a similar approach, Ali and Elsayed (2018) use the same reform to investigate the intergenerational effects of parental education on child health. Their results suggest that parental education has no impact on child mortality or nutritional status.

## 3.  Education System in Egypt

With more than 19 million students enrolled in the pre-university education in school year 2014–15, Egypt has one of the largest education systems in the MENA region. The Egyptian pre-university system is divided into two levels: basic and secondary education. Basic education starts at age six years and is mandatory for all individuals of that age. It covers two stages: primary (grades 1–6) and preparatory (grades 7–9). Upon completion of basic education, students transition to either general secondary (three years) or technical/vocational secondary schools (three to five years).

Between 1988 and 1999, basic education consisted of eight years (grades 1–8): five years of primary school and three years of preparatory school. In 1999, however, the Egyptian government passed a law (Law No. 23 for 1999) that extended basic education to nine years, adding an extra year to primary school. The 1999 law was intended to reverse a government policy that reduced primary school from six to five years beginning in 1988.2 The rationale behind the 1999 reform was that Egyptian students in primary schools were spending less time in basic education compared with students in other developing countries and, therefore, were not gaining enough knowledge or skills that prepare them for post-primary education. Allowing students to spend more time in primary school, government officials argued, would improve their cognitive skills, reduce dropout rates, and increase educational attainment, especially among disadvantaged children.

The 1999 school reform resulted in three changes: an addition of an extra year to primary school, changes in school infrastructure, and a reduction in enrollment in post-primary education. This paper focuses only on the effect of adding an extra year to primary school on individuals’ educational and labor market outcomes because changes in school infrastructure and the decline in post-primary enrollment affected all students, regardless of whether or not they were affected by the addition of the sixth grade. To the extent that students from the treatment and comparison groups react similarly to changes in school infrastructure or post-primary enrollment, the estimated effects of the six-year system are not expected to be biased. First, the reform increased the number of years of primary school from five to six years. Although extending primary education to six years was announced in 1999, it was first implemented in school year 2004–05. In particular, students who completed fifth grade in school year 2003–04 moved to the sixth grade of primary school rather than starting their first year of preparatory school. Given that, in Egypt, a child must turn six before 1 October in order to attend primary education, the first school cohort affected by the new primary system includes individuals who were born on or after 1 October 1992.

Second, in an anticipation of the rise in primary school enrollment resulting from adding an extra year to primary education, the government adopted a plan to construct new schools and to add more classrooms to existing schools. However, because of lack of funding, the actual increase in the number of schools was small and, therefore, not sufficient to accommodate the large rise in primary school enrollment. As shown in table 1, between 2002–03 and 2006–07, the number of schools increased by 3.2 percent at the primary level and 1.1 percent at the preparatory level. During the same period, enrollment in primary education increased by 23.9 percent, from 6.6 million to 8.2 million students. Because of the limited number of new schools, the government relied mainly on re-assigning existing classrooms in preparatory schools to primary school students. For example, between 2002–03 and 2006–07, the number of classrooms in primary school increased by 16.8 percent while the number of preparatory schools’ classrooms declined by 25.8 percent. It should also be noted that, unlike the new six-year primary system, which only affected students who were in fifth grade in 2003–04, the changes in school infrastructure, which were announced in 1999, affected all students attending primary school after 1999–2000, including both students who were subject to the five-year system and those who were subject to the new six-year system. For example, students from the control group who attended primary education after 1999, when the reform was announced, but finished their fifth grade before 2003–04, were affected by the changes in school infrastructure but not the extra year in primary school. In contrast, students who were first enrolled in primary school starting from 1999–2000 were affected by both changes in infrastructure and the six-year system.

Table 1.
Number of Schools, Classes, and Students in Egypt (2002—03 through 2006—07)
SchoolsClassesStudents
YearPrimaryPreparatoryPrimaryPreparatoryPrimaryPreparatory
2002—03 14,609 7,023 158,902 91,302 6,585,748 3,928,204
2003—04 14,792 7,309 159,809 90,670 6,639,757 3,841,694
2004—05 14,951 7,447 183,249 66,573 7,939,554 2,628,475
2005—06 14,963 7,621 184,317 66,138 8,078,202 2,558,337
2006—07 15,074 7,762 185,538 67,729 8,160,236 2,623,311
SchoolsClassesStudents
YearPrimaryPreparatoryPrimaryPreparatoryPrimaryPreparatory
2002—03 14,609 7,023 158,902 91,302 6,585,748 3,928,204
2003—04 14,792 7,309 159,809 90,670 6,639,757 3,841,694
2004—05 14,951 7,447 183,249 66,573 7,939,554 2,628,475
2005—06 14,963 7,621 184,317 66,138 8,078,202 2,558,337
2006—07 15,074 7,762 185,538 67,729 8,160,236 2,623,311

Source: Egyptian Ministry of Education (2008).

Third, the 1999 reform resulted in a reduction in enrollment in post-primary education. However, similar to changes in school infrastructure, the decline in enrollment affected students regardless of their treatment status, that is, whether or not they were affected by adding an extra year of primary education. For example, during the first year of implementing the new six-year primary system (2004–05), preparatory schools did not admit new students because those who were supposed to start their preparatory education in that year had to attend an extra year of primary school. During that year, there were only two cohorts of students attending preparatory schools: the second-year cohort and the third-year cohort. Students in both cohorts were born prior to the cutoff date. Similarly, during the following year, 2005–06, only two cohorts of students attended preparatory school: the first-year cohort and the third-year cohort. However, whereas the third-year cohort consists of students who were subject to the five-year primary system, students in the first-year cohort were affected by the new six-year system.3

## 4.  Data

The data for this study come from the 2014 Survey of Young People of Egypt (SYPE). The first round of SYPE was conducted in 2009 on a nationally representative sample of individuals aged ten to twenty-nine years. The 2014 round of the survey followed the same individuals five years after the initial interview (Roushdy and Sieverding 2015). There are two main advantages of the SYPE data set. First, in addition to providing basic demographic characteristics, the survey includes rich information on individuals’ schooling and learning outcomes such as literacy skills, wealth, and labor force participation. Second, for the purpose of this study, SYPE collects information on month and year of birth, which allows one to identify individuals who were affected by the school reform using month of birth.

### Treatment Variable

To identify the treatment status, I use information on month and year of birth for individuals in the sample. The new six-year primary school system was first implemented in school year 2004–05, affecting all students who completed their fifth grade in the previous school year. Given the fact that, in Egypt, a child has to turn six years old before 1 October in order to attend primary education, the first school cohort who was affected by the new primary system includes individuals who were born on or after 1 October 1992. Therefore, to measure the treatment status, I use a binary variable that takes the value 1 for individuals who were affected by the compulsory school reform, that is, those who were born on or after 1 October 1992, and zero otherwise.

### Schooling Outcomes

The 1999 school reform is expected to affect individuals’ educational attainment in several ways. First, the reform increased total years of schooling required to complete compulsory education from eight to nine years and secondary education from eleven to twelve years. Second, adding an extra year to primary education may discourage some individuals from attending school or make it difficult to complete primary school. Third, spending more time in primary school may also improve the knowledge and skills of students, and, as a result, increase their preparedness to pursue post-primary education. To examine these effects, I focus on four main schooling outcomes: (1) total years of schooling, (2) not attending primary school, (3) completing primary school, and (4) post-primary attendance. Years of schooling is measured as the total years of education that individuals attended. Not attending primary school is measured using a binary variable coded as 1 for individuals who did not attend primary school and zero otherwise. Completing primary education is also measured using a binary variable that takes one for individuals who completed their primary education. Similarly, post-primary attendance is coded as 1 for individuals who attended post-primary education or higher and zero otherwise.

### Labor Market Outcomes

In addition to estimating the effect on educational attainment, I examine whether extending compulsory education has improved individuals’ labor market outcomes. Two measures are used to capture the labor markets: labor force participation and employment status. Labor force participation is measured using a binary variable that is coded as 1 for individuals who are in the labor force and zero otherwise. Similarly, employment status is coded as 1 for individuals who were working for cash at the time of the survey and zero otherwise.

Table 2 provides mean characteristics for the full sample. As shown, 53 percent of individuals are female and 41 percent live in urban areas. The average number of years of schooling is 10.7. About 83 percent of individuals can read a simple sentence, 82 percent can write a letter, and 87 percent can do simple arithmetic. The share of employed individuals and those in the labor force are low in the sample. More than 60 percent of the sample are out of the labor force and only 31 percent are employed.

Table 2.
Descriptive Statistics
VariableObservationsMeanStandard DeviationMinimumMaximum
Demographic characteristics
Female 10,584 53.4 49.9
Age, years 10,584 23.4 5.7 13 35
Born on or after October 1992 9,786 37.8 48.5
Urban 10,584 40.8 49.2
Wealth quintiles
1st quintile 1,802 17.0 37.6
2nd quintile 2,031 19.2 39.4
3rd quintile 2,089 19.7 39.8
4th quintile 2,193 20.7 40.5
5th quintile 2,469 23.3 42.3
Schooling outcomes
Total years of schooling 8,832 10.7 3.2 24
Not attending school 10,581 11.7 32.2
Completing primary education 10,581 88.3 32.2
Completing post-primary education 10,581 80.1 39.9
Literacy and cognitive skills
Basic reading skills 10,571 82.8 37.7
Write a letter 10,570 82.0 38.4
Do simple arithmetic 10,571 87.3 33.3
High school test score 5,515 73.0 11.2 99
Labor market outcomes
Labor force participation 10,551 38.9 48.8
Employed 10,551 31.4 46.4
VariableObservationsMeanStandard DeviationMinimumMaximum
Demographic characteristics
Female 10,584 53.4 49.9
Age, years 10,584 23.4 5.7 13 35
Born on or after October 1992 9,786 37.8 48.5
Urban 10,584 40.8 49.2
Wealth quintiles
1st quintile 1,802 17.0 37.6
2nd quintile 2,031 19.2 39.4
3rd quintile 2,089 19.7 39.8
4th quintile 2,193 20.7 40.5
5th quintile 2,469 23.3 42.3
Schooling outcomes
Total years of schooling 8,832 10.7 3.2 24
Not attending school 10,581 11.7 32.2
Completing primary education 10,581 88.3 32.2
Completing post-primary education 10,581 80.1 39.9
Literacy and cognitive skills
Basic reading skills 10,571 82.8 37.7
Write a letter 10,570 82.0 38.4
Do simple arithmetic 10,571 87.3 33.3
High school test score 5,515 73.0 11.2 99
Labor market outcomes
Labor force participation 10,551 38.9 48.8
Employed 10,551 31.4 46.4

Table 3 presents the distribution of schooling in Egypt. Three points are worth mentioning. First, a large number of individuals in the sample have not completed primary education. In particular, 10.6 percent of individuals have no formal education and 1.1 percent can read and write but did not complete primary school. Second, the majority of individuals who attended school have completed either compulsory education (13.7 percent have completed preparatory school) or secondary education (44.2 percent have completed some type of secondary education). Third, there is a large gender gap in schooling in Egypt. For example, 14.6 percent of female individuals in the sample have no formal education compared with only 5.9 percent of male respondents. There are also rural–urban disparities in schooling. As shown in table 3, 14.0 percent of individuals living in rural areas have no formal education compared with 5.5 percent of those living in urban areas. The rural–urban gap is greater among those with postsecondary education. Particularly, 31.4 percent of individuals in urban areas have attended some type of postsecondary education compared with only 15.8 percent of those living in rural areas.

Table 3.
Education Distribution Among Young Egyptians by Gender and Place of Residence
GenderPlace of Residence
Full SampleMaleFemaleUrbanRural
Illiterate (no formal education) 10.57 5.90 14.64 5.46 14.09
Read and write 1.14 0.77 1.47 0.76 1.41
Primary education 8.15 8.92 7.47 7.73 8.44
Preparatory education 13.65 12.65 14.51 12.89 14.17
Secondary education 44.23 47.42 41.63 41.74 46.11
Postsecondary education 22.18 24.33 20.28 31.42 15.79
Total years of schooling 10.7 10.7 10.6 11.1 10.3
Observations 10,581 4,931 5,650 4,322 6,259
GenderPlace of Residence
Full SampleMaleFemaleUrbanRural
Illiterate (no formal education) 10.57 5.90 14.64 5.46 14.09
Read and write 1.14 0.77 1.47 0.76 1.41
Primary education 8.15 8.92 7.47 7.73 8.44
Preparatory education 13.65 12.65 14.51 12.89 14.17
Secondary education 44.23 47.42 41.63 41.74 46.11
Postsecondary education 22.18 24.33 20.28 31.42 15.79
Total years of schooling 10.7 10.7 10.6 11.1 10.3
Observations 10,581 4,931 5,650 4,322 6,259

## 5.  Identification Strategy

To examine the effect of extending compulsory schooling on educational and labor market outcomes, I use a sharp regression discontinuity (RD) design similar to that used by Ali and Gurmu (2018) and Ali and Elsayed (2018). A standard linear RD model can be specified as follows (Imbens and Lemieux 2008; Lee and Lemieux 2010):
$Yi=δ1+δ2Ti+δ3(Xi-c)+δ4Ti*(Xi-c)+αkZi+ɛi,$
(1)
where $Yi$ refers to the outcome of interest$;Xi$ is the forcing variable that represents date of birth for individual i, expressed in month and year of birth; $c$ is the cutoff date; $(Xi-c)$ denotes an individual's date of birth relative to the cutoff date; $Zi$ is a vector of control variables that includes gender, age, urban status, and wealth index; and $ɛi$ is an idiosyncratic error term. $Ti$ is the treatment variable that takes value 1 for individuals who were subject to the new six-year primary school system and zero otherwise.

The first school cohort affected by the new six-year primary system is composed of all students who completed fifth grade in school year 2003–04. Instead of starting their first grade of preparatory education in school year 2004–05, students in that cohort were required to attend the sixth grade of primary school. Given that in Egypt a child has to turn six before 1 October in order to attend primary education, the first school cohort affected by the new primary system includes individuals who were born on or after 1 October 1992. Therefore, 1 October 1992 represents a cutoff date such that individuals born on or after 1 October 1992 were subject to the new six-year primary systems and individuals who were born before 1 October 1992 were affected by the old five-year system.

I estimate the RD equation using a nonparametric kernel-based local linear regression that assigns more weights to observations closer to the cutoff date. The kernel regression estimates can be obtained by solving the following specification:
$min∑i=1N[Yi-δ1-δ2Ti-δ3(Xi-c)-δ4Ti*(Xi-c)-αkZi]2Kh(Ti,(Xi-c)),$
(2)
where $Kh(Ti,(Xi-c)$) represents a kernel weighting function with bandwidth h. I use the following weighting function in the analysis:
$Kh((Ti,(Xi-c))=max0,1-Xi-Ch.$
As a robustness check, I test the sensitivity of the results using two parametric methods: a standard local linear regression and a local polynomial (quadratic) regression. The standard linear regression is estimated using the same specification in equation 1, without imposing the kernel weighting function, whereas the local polynomial regression is specified as follows:
$Yi=β1+β2Ti+β3(Xi-c)+β4(Xi-c)2+β5Ti*(Xi-c)+β6Ti*(Xi-c)2+αkZi+ωi,$
(3)
where $(Xi-c)2$ represents the squared deviation in year-month of birth from the 1992 cutoff date.

I use a plug-in method developed by Imbens and Kalyanaraman (2012) to determine the optimal number of bandwidth. I also check the robustness of findings using two other methods: a cross-validation method created by Ludwig and Miller (2007) and a new robust method proposed by Calonico, Cattaneo, and Titiunik (2014a, b).5 All three methods produce similar results. Therefore, I only report the findings from the plug-in method. Furthermore, in the Robustness Check section, I examine the sensitivity of the results to a wide range of bandwidths.

A key assumption of the RD design is that the treatment variable is measured without error. There are two implications of this assumption. First, individuals fully comply with school entry laws. That is, primary schools only accept children who turn six before 1 October. Although this assumption may hold for the vast majority of children in primary schools, some schools may accept children who are a few months shy of legal school entry age in response to pressures from parents. Another implication is that individuals in the sample did not repeat any grades between the first and fifth grades. If individuals (especially those who were born just before 1 October 1992 and therefore assigned to the control group) have repeated one or more grades, then they would have been affected by the school reform. Any violation of these two implications will introduce measurement error to the treatment variable. Failure to account for this measurement error may bias the effect of the school reform because the classical assumption of the measurement error (i.e., the true value of the variable of interest is independent of the measurement error) does not hold in the case of a binary treatment variable. In fact, the true value of the treatment variable is always negatively related to the measurement error, which makes it very difficult to predict the direction of the bias. To account for these measurement issues, I restrict the sample to individuals who started primary school at age six and did not repeat any grades in primary school.

## 6.  Baseline Results

### Schooling Outcomes

I begin the analysis by examining the graphical relationship between year-month of birth, the assignment variable, and schooling outcomes. Figure 1 plots the effect of the 1999 school reform on years of schooling, primary school attendance and completion, and post-primary attendance. Across all graphs, the horizontal axis represents year-month of birth, centered on the 1 October 1992 cutoff date, and the vertical axis represents the outcome of interest.

Figure 1.

Discontinuity in Schooling Outcomes

Figure 1.

Discontinuity in Schooling Outcomes

As shown, there is a small discontinuous increase in years of schooling for individuals born just around the cutoff date, which suggests that individuals who were subject to the six-year primary system completed, on average, more years of schooling than those affected by the five-year system. Notice that the downward slope of years of education on the right side of the cutoff date is mainly driven by the young age of a large portion of individuals in the treatment group, most of whom are still attending school. Unlike years of schools, the 1999 school reform does not seem to affect any of the three other schooling outcomes. That is, there are no differences between individuals born around the 1992 cutoff date in the likelihood of not attending primary school, completing primary education, or pursuing post-primary education.

Regression estimates for the effect of the 1999 school reform on these schooling outcomes are reported in table 4. The first column presents the results from the nonparametric kernel RD regression and the second and third columns show the estimates from the standard local linear and local quadratic regressions, respectively. In panel (a), I examine the effect of expanding compulsory schooling on total years of education. Across all specifications, the 1999 school reform has a large positive impact on total years of education. An extra year of primary education increases years of schooling by somewhere between 0.63 (model 2) and 0.76 years (model 3). This large effect on total years of schooling is expected given that (1) the 1999 school reform increased the number of years of required to obtain compulsory education from eight to nine years and high school degree from eleven to twelve years, and (2) the majority of individuals who attend school in Egypt go on to finish their compulsory and high school education. Relatively few individuals drop out before completing their primary or preparatory degrees.

Table 4.
Regression Estimates for the Impact of Extending Compulsory Education on Schooling Outcomes
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Sample Mean
(a) Total years of schooling 0.688*** 0.631*** 0.764*** 10.7
(0.13) (0.126) (0.19)
[1,936] [1,975] [1,975] 11.7
(b) Not attending school −0.001 −0.002 −0.001
(0.001) (0.002) (0.001)
[1,936] [2,629] [2,629]
(c) Completing primary school 0.004 0.003 0.005 88.3
(0.003) (0.003) (0.004)
[4,399] [4,456] [4,456]
(d) Post-primary attendance 0.019 0.018 0.019 80.1
(0.014) (0.012) (0.016)
[4,399] [6,101] [6,101]
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Sample Mean
(a) Total years of schooling 0.688*** 0.631*** 0.764*** 10.7
(0.13) (0.126) (0.19)
[1,936] [1,975] [1,975] 11.7
(b) Not attending school −0.001 −0.002 −0.001
(0.001) (0.002) (0.001)
[1,936] [2,629] [2,629]
(c) Completing primary school 0.004 0.003 0.005 88.3
(0.003) (0.003) (0.004)
[4,399] [4,456] [4,456]
(d) Post-primary attendance 0.019 0.018 0.019 80.1
(0.014) (0.012) (0.016)
[4,399] [6,101] [6,101]

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, gender, urban status, and wealth quintile. Sample sizes are in brackets.

***Significant at the 99% confidence level.

Panel (b) provides the estimated effects for not attending primary school. Consistent with the graphical analysis, there is no evidence that expanding primary school from five to six years has discouraged individuals from attending school. Across all specifications, the estimated treatment effect is negative but cannot be distinguished from zero. Panels (c) and (d) present the estimated effects for completing primary school and attending post-primary education. As shown, the 1999 school reform seems to have positive effects on both outcomes. For example, the coefficient estimate for post-primary education in model 1 suggests that adding an extra year to primary schooling increases the likelihood of attending post-primary education by 1.9 percentage points with an upper bound of 4.8 percentage points, which is substantial from a policy perspective. However, none of the effects on completing primary schooling or pursuing post-primary education is statistically significant at the conventional levels.

### Learning Outcomes

Although years of schooling and other measures of schooling outcomes are commonly used to estimate the effect of expanding compulsory education on educational attainment, it provides little information regarding whether this expansion has improved student learning. This is particularly important in the context of the Egyptian school reform. The reason is that a key rationale behind adding an extra year to primary school was that Egyptian students were spending fewer years in primary school compared with students in other countries and, therefore, many of them were graduating without acquiring the basic skills that prepare them for post-primary education.

Figure 2 shows the relationship between the school reform and measures of basic literacy and cognitive skills. Except for arithmetic skills, which show a very modest discontinuity around the cutoff date, there is no effect of the school reform on literacy skills. Regression estimates for the impact of expanding compulsory education on basic literacy skills are shown in panels (a)–(c) of table 5. As shown, expanding compulsory education has a positive impact on basic literacy skills, measured using reading skills and self-reported writing and math skills. For example, in model 1, the point estimate for reading skills is 0.009 with a standard error of 0.008, which indicates that adding an extra year to primary school may improve reading skills by up to 2.5 percentage points (i.e., the upper bound of the point estimate). However, across all specifications, the effects on basic literacy skills are statistically indistinguishable from zero. The only exception is the coefficient on writing skills in model 3, which suggests that expanding compulsory education increases the likelihood of being able to write a letter by 1.5 percentage points. This effect, however, is sensitive to model specification and only significant at the 0.1 level.

Figure 2.

Discontinuity in Learning Outcomes

Figure 2.

Discontinuity in Learning Outcomes

Table 5.
Regression Estimates for the Impact of Extending Compulsory Schooling on Learning Outcomes
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Sample Mean
(a) Read a sentence 0.009 0.005 0.014 82.8
(0.008) (0.008) (0.012)
[2,616] [2,629] [2,629]
(b) Write a letter 0.008 0.004 0.015* 82.0
(0.008) (0.008) (0.012)
[2,805] [2,837] [2,837]
(c) Do simple arithmetic 0.011 0.008 0.015 87.3
(0.007) (0.008) (0.012)
[2,499] [2,514] [2,514]
(d) High school test score 0.844 1.195 0.210 73.0
(1.013) (0.948) (1.425)
[2,003] [2,042] [2,042]
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Sample Mean
(a) Read a sentence 0.009 0.005 0.014 82.8
(0.008) (0.008) (0.012)
[2,616] [2,629] [2,629]
(b) Write a letter 0.008 0.004 0.015* 82.0
(0.008) (0.008) (0.012)
[2,805] [2,837] [2,837]
(c) Do simple arithmetic 0.011 0.008 0.015 87.3
(0.007) (0.008) (0.012)
[2,499] [2,514] [2,514]
(d) High school test score 0.844 1.195 0.210 73.0
(1.013) (0.948) (1.425)
[2,003] [2,042] [2,042]

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, gender, urban status, and wealth quintile. Sample sizes are in brackets.

*Significant at the 90% confidence level.

One might question whether expanding primary school from five to six years would have an impact on basic literacy skills, since there might be very little variation in these measures at the grade level affected by the reform (i.e., the fifth grade). To address this limitation, I use student performance in high school, measured using their test scores in the final examination of the general secondary education, to examine whether expanding compulsory education has improved student learning. It should be noted that, similar to some of the literacy skills measures, students’ test scores in the final examination of secondary education are also self-reported, which might result in measurement error. In particular, survey respondents may simply not be able to remember their high school test scores or may not report their true test scores even if they do remember. This is likely to affect students at the low end of the performance distribution, who may be hesitant to report their actual test scores. Measuring test scores with error, however, is not expected to bias the effects of the 1999 school reform for two reasons. First, given the high-stakes nature of the high school exam and the significant consequences it has on individuals’ future academic and career outcomes, it is unlikely that survey respondents will not be able to remember their test scores. The salient nature of the secondary education final examination is especially true for young workers or those who still enrolled in college, who represent the vast majority of the sample, since they are still experiencing the consequences of their performance in that exam. Second, and most importantly, there is little reason to believe that misreporting high school's test scores is correlated with the forcing variable—year-month of birth—and, as a result, the measurement error is not expected to be systematic around the 1992 school entry cutoff date. Therefore, assuming the error in the outcome variable (test scores) is independent of the treatment status, the estimated effects of the school reform will be unbiased (Wooldridge 2002).

Another issue related to measuring test scores is sample selection. Test scores are only available for students who took the secondary education final examination. Students who dropped out of school before taking the test are not included in the sample. If extending primary education from five to six years has caused students to stay longer in school and therefore increased the likelihood of taking the test, then the effect on the school reform will be biased. This bias might be downward if the marginal student affected by the school reform is less academically prepared than the average student. However, given that there is no evidence that the school reform affects post-primary attendance, the sample selection does not pose a serious threat to the validity of the results.

Figure 2 shows the relationship between the compulsory school reform and secondary education performance. As shown, the school reform does not seem to have an effect on student performance in secondary education. Table 5(d) presents the estimated treatment effects for the same outcome. Consistent with the graphical analysis, there is no evidence that adding an extra year to primary education has significantly improved student learning. As shown, the effect of the school reform is positive but not statistically significant.

### Labor Market Outcomes

In this section, I examine the effect of extending compulsory education on two labor market outcomes: labor force participation and employment status. Figures 3 and 4 plot the relationship between month-year of birth, the forcing variable, and each of the two outcomes. As shown, there are no discontinuous changes in the labor force participation or employment status of individuals born just before and just after the 1992 cutoff date. This indicates that labor market outcomes for individuals who were affected by the new six-year primary systems are very similar to the outcomes of individuals who were subject to the five-year system.

Figure 3.

Discontuinity in Labor Force Participation

Figure 3.

Discontuinity in Labor Force Participation

Figure 4.

Discontuinity in Employment Status

Figure 4.

Discontuinity in Employment Status

Regression estimates for these outcomes are reported in table 6. In general, expanding primary education from five to six years seems to have a large positive effect on employment status. For instance, the estimates from table 6 suggest that individuals who are affected by the new six-year primary systems are more likely to be employed than those who were subject to the five-year system, by somewhere between 2.3 (model 3) and 3.1 percentage points (model 2). However, these effects are not statistically significant at the conventional levels. Given that the vast majority of individuals in the sample are still in their early twenties, the estimated effects for labor market outcomes should be interpreted with caution. This is because young workers often experience higher rates of job turnover compared with older workers, and thus their current outcomes may not reflect their long-term labor market outcomes.

Table 6.
Estimated Effects of Extending Compulsory Schooling on Labor Market Outcomes
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Sample Mean
Labor force participation −0.024 −0.047 0.014 38.9
(0.039) (0.035) (0.052)
[2,175] [2,202] [2,202]
Employment status 0.028 0.031 0.023 31.4
(0.038) (0.035) (0.053)
[2,175] [2,148] [2,148]
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Sample Mean
Labor force participation −0.024 −0.047 0.014 38.9
(0.039) (0.035) (0.052)
[2,175] [2,202] [2,202]
Employment status 0.028 0.031 0.023 31.4
(0.038) (0.035) (0.053)
[2,175] [2,148] [2,148]

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, gender, urban status, and wealth quintile. Sample sizes are in brackets.

## 7.  Subgroup Analysis

One of the primary objectives of the 1999 Egyptian school reform was to improve educational attainment among disadvantaged students, such as female students and those who live in rural areas. In this section, I examine whether the effect of expanding compulsory education varies by gender and place of residence.

Table 7 provides the estimated effects of the school reform on educational and labor market outcomes for female (columns 1–3) and male (columns 4–6) individuals. As shown, expanding compulsory schooling has a large positive effect on total years of education among both male and female resepondents. This effect, however, is greater for male than female individuals. For example, estimates from the kernel RD regression suggest that expanding primary education from five to six years increases years of schooling by 0.55 years for female students (model 1) and 0.85 for male students (model 4). The results from the local polynomial regression show a larger gender gap in schooling. As shown, the 1999 school reform increases years of schooling by 0.54 for female students (model 3) and 1.02 for male students (model 6).

Table 7.
Effects of Extending Compulsory Education by Gender
FemalesMales
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Nonparametric Kernel (4)Local Linear (5)Local Quadratic (6)
Years of schooling 0.548*** 0.564*** 0.540** 0.846*** 0.724*** 1.022***
(0.157) (0.153) (0.223) −0.133 −0.146 −0.202
[1,068] [1,084] [1,084] [1,002] [1,018] [1,018]
Not attending school 0.000 0.000 0.000 −0.002 −0.003 −0.002
(0.000) (0.000) (0.000) (0.002) (0.003) (0.002)
[1,068] [1,289] [1,289] [1,029] [1,234] [1,234]
Completing primary 0.002 0.002 0.002 0.007 0.004 0.011
(0.002) (0.002) (0.002) (0.005) (0.005) (0.007)
[2,136] [2,152] [2,152] [1,918] [1,961] [1,961]
Post-primary attendance 0.002 0.012 −0.013 0.035* 0.031 0.038
(0.017) (0.018) (0.025) (0.021) (0.019) (0.025)
[2,136] [2,045] [2,045] [1,918] [2,219] [2,219]
Read a sentence 0.001 −0.006 0.008 0.018** 0.011 0.026**
(0.011) (0.012) (0.016) (0.009) (0.009) (0.013)
[1,304] [1,314] [1,314] [1,277] [1,287] [1,287]
Write a letter −0.001 −0.006 0.005 0.017** 0.012 0.028**
(0.011) (0.012 (0.016) (0.008) (0.007) (0.011)
[1,347] [1,359] [1,359] [1,340] [1,349] [1,349]
Do simple arithmetic 0.01 0.01 0.008 0.009 0.002 0.021*
(0.011) (0.011) (0.015) (0.007) (0.009) (0.012)
[1,401] [1,417] [1,417] [1,166] [1,177] [1,177]
Secondary education score 1.015 1.423 0.108 1.036 1.605 −0.088
(1.784) (1.549) (2.425) (1.309) (1.269) (1.839)
[934] [957] [957] [1,107] [1,118] [1,118]
Labor force participation −0.042 −0.044 −0.032 −0.011 −0.019 0.016
(0.049) (0.047) (0.068) (0.060) (0.057) (0.075)
[1,157] [1,172} [1,172] [1,082] [1,099] [1,099]
Employment status −0.016 −0.014 −0.030 0.059 0.079 0.049
(0.031) (0.029) (0.042) (0.058) (0.056) (0.072)
1,370 1,334 1,334 1,029 1,082 1,082
FemalesMales
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Nonparametric Kernel (4)Local Linear (5)Local Quadratic (6)
Years of schooling 0.548*** 0.564*** 0.540** 0.846*** 0.724*** 1.022***
(0.157) (0.153) (0.223) −0.133 −0.146 −0.202
[1,068] [1,084] [1,084] [1,002] [1,018] [1,018]
Not attending school 0.000 0.000 0.000 −0.002 −0.003 −0.002
(0.000) (0.000) (0.000) (0.002) (0.003) (0.002)
[1,068] [1,289] [1,289] [1,029] [1,234] [1,234]
Completing primary 0.002 0.002 0.002 0.007 0.004 0.011
(0.002) (0.002) (0.002) (0.005) (0.005) (0.007)
[2,136] [2,152] [2,152] [1,918] [1,961] [1,961]
Post-primary attendance 0.002 0.012 −0.013 0.035* 0.031 0.038
(0.017) (0.018) (0.025) (0.021) (0.019) (0.025)
[2,136] [2,045] [2,045] [1,918] [2,219] [2,219]
Read a sentence 0.001 −0.006 0.008 0.018** 0.011 0.026**
(0.011) (0.012) (0.016) (0.009) (0.009) (0.013)
[1,304] [1,314] [1,314] [1,277] [1,287] [1,287]
Write a letter −0.001 −0.006 0.005 0.017** 0.012 0.028**
(0.011) (0.012 (0.016) (0.008) (0.007) (0.011)
[1,347] [1,359] [1,359] [1,340] [1,349] [1,349]
Do simple arithmetic 0.01 0.01 0.008 0.009 0.002 0.021*
(0.011) (0.011) (0.015) (0.007) (0.009) (0.012)
[1,401] [1,417] [1,417] [1,166] [1,177] [1,177]
Secondary education score 1.015 1.423 0.108 1.036 1.605 −0.088
(1.784) (1.549) (2.425) (1.309) (1.269) (1.839)
[934] [957] [957] [1,107] [1,118] [1,118]
Labor force participation −0.042 −0.044 −0.032 −0.011 −0.019 0.016
(0.049) (0.047) (0.068) (0.060) (0.057) (0.075)
[1,157] [1,172} [1,172] [1,082] [1,099] [1,099]
Employment status −0.016 −0.014 −0.030 0.059 0.079 0.049
(0.031) (0.029) (0.042) (0.058) (0.056) (0.072)
1,370 1,334 1,334 1,029 1,082 1,082

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, urban status, and wealth quintile. Sample sizes are in brackets.

***Significant at the 99% confidence level; **significant at the 95% confidence level; *significant at the 90% confidence level.

Unlike years of schooling, results from table 6 show no significant effects of the 1999 school reform on females’ educational paths, literacy skills, high school performance, or labor market outcomes. For instance, across all specifications, the school reform seems to increase the likelihood of not attending school, completing primary education, and attending post-primary education among female individuals. None of these effects, however, can be distinguished from zero.

In contrast, estimates from table 7 indicate that expanding compulsory education has improved the reading and self-reported writing skills among male individuals. For example, the coefficients from the kernel regression (model 4) show the school reform has increased the probability of reading a sentence and writing a letter by 1.8 and 1.7 percentage points, respectively. Both effects are significant at the 0.05 level. There is also tentative evidence that the school reform has a positive effect on males’ post-primary attendance, math skills, and employment status. However, the estimated effects for these outcomes are sensitive to model specification and only significant at the 0.1 level. Overall, the results from table 7 suggest that, except for total years of education, the school reform has no impact on educational paths, literacy skills, or labor market outcomes among female individuals. There is some evidence, however, that the 1999 school reform has improved basic reading and writing skills for male students. One potential explanation for the large effects of the 1999 school reform among males is that a larger share of males attend school than females. In fact, only 5.9 percent of male respondents in the sample have no formal education, compared with 14.6 percent of female respondents. As a result, the effect of the school reform is expected to be large among males, which is consistent with the results.

Table 8 presents the estimated effects of expanding compulsory schooling by place of residence. Columns 1–3 show the results for urban areas and columns 4–6 provide the results for rural areas. Overall, the school reform has a large positive impact on total years of schooling in both urban and rural areas. The effect is slightly larger in rural areas. There is no evidence, however, that that expanding primary schooling has affected individuals’ post-primary attendance, literacy skills, or labor market outcomes across both urban and rural areas. For example, estimates from the nonparametric kernel regression indicate that the school reform increases total years of education by 0.61 in urban areas (model 1) compared with 0.75 years in rural areas (model 4). The results from table 8 also show some positive effects of the school reform on reading skills (models 1 and 3), primary school completion (model 3), and writing skills (model 3) among individuals living in urban areas. These effects, however, are not robust across specifications and only significant at the 0.1 level.

Table 8.
Effects of Extending Compulsory Education by Place of Residence
UrbanRural
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Nonparametric Kernel (4)Local Linear (5)Local Quadratic (6)
Years of schooling 0.609*** 0.536*** 0.695*** 0.746*** 0.721*** 0.775***
(0.154) (0.169) (0.204) (0.170) (0.162) (0.241)
[913] [926] [926] [1,176] [1,186] [1,186]
Not attending school −0.003 −0.004 −0.004 0.000 0.000 0.000
(0.003) (0.003) (0.004) (0.000) (0.000) (0.000)
[913] [1,343] [1,343] [1,176] [1,348] [1,348]
Completing primary 0.005 0.004 0.007* 0.004 0.002 0.007
(0.004) (0.004) (0.004) (0.004) (0.003) (0.006)
[2,273] [2,298] [2,298] [2,156] [2,201] [2,201]
Post-primary attendance −0.002 −0.007 0.007 0.034 0.032* 0.036
(0.021) (0.020) (0.028) (0.022) (0.018) (0.027)
[2,273] [2,244] [2,244] [2,156] [2,742] [2,742]
Read a sentence 0.020* 0.017 0.024* 0.004 0.005 0.002
(0.011) (0.012) (0.014) (0.010) (0.009) (0.014)
[1,058] [1,076] [1,076] [1,201] [1,212] [1,212]
Write a letter 0.011 0.001 0.029* 0.011 0.007 0.017
(0.010) (0.013) (0.015) (0.009) (0.009) (0.013)
[1,097] [1,107] [1,107] [1,281] [1,293] [1,293]
Do simple arithmetic 0.010 0.007 0.016 0.004 0.006 −0.001
(0.011) (0.011) (0.013) (0.008) (0.009) (0.012)
[1,272] [1,287] [1,287] [1,242] [1,259] [1,259]
Secondary education score 1.970 2.198 1.288 −0.213 0.295 −1.276
(1.717) (1.574) (2.169) (2.009) (1.789) (2.800)
[989] [1,001] [1,001] [978] [1,004] [1,004]
Labor force participation −0.008 −0.039 0.055 −0.042 −0.057 −0.018
(0.073) (0.063) (0.100) (0.049) (0.048) (0.065)
[1,010] [1,017] [1,017] [1,293] [1,303] [1,303]
Employment status 0.033 0.039 0.007 0.049 0.048 0.055
(0.061) (0.054) (0.087) (0.036) (0.037) (0.050)
[1,115] [1,058] [1,058] [1,123] [1,176] [1,176]
UrbanRural
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)Nonparametric Kernel (4)Local Linear (5)Local Quadratic (6)
Years of schooling 0.609*** 0.536*** 0.695*** 0.746*** 0.721*** 0.775***
(0.154) (0.169) (0.204) (0.170) (0.162) (0.241)
[913] [926] [926] [1,176] [1,186] [1,186]
Not attending school −0.003 −0.004 −0.004 0.000 0.000 0.000
(0.003) (0.003) (0.004) (0.000) (0.000) (0.000)
[913] [1,343] [1,343] [1,176] [1,348] [1,348]
Completing primary 0.005 0.004 0.007* 0.004 0.002 0.007
(0.004) (0.004) (0.004) (0.004) (0.003) (0.006)
[2,273] [2,298] [2,298] [2,156] [2,201] [2,201]
Post-primary attendance −0.002 −0.007 0.007 0.034 0.032* 0.036
(0.021) (0.020) (0.028) (0.022) (0.018) (0.027)
[2,273] [2,244] [2,244] [2,156] [2,742] [2,742]
Read a sentence 0.020* 0.017 0.024* 0.004 0.005 0.002
(0.011) (0.012) (0.014) (0.010) (0.009) (0.014)
[1,058] [1,076] [1,076] [1,201] [1,212] [1,212]
Write a letter 0.011 0.001 0.029* 0.011 0.007 0.017
(0.010) (0.013) (0.015) (0.009) (0.009) (0.013)
[1,097] [1,107] [1,107] [1,281] [1,293] [1,293]
Do simple arithmetic 0.010 0.007 0.016 0.004 0.006 −0.001
(0.011) (0.011) (0.013) (0.008) (0.009) (0.012)
[1,272] [1,287] [1,287] [1,242] [1,259] [1,259]
Secondary education score 1.970 2.198 1.288 −0.213 0.295 −1.276
(1.717) (1.574) (2.169) (2.009) (1.789) (2.800)
[989] [1,001] [1,001] [978] [1,004] [1,004]
Labor force participation −0.008 −0.039 0.055 −0.042 −0.057 −0.018
(0.073) (0.063) (0.100) (0.049) (0.048) (0.065)
[1,010] [1,017] [1,017] [1,293] [1,303] [1,303]
Employment status 0.033 0.039 0.007 0.049 0.048 0.055
(0.061) (0.054) (0.087) (0.036) (0.037) (0.050)
[1,115] [1,058] [1,058] [1,123] [1,176] [1,176]

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, gender, and wealth quintile. Sample sizes are in brackets.

***Significant at the 99% confidence level; *significant at the 90% confidence level.

## 8.  Robustness Checks

### Covariate Balance Around the Cutoff Date

The validity of the results from the RD design rests on a strong ignorability assumption, which assumes that individuals around the cutoff date (i.e., those who are born just before and just after 1 October 1992) are as if randomly assigned. Although there is no direct way of testing this assumption, it has several implications that could be examined. One implication is that there should be no systematic differences between individuals born just around the cutoff date. To test the validity of this implication, I examine the pretreatment covariate balance between the treatment and the comparison groups, focusing on four key variables: gender (coded as 1 for females and zero otherwise), place of birth (coded as 1 for individuals born in urban areas and zero otherwise), and parental education (coded as 1 for individuals whose mothers/fathers have no education and zero otherwise). If the strong ignorability assumption holds, then there should be no differences between the two groups across these four variables. In fact, as shown in table 9, there is no evidence of significance differences, at the 0.05 level, between the treatment and the comparison groups across gender, place of birth, or parental education.

Table 9.
Regression Estimates for Covariate Balance Around the Cutoff Date
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)
% Female 0.026 0.076* 0.076*
(0.048) (0.044) (0.044)
[2,269] [2,291] [2,291]
% Father with no education 0.011 0.011 0.011
(0.040) (0.037) (0.037)
[1,184] [1,205] [1,205]
% Mother with no education 0.092 0.079 0.079
(0.098) (0.086) (0.086)
[537] [552] [552]
% Born in urban area −0.003 0.000 0.000
(0.020) (0.018) (0.018)
[771] [799] [799]
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)
% Female 0.026 0.076* 0.076*
(0.048) (0.044) (0.044)
[2,269] [2,291] [2,291]
% Father with no education 0.011 0.011 0.011
(0.040) (0.037) (0.037)
[1,184] [1,205] [1,205]
% Mother with no education 0.092 0.079 0.079
(0.098) (0.086) (0.086)
[537] [552] [552]
% Born in urban area −0.003 0.000 0.000
(0.020) (0.018) (0.018)
[771] [799] [799]

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age and wealth quintile. Sample sizes are in brackets.

*Significant at the 90% confidence level.

### Density of the Forcing Variable

Another implication of the strong ignorability assumption is that individuals should not be able to manipulate the assignment variable, that is, those around the cutoff date have no full control on whether they receive the treatment. One way to test this assumption is to examine the density of the assignment variable around the cutoff date. A discontinuity in the density around the cutoff date would indicate that individuals may be manipulating the threshold (McCrary 2008). As shown in figure 5, there is no evidence of such discontinuity. In addition, a formal test of discontinuity in density around the cutoff date failed to reject the null hypothesis.

Figure 5.

Density of the Assignment Variable Around the Cutoff Date

Figure 5.

Density of the Assignment Variable Around the Cutoff Date

### Treatment Misspecification

In addition to strong ignorability, the RD design assumes the treatment variable is measured without error. One important implication of this assumption, as discussed in the methodology section, is that primary schools only accept children who turn six before 1 October. Although this assumption may hold for the vast majority of children in primary schools, some schools may accept children who are a few months shy of the legal school entry age in response to pressures from parents. To test the sensitivity of the results to this source of measurement error, I exclude individuals who were born within three months around the cutoff date. Estimates from this specification are reported in table 10. Overall, the results are similar to the main analysis—except for total years of education, the 1999 school reform has no impact on the likelihood of not attending school or completing primary education. There is also no evidence that the reform has improved individuals’ literacy skills, labor force participation, or employment status. Unlike the results from the main analysis, estimates from table 10 show some positive effects of the reform on post-primary attendance. These effects, however, are only significant at the 0.1 level.

Table 10.
Effects of Extending Compulsory Education on Schooling and Labor Market Outcomes
Nonparametric Kernel (1)Local linear (2)Local Quadratic (3)
Years of schooling 0.568*** 0.533*** 0.629**
(0.144) (0.156) (0.249)
[1,735] [1,774] [1,774]
Not attending school −0.001 −0.002 −0.002
(0.002) (0.002) (0.002)
[1,735] [2,428] [2,428]
Completing primary 0.005 0.004 0.008
(0.004) (0.003) (0.006)
[4,163] [4,220] [4,220]
Post-primary attendance 0.034** 0.023* 0.034*
(0.017) (0.013) (0.020)
[4,163] [5,865] [5,865]
Read a sentence 0.008 0.003 0.012
(0.009) (0.009) (0.015)
[2,415] [2,428] [2,428]
Write a letter 0.002 −0.001 0.008
(0.008) (0.008) (0.012)
[2,604] [2,636] [2,636]
Do simple arithmetic 0.015 0.009 0.025
(0.010) (0.010) (0.016)
[2,298] [2,313] [2,313]
Secondary education score 1.422 1.659 0.592
(1.548) (1.363) (2.537)
[1,802] [1,841] [1,841]
Labor force participation 0.004 −0.035 0.097
(0.051) (0.046) (0.081)
[1,974] [2,001] [2,001]
Employment status 0.086* 0.071* 0.129
(0.047) (0.042) (0.082)
[1,974] [1,947] [1,947]
Nonparametric Kernel (1)Local linear (2)Local Quadratic (3)
Years of schooling 0.568*** 0.533*** 0.629**
(0.144) (0.156) (0.249)
[1,735] [1,774] [1,774]
Not attending school −0.001 −0.002 −0.002
(0.002) (0.002) (0.002)
[1,735] [2,428] [2,428]
Completing primary 0.005 0.004 0.008
(0.004) (0.003) (0.006)
[4,163] [4,220] [4,220]
Post-primary attendance 0.034** 0.023* 0.034*
(0.017) (0.013) (0.020)
[4,163] [5,865] [5,865]
Read a sentence 0.008 0.003 0.012
(0.009) (0.009) (0.015)
[2,415] [2,428] [2,428]
Write a letter 0.002 −0.001 0.008
(0.008) (0.008) (0.012)
[2,604] [2,636] [2,636]
Do simple arithmetic 0.015 0.009 0.025
(0.010) (0.010) (0.016)
[2,298] [2,313] [2,313]
Secondary education score 1.422 1.659 0.592
(1.548) (1.363) (2.537)
[1,802] [1,841] [1,841]
Labor force participation 0.004 −0.035 0.097
(0.051) (0.046) (0.081)
[1,974] [2,001] [2,001]
Employment status 0.086* 0.071* 0.129
(0.047) (0.042) (0.082)
[1,974] [1,947] [1,947]

Note: Individuals who were born within three months of the cutoff date are excluded from the sample. Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, gender, urban status, and wealth quintile. Sample sizes are in brackets.

***Significant at the 99% confidence level; **significant at the 95% confidence level; *significant at the 90% confidence level.

### Sensitivity to Bandwidths

The main results in section 6 indicate that expanding primary education from five to six years has a large impact on years of schooling. There is no evidence, however, that this expansion affects individuals’ learning or labor market outcomes. In this section, I examine the extent to which these results are sensitive to the number of bandwidths used in the analysis. In particular, I reestimate the effect of the 1999 school reform on individuals’ schooling and labor market outcomes using a wide range of bandwidths. The estimates from these models are shown in figures 69, with 95 percent confidence intervals. Figures 6 and 7 provide the estimated effects of the 1999 school reform on schooling and learning outcomes; figures 8 and 9 present the effects of the reform on labor market outcomes. Overall, these graphs show that, except for years of schooling, expanding primary education has no effect on individuals’ learning or labor market outcomes. For example, increasing the bandwidth slightly changes the magnitude of the estimated effects for literacy skills and labor market outcomes, although none of the effects can be distinguished from zero.

Figure 6.

95% Confidence Interval for Estimated Effects on Schooling Outcomes

Figure 6.

95% Confidence Interval for Estimated Effects on Schooling Outcomes

Figure 7.

95% Confidence Interval for Estimated Effects on Learning Outcomes

Figure 7.

95% Confidence Interval for Estimated Effects on Learning Outcomes

Figure 8.

95% Confidence Interval for Estimated Effects on Labor Force Participation

Figure 8.

95% Confidence Interval for Estimated Effects on Labor Force Participation

Figure 9.

95% Confidence Interval for Estimated Effects on Employment Status

Figure 9.

95% Confidence Interval for Estimated Effects on Employment Status

## 9.  Nonpecuniary Outcomes

Research on returns to schooling suggests that education not only increases lifetime earnings, it also improves well-being, leads individuals to make better decisions about health and marriage, and decreases the likelihood of engaging in risky behavior (Dee 2004; Oreopoulos and Salvanes 2011). In this section, I estimate the effect of the Egyptian compulsory school reform on four nonpecuniary outcomes: smoking, self-reported health, happiness, and trust. Smoking is measured using a binary variable that is coded as 1 for individuals who ever smoked and zero otherwise. To measure health status, I create a binary variable that takes 1 for individuals who reported being in Excellent'' or Very good'' health and zero otherwise. Similarly, happiness and trust are measured using two binary variables that take 1 for individuals who reported being happy and those who agree that “people can be trusted,” respectively. The effects of the compulsory school expansion are shown in table 11. Overall, there is no evidence that expanding compulsory education improves any of the four nonpecuniary outcomes.

Table 11.
Effects of Extending Compulsory Education on Nonpecuniary Outcomes
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)
Very good health −0.018 −0.003 −0.042
(0.033) (0.030) (0.045)
[4,820] [4,872] [4,872]
Ever smoked −0.006 0.005 −0.023
(0.023) (0.021) (0.033)
[3,517] [3,579] [3,579]
Feel happy −0.021 −0.025 −0.028
(0.018) (0.017) (0.025)
[5,402] [4,877] [5,439]
Believe people can be trusted −0.026 −0.041* −0.004
(0.023) (0.023) (0.030)
[4,698] [4,763] [4,763]
Nonparametric Kernel (1)Local Linear (2)Local Quadratic (3)
Very good health −0.018 −0.003 −0.042
(0.033) (0.030) (0.045)
[4,820] [4,872] [4,872]
Ever smoked −0.006 0.005 −0.023
(0.023) (0.021) (0.033)
[3,517] [3,579] [3,579]
Feel happy −0.021 −0.025 −0.028
(0.018) (0.017) (0.025)
[5,402] [4,877] [5,439]
Believe people can be trusted −0.026 −0.041* −0.004
(0.023) (0.023) (0.030)
[4,698] [4,763] [4,763]

Note: Standard errors are clustered at the year-month of birth level and reported in parentheses. In all regressions, I control for age, gender, urban status, and wealth quintile. Sample sizes are in brackets.

*Significant at the 90% confidence level.

## 10.  Conclusion

Using a natural experiment from Egypt, this paper examines the long-term effects of extending compulsory education. Beginning in school year 2004–05, the Egyptian government extended primary education from five to six years, moving from an eight-year compulsory education system to a nine-year system. Using a sharp regression discontinuity design, I examine whether extending compulsory education affects years of schooling, literacy skills, post-primary attendance, and labor market outcomes. The results suggest that extending compulsory education has large positive effects on years of schooling. An extra year of compulsory education increases years of schooling by 0.6 to 0.8 years. This effect, however, is concentrated among male individuals. In particular, the findings from this paper show that expanding compulsory education increases the schooling gap between male and female individuals by somewhere between 0.30 and 0.48 years of schooling. These findings also show no effects of expanding compulsory schooling on individuals’ literacy skills, schooling beyond the primary education level, or labor market outcomes. There is some evidence, however, that the 1999 school reform has improved reading and self-reported writing skills among males.

These results rest on the identification assumption that individuals born just around the cutoff date are as if randomly assigned. Several pieces of evidence support this assumption. First, I find that predetermined characteristics are not correlated with the treatment status. That is, individuals who were affected by the compulsory school reform have, on average, observable characteristics that are similar to those who were not affected by the reform. Second, the estimated effects are robust across multiple specifications and sample restrictions. For example, when I exclude individuals who are most likely to be affected by treatment misspecification (those who were born within three months of the official entrance age), the estimated treatment effects are the same.

The findings of this paper have major policy implications. Although the results show a positive impact of expanding compulsory education on total years of schooling, it also suggests that, if not accompanied with improving school quality or increasing school resources, the mere expansion of compulsory education is likely to have little effect on individuals’ literacy skills and long-term labor market outcomes. Similar to many other developing countries, Egyptian schools face numerous challenges in areas such as infrastructure, teacher quality, and school governance. Failing to address these challenges will likely impede any gains resulting from expanding compulsory education. Furthermore, the evidence from this paper indicates that expanding compulsory schooling may exacerbate the schooling gap between males and females in developing countries. Particularly, because compulsory education is not strictly enforced in many of these countries, increasing years of primary schooling may discourage some parents (especially those who put low value on female education) from sending young girls to school. As a result, the adverse effects on female education should be taken into account when designing policies that expand compulsory education. For example, these policies should include elements that improve the enforcement of compulsory schooling and/or provide parents with more incentives to send their children to school.

## Acknowledgments

I thank Rania Roushdy and Ali Rashed from the Population Council for providing access to the SYPE dataset. I also thank Fatma Romeh M. Ali, Basit Zafar, Tim Sass, two anonymous reviewers, and seminar participants at the 2016 Annual Meeting of the Association for Education Finance and Policy for their insightful comments.

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## Notes

1.

For example, in 1968, Taiwan expanded compulsory schooling from six to nine years by including three years of junior high school as part of compulsory education.

2.

Prior to school year 1988–89, basic education included nine years: six years for primary school plus three years for preparatory school. In 1988, the government passed a law that reduced the length of primary school from six to five years. The six-year primary system was reinstated in 1999 by Law No. 23 for 1999. (For more information about the 1988 reform, see Ali and Elsayed 2018.)

3.

To address the fact that some cohorts of students in the control group may not have been affected by changes in school infrastructure or decline in enrollment resulted from the 1999 school reform (such as those who finished primary education before 1999), I examine the effect of the reform among students who were affected by these changes but attended different primary school systems. For example, in the robustness check section, I examine the effect of the reform within ten to twenty-four months around the cutoff date. The results are very similar to the main analysis.

4.

The final score of each student in the secondary education final examination reflects the sum of the student's exam scores in the second and third years, converted to a 100-point scale.

5.

Appendix table A.1 provides optimal bandwidth for schooling, learning, and labor market outcomes resulting from each of the three methods.

## Appendix

Table A.1.
Optimal Bandwidth for Schooling, Learning, and Labor Market Outcomes
Plug-inCross ValidationRobust RD
Total years of schooling 37 58 33
Not Attending school 64 NA 34
Completing primary education 64 96 34
Post-primary attendance 105 96 22
Read a sentence 64 96 25
Write a letter 73 96 39
Do simple arithmetic 58 86 29
Secondary school score 39 70 15
Labor force participation 45 62 37
Employment status 45 62 38
Plug-inCross ValidationRobust RD
Total years of schooling 37 58 33
Not Attending school 64 NA 34
Completing primary education 64 96 34
Post-primary attendance 105 96 22
Read a sentence 64 96 25
Write a letter 73 96 39
Do simple arithmetic 58 86 29
Secondary school score 39 70 15
Labor force participation 45 62 37
Employment status 45 62 38