LowWageReturnstoSchoolinginaDeveloping Country ...faculty.smu.edu/millimet/classes/eco7377/papers/aydemir kirdar 201… · school level (grades 6–8) was 52.8%.2 Thus, the 1997 reform

1046© 2017 The Department of Economics, University of Oxford and John Wiley & Sons Ltd.

doi: 10.1111/obes.12174

Low Wage Returns to Schooling in a DevelopingCountry: Evidence from a Major Policy Reform inTurkey*

Abdurrahman Aydemir† and Murat G. Kirdar‡

†Faculty of Arts and Social Sciences, Sabanci University, Orhanli, Tuzla 34956, Istanbul,Turkey (e-mail: [email protected])‡Department of Economics, Bogazici University, Istanbul, 34342, Turkey(e-mail: [email protected])

Abstract

In this paper, we estimate returns to schooling for young men and women in Turkey usingthe exogenous and substantial variation in schooling across birth cohorts brought about bythe 1997 reform of compulsory schooling within a fuzzy regression discontinuity design.We estimate that the return from an extra year of schooling is about 7–8% for women andan imprecisely estimated 2–2.5% for men. The low level of the estimates for men contrastsstarkly with those estimated for other developing countries. We identify several reasonswhy returns to schooling are low for men and why they are higher for women in our context.In particular, the policy alters the schooling distributions of men and women differently,thus the average causal effect puts a higher weight on the causal effect of schooling athigher grade levels for women than for men.

I. Introduction

Few studies deal with the endogeneity of education in the estimation of returns to schoolingin developing country contexts. These include Duflo (2001), who uses a major schoolconstruction policy as a source of exogenous change in schooling in Indonesia; Spohr(2003), who explores the impact of Taiwan’s 1968 reform and Fang et al. (2012), who studythe 1986 implementation of compulsory education law in China. This paper contributes tothis small literature by estimating the returns to schooling for both men and women in thedeveloping country context of Turkey – using an IV regression discontinuity design thatrelies on the extension of compulsory schooling from 5 to 8 years in 1997.

JEL Classification numbers: J18, J31, I21, I28.*We would like to thank Jonah Gelbach, James MacKinnon, and the seminar participants at Bilkent and Koc

Universities and at the 2015 SOLE/EALE conference for valuable comments and suggestions. The usual disclaimerholds.

OXFORD BULLETIN OF ECONOMICS AND STATISTICS, 79, 6 (2017) 0305–9049

Low wage returns to schooling in a developing country 1047

In 1997, Turkey instituted a major reform of its education system, which increasedthe duration of compulsory schooling from 5 to 8 years.1 According to national educationstatistics, during the 1996–97 school year, the year before the law changed, the net enrol-ment was 89.4% at the primary school level (grades 1–5), while enrolment at the secondaryschool level (grades 6–8) was 52.8%.2 Thus, the 1997 reform potentially affected close tohalf of school-age children at the secondary school level. By the 2000–01 school year, 4years after the law was enacted, the net enrolment rate at the compulsory schooling stage(grades 1–8) increased to 95.3%. Such a drastic rise in the number of students could raiseconcerns about the quality of schooling. However, the government reacted very fast toexpand the schooling infrastructure. By early 2000, two years after the school reform, thestudent-to-teacher ratio and student-to-class ratio were below their pre-reform levels (Kir-dar, Dayioglu-Tayfur and Koc, 2015). In fact, based on the results of certain internationaltests, we show that achievement of the affected cohorts vis-a-vis the unaffected indicatesno deterioration in the quality of schooling (MEB, 2007).3

Although several studies have estimated the causal returns to schooling, mostly indeveloped-country settings, this paper adds to the small number of studies employing re-gression discontinuity design – which imposes weaker identifying assumptions than thedifference-in-differences methodology used in many of the previous studies.4 Our identi-fication method in estimating returns to schooling thus rests on the comparison of birthcohorts which are affected by the policy with those which are not. Imperfect compliancewith the policy in our context leads to a fuzzy regression discontinuity design, where weinstrument schooling with a policy dummy defined by birth cohort. In our context, a criticalissue is disentangling the policy effect from the strong time trends in the outcome variables.For this purpose, we allow for very flexible time trends, going up to fourth-order poly-nomials. In certain specifications, we allow the time trends to be different before and afterthe discontinuity. Moreover, using various subsamples defined by gradually taking narrowertime intervals around the discontinuity and adjusting for the degree of the polynomialssimultaneously, we check the robustness of our results in a similar vein to a non-parametricapproach.

A key distinguishing feature of this study is the plausible exogeneity of our instrument.The actual timing of the policy was driven by political developments and was independent ofpotential returns to education and macroeconomic conditions. While there was a substantialfinancial investment on schooling infrastructure to meet the needs of increased studentpopulation due to the extension of compulsory school, its timing did not coincide with aneconomic boom – which could imply the implementation of other simultaneous policiesaffecting schooling outcomes. Moreover, the implementation of the reform was unexpectedand took place over a short period of time. Another important feature of our study is thestrength of our instrument, resulting from the remarkable change in schooling outcomes

1Basic Education Law (no. 4306, dated 16 August 1997).

2TUIK (Turkish Statistical Institute), Education Statistics.

3We provide detailed evidence on this in section III.

4Stephens and Yang (2014) show that once the common-trend assumption of the difference-in-differences studies

is relaxed, the returns to schooling estimate in the US context becomes either very small or wrong-signed andstatistically insignificant.

© 2017 The Department of Economics, University of Oxford and John Wiley & Sons Ltd

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with the reform.5 The policy led to a sharp increase in schooling levels across birth cohortsfor two main reasons. First, the duration of the extension was long (3 years). Second, sincethe dropout rates after the completion of compulsory schooling were high in Turkey prior tothe reform, the reform changed the behaviour of many students. In addition, since Turkey’scompulsory schooling reform affected a large fraction of the population, the local averagetreatment effect we estimate comes close to the average treatment effect as in Oreopoulos(2006).

The data we use in this study come from the 2002–13 Household Labor Force Surveys(HLFS) of Turkey. Since our identification strategy is based on a comparison of birthcohorts – albeit one where the discontinuity across birth cohorts is very substantial andwhere there are no other contaminating policies – our key variable of interest, the policyvariable, is invariant across birth cohorts. Moreover, the number of birth cohorts in somesamples is as small as 18. Therefore, we use several alternative approaches (outlined inCameron and Miller, 2015) to estimate accurate standard errors when there are few clusters.In addition to the standard cluster-robust estimates, these approaches include inferencebased on aT distribution with adjusted degrees-of-freedom, parametric Moulton correctionof standard errors, and wild cluster bootstrap.

We find that the instrumental-variable regression-discontinuity (IV-RD) estimate is astatistically insignificant 2–2.5% for men and about 7–8% for women.These estimates, par-ticularly those for men, are much smaller than the estimates reported by the previous studiesin developing country settings. Duflo (2001) reports return estimates for men ranging from6.8% to 10.6%. Spohr (2003) finds larger effects on females’ workforce participation andtotal earnings, where annual earnings increase by 5.8% per additional year of schoolingfor men and by 16.7% for women. Fang et al. (2012) report overall returns to educationof approximately 20% per year. However, the low returns we find in this study add to agrowing number of recent studies that report zero or low returns to schooling in developedcountry contexts (Pischke and von Wachter, 2008; Devereux and Hart, 2010; Stephensand Yang, 2014) but in a developing country context. Hence, this paper contributes to therenewed discussion in the literature on returns to education.

While the previous studies in developing country contexts find higher returns for womenthan for men, there is little discussion of these differential returns. We provide a detailedaccount of how the reform affects the distribution of highest grade completed by gender (asin Acemoglu and Angrist, 2000), which provides important insights related to this apparentdifference in returns. In particular, the female sample for whom we estimate the returnsto schooling include a larger fraction of those who are induced to complete high schoolas a result of the policy, compared to the male sample. Thus, the average causal effect forwomen puts a higher weight on the returns to schooling at high school grade levels thanthat for men, and returns to schooling are higher at high school grade levels than at lowergrade levels.

Since our fuzzy regression discontinuity design estimates have LATE interpretation (asshown by Hahn, Todd and van der Klaauw, 2001), our estimates are only for compliers

5The importance of a strong source of exogenous variation is discussed by Bound, Jaeger and Baker (1995), who

show that asymptotic bias resulting from weak instruments pushes the 2SLS estimates toward the OLS estimate. Thisissue is further addressed by Staiger and Stock (1997).



(who take the treatment when they satisfy the cutoff rule, but who would not take itotherwise). The individuals who are induced to change their behaviour at the cutoff areobserved between the ages of 18 and 26 in our wage sample. While this is a relatively younggroup, we check the sensitivity of our returns-to-schooling estimates by imposing higherminimum-age restrictions on our sample. In particular, we provide returns to schoolingestimates also when the sample is restricted to individuals who are older than 20, 22 and24, respectively, and show that our estimates are quite stable across these groups.

In the next section, we provide background on several methodological challenges forestimating returns to schooling and discuss how the reform used in this study overcomesthese estimation challenges. This is followed by a brief description of Turkey’s compulsoryschooling reform in section III. Section IV discusses the data used in the analysis. Themethodology is discussed in section V. Section VI presents the findings and section VIIconducts robustness checks on these findings. Section VIII provides an interpretation ofthese findings. Section IX concludes.

II. Related literature

Many studies use institutional features of education systems as a source of exogenousvariation in schooling so that returns to schooling in terms of earnings can be estimatedconsistently.6 In the UK and Ireland context, Harmon and Walker (1995) and Oreopoulos(2006) use identification strategies that rely on a comparison of the birth cohorts affectedby changes in compulsory schooling laws with those not affected. Similarly, in this paper,we compare the birth cohorts that are affected by the 1997 education reform in Turkey withthose that are unaffected.7

Imbens and Angrist (1994) show that the 2SLS estimates give the effect for the set ofcompliers – those who change their schooling choice due to the instrument. However, theset of compliers may not be representative of the whole population. The estimates derivedfrom the changes in compulsory school leaving age provide local treatment effects (LATE)for compliers. Oreopoulos (2006) notes that as the fraction of the population affected bythe policy change increases, the LATE estimate approaches the average treatment effect(ATE) because the marginal individual affected by the policy change becomes increasinglysimilar to the average individual in the population. Using a much larger set of compliers,Oreopoulos (2006) finds that the 2SLS estimates in the UK context are not substantiallydifferent from those found by Angrist and Krueger (1991). Devereux and Hart (2010),however, find much lower returns in the same context. Similarly, Pischke and von Wachter(2008) report zero returns in the German context, where a large fraction of the populationis affected by a change in compulsory schooling. Thus, there is mixed evidence fromthese studies in developed country contexts about the IV estimates of returns to education.Our estimates in a developing country context contribute to the ongoing discussion in the

6Several studies in the literature also employ alternative instruments based on the distance to the nearest college

(Kane and Rouse, 1995; Card, 1995; Connely and Uusitalo, 1997; Maluccio, 1997), family background variables(Card, 1995) and new school construction at various locations (Duflo, 2001).

7Several studies provide non-causal estimates of returns to education in the Turkish context. Tansel (1994) focuses

on Turkey while Salehi-Isfahani, Tunali and Assaad (2009) and Tansel and Daoud (2014) provide cross-countrycomparisons involving Turkey.


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literature about the relative size of returns to education. Similar to these studies, Turkey’scompulsory schooling reform affects a large fraction of the population, which brings thelocal average treatment effect estimate closer to the average treatment effect.8

In both the British and German contexts discussed above, the changes in compulsoryeducation laws involve 1-year increases, increasing the schooling leaving age from 14 to15 in the former case and adding a compulsory ninth grade for students in the latter case.When there are nonlinearities in the returns to schooling, returns to schooling estimateswould depend on the specific age and grade at which the policy-induced change takes place.For example, while Pischke and von Wachter find zero or low returns to an additional yearof schooling resulting from the compulsory school extension from eighth to ninth grade,other IV estimates from Germany (Ichino and Winter-Ebmer, 1999, 2004; Becker andSiebern-Thomas, 2001) are much larger, around 10%. Pischke and von Wachter argue thatthis difference in results may be due to the instruments that consider education differencesat different points – for example, differences in grades 10 and above in the Becker andSiebern–Thomas study. They argue that the additional year of schooling explored in theirstudy, which they estimate to have a zero return in terms of earnings, may not be equippingstudents with any labour market-relevant skills. A unique feature of our context is that notonly does the policy affect a large fraction of school-age children; it also induces higherschooling at different school levels. Individuals who would leave school by the end of grade5, 6, or 7 in the absence of the policy are now required to complete 8 years of schooling.Moreover, there are spillover effects beyond grade 8; some students continue schooling upto grades 9, 10, or 11 with the policy change. Thus, we consider the potential nonlinearitiesin the returns to schooling estimates by grade level.

III. Turkey’s compulsory schooling reform

Prior to the 1997 reform in Turkey, the school system consisted of 5 years of primaryeducation followed by 3 years of lower secondary and 3 years of high-school education.Only the first 5 years were compulsory. In 1997, the government increased compulsoryschooling from 5 to 8 years. With the reform, the first 8 years of education were redefined asprimary education, again followed by 3 years of high school. This policy was implementednationwide, and its timing was closely related to the political developments of the time.The major motivation for the new policy was to restrict religious education.9 Unlike somemajor schooling and health reforms in other contexts that are made possible by better-than-average economic conditions, the reform in Turkey was independent of the macroeconomiccontext, and therefore did not coincide with other policies that would have a bearing onschooling outcomes.

8A difference between our context and that of Oreopoulos (2006) is that in our context, there are those who do

not accept the treatment even though they are bound by it (never-takers). Therefore, our LATE is not equal to thetreatment on the non-treated.

9This was achieved primarily in two ways. First, the middle school levels (grades 6–8) of ‘Imam Hatip schools’,

which provide a combination of religious and secular education, were closed with the introduction of 8 years ofcompulsory education. These schools still provided education at the high-school level. Second, students who enrolledin Quranic schools, which provide only religious education, immediately upon the completion of compulsory schoolhad to delay their attendance for 3 years.



Prior to 1997, the dropout rate after the completion of 5 years of compulsory educationwas very high. According to the enrolment ratios reported by national education statistics,in the 1996–97 school year, 1 year before the policy change took effect, almost 40% ofstudents dropped out of school immediately after earning a primary school degree. Theextension of compulsory school from 5 to 8 years resulted in a sharp increase in thenumber of students in grades 6–8. In fact, the number of students enrolled in grades 1–8increased by around 16% – from slightly over 9 million students to close to 10.5 million –between the 1996–97 and 2000–01 school years. The Ministry of Education respondedto these increases with a number of measures to ensure that all students were schooledwithout a significant decline in education quality. These measures included constructionof new schools, increase of capacity in existing schools, hiring of new teachers, bussingof students, and construction of boarding schools for those in rural areas. (Kirdar et al.(2015) documents a detailed account of these changes.) As a result, the student-to-classratio, which rose from 28.6 in the 1997–98 school year to 31.2 in the 1999–2000 school year,fell to 28.3 in the 2001–02 school year and continued to decline with further investment ineducation. The student-to-teacher ratio remained steadily around 30 in the initial years ofthe policy change and fell below 28 by early 2000. While the newly hired teachers lackedthe experience of existing teachers, they had more exposure to newer computer-assistedteaching techniques. Thus, the effect of new teacher hiring on instruction quality is unclear.

These changes in the schooling infrastructure and the substantial increase in the studentpopulation with the policy might raise concerns about a deterioration in the quality ofschooling. However, evidence from the TIMSS 1999 and 2007 international tests thatcover grade 8 students indicates no such deterioration at all. These tests aim to uncoverthe trends in mathematics and science achievement over time and reflect the quality andcontent of instruction in these subjects. The cohort of 8 graders in Turkey who participatedin TIMSS 1999 was not affected by the compulsory schooling reform whereas those whoparticipated in TIMSS 2007 were affected. Between 1999 and 2007, the mathematicsachievement score of Turkey increased by 3 points (from 429 to 432) while the averagescore among all participating countries declined by 37 points (from 487 to 450) (MEB,2007). When we examine the changes by gender, we see that both males and femalesimproved their mathematics scores by 3 points in this period. The improvement in scienceachievement amongTurkish students was more pronounced: while the average score amongall participating countries decreased by 23 points (from 488 to 465), it increased by 21points between 1999 and 2007 (from 433 to 454) for Turkey. Over this period, the averagescience score increased by 26 points for girls and by 18 points for boys. Thus, these resultssuggest that there was no deterioration in the quality of schooling following the compulsoryschool reform.10

The reform also brought about a shift of students across different education streams byeliminating religious schools (called Imam-Hatip schools) and technical education at thelower secondary level. In the 1996–97 school year, 11.5% of male and 13.1% of femalesecondary school students were enrolled in Imam-Hatip schools. The curriculum in theseschools is parallel to non-vocational schools in terms of secular education. Students are,

10Note that the improvements in test scores are modest in size and unlikely to have a significant effect on our point

estimates. The 3-point increase in the math score corresponds to a 2.7% of a standard deviation increase while the21-point increase in the science score corresponds to a 23.1% of a standard deviation increase.


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however, also required to complete certain additional courses on religion. Since students inImam-Hatip schools cover the same subject matter as those in non-vocational schools, theyare able to go on to secular education and major in any field at university. Thus, there is noreason to expect a fall in the productivity of students who would attend religious secondaryschools in the absence of the policy, as most of these students work in jobs not relatedwith their religious education. A difference in productivity could be expected, however, forstudents in technical tracks, which aim to meet the semi-skilled worker requirements of themarket. Nonetheless, the fraction of students enrolled in technical secondary schools wasvery small. In the 1996–97 school year, the year before the new policy, this fraction wasonly 1.3%. Thus, the shift of students from technical tracks to the general track is unlikelyto lead to a significant bias in our estimates.

The education reform of 1997 went into effect for the 1997–98 school year. It coveredstudents who finished grade 4 or a lower grade at the end of the 1996–97 school year –those who did not hold a primary education diploma at the beginning of the 1997–98 schoolyear. Thus, students who started school in September 1993 or afterward were bound bythe policy, whereas students who started school in September 1992 or earlier were exemptfrom it. Most children in Turkey start school at the age of six. Conditional on this schoolstart age, children who were born before September 1986 would not be affected by thispolicy.

Next, we present the change in school attainment with the policy using micro-level datafrom the 2002–13 Turkish HLFS. Figure 1 displays the fraction of children who completegrade 8 by birth year for men and women. While panel (a) uses all data points, panel (b)uses a bubble which excludes the 1986 and 1987 birth cohorts around the cut-off due to thefuzziness in the treatment status of these cohorts. Separate linear polynomials are fitted onboth sides of the cut-off. The exclusion of the bubble comes at the cost of extrapolating thepolynomials within the bubble until the cut-off. Both panels of Figure 1, particularly panel(b), show significant discontinuities between the 1986 and 1987 birth cohorts for bothmen and women, as well as non-trivial time trends both before and after the discontinuity.Figure 2, which presents the fractions of birth cohorts completing at least high school,shows significant spillover effects of the policy on high-school completion rates for bothmen and women. For women, these spillover effects on high-school completion are evenmore striking. These effects are especially visible in panel (b), where a bubble is used. Infact, this panel indicates that the fraction of women completing at least high school jumpsfrom just over 40% right before the cut-off to almost 50% right after the cut-off (see Kirdaret al. (2015) for more on these spillover effects). Overall, the policy has been extremelyeffective in increasing schooling among males and females, not only at the newly mandatedgrades 6–8 but also at the high-school grade levels.

In addition to the jump observed in educational attainment, a comparison of the slopesof the polynomials fitted on both sides of the cut-off indicates a change in trend for grade8 completion in Figure 1. While the trend for men and women were similar prior to thepolicy reform, the trend for men slows down but the trend for women increases followingthe reform. This is likely to be driven by the fact that grade 8 completion was muchlower for women prior to the policy reform. With the enforcement of the law that aimeduniversal completion for both genders, the policy bite on women has been stronger that ledto an increased trend. This, however, does not pose a problem for our identification as we



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Figure 1. Fraction completing at least grade 8Notes: (a, b) The sample includes individuals aged 18 or older in the 2002–13 Turkish Labor Force Surveys.Panel (b) excludes the 1986 and 1987 birth cohorts for which the treatment status is fuzzy. The fitted lines arelinear polynomials.

estimate returns to schooling through an RD design that exploits the level break in grade8 completion around the cut-off.11

IV. Data

The data used in the analysis come from the 2002–13 Turkish HLFS. HLFS is a nationallyrepresentative survey of individuals in Turkey. We use all rounds of HLFS data that includewage and employment information for individuals aged 15 and over. The data report theage, level of educational attainment, hours of work for the reference week, and earningsof individuals during the past month, including bonus payments and premiums.

The sample is restricted to full-time workers, and it therefore excludes workers withfewer than 30 hours worked during the reference. Since the policy change had significantspillover effects on high-school completion, we restrict our sample to those who are at least18 years old in the survey year in order to avoid excluding individuals who are affected bythe policy but who are still at school. There is no information in the data about the earningsof self-employed individuals; thus, the analysis is restricted to wage and salary earners only.This restriction is relatively parsimonious in our context because as the primary sample

11The larger gains in grade 8 completion among women over time implies a larger increase in the supply of women

with that education level compared to men with similar education. In labour markets segregated by gender, if suchsupply side effects are substantial one might expect female wages to be depressed more than men for that educationgroup.


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Figure 2. Fraction completing at least high schoolNotes: (a, b) The sample includes individuals aged 20 or older in the 2002–13 Turkish Labor Force Surveys.Panel (b) excludes the 1986 and 1987 birth cohorts for which the treatment status is fuzzy. The fitted lines arelinear polynomials.

includes only young workers, the fractions of wage earners are high: about 89% for menand 95% for women. We also trim the top 1% and bottom 1% of the wage distribution toexclude outlier observations.

We also exclude college graduates in our primary sample due to the following. Oursample includes all individuals in the labour force who are 18 and older; hence, youngerindividuals in our sample are less likely to be college graduates. In addition, due to the ratherrecent implementation of the policy, the treated individuals are on average younger than thenon-treated individuals in our sample. These two facts together imply that compared to thetreated individuals, the non-treated individuals have a higher fraction of college graduates.(This issue is particularly important for the female wage-earner sample because labourforce participation is very highly correlated with education for women.) The exclusionof college graduates provides a sample where the treated and the control groups are moresimilar in terms of their educational distributions.12 This exclusion would be problematic ifselection into college education were to change as a result of the policy because, in that case,the exclusion of college graduates would create an imbalance in terms of the unobserved

12In their study of intergenerational transmission of human capital, Black, Devereux and Salvanes (2005) also

restrict their sample to parents whose educational attainment is below a certain grade level. However, their goal is toincrease the strength of the instrument in the first-stage estimation.



characteristics of treated and untreated units. However, we show at the beginning ofsection VI that the data provide no evidence of a policy effect on college graduation.Therefore, a comparison of individuals with less than college education provides a com-parison between similar individuals.13 In order to test robustness of our results to thissample restriction, we also report estimates from a sample that includes college graduates.In this case, however, in order to avoid excluding individuals who are still attending college,we limit our sample to individuals who are 24 years old or older.

The HLFS surveys do not include information on completed years of schooling, butincludes information on the highest completed level of schooling. Therefore, we refer tothe Turkish Demographic and Health Surveys (TDHS), which include information on bothcompleted degrees and completed years of schooling, to find the distribution of years ofschooling conditional on the highest completed schooling level. Using this information,we generate the mean years of schooling for each of the highest completed schooling levelsin the HLFS.14 The birth year of individuals, which determines exposure to the policy, isgenerated by subtracting the reported age from the survey year. We define a policy dummy,which is equal to one for those born in 1987 or later and zero for earlier birth cohorts. Thispolicy dummy is used as an instrument for schooling.

The variation across workers in annual earnings reflects the number of hours they workin a year as well as the differences in the hourly earnings. The annual hours of work coulddiffer across educational groups because workers who are more educated may be morelikely to be employed at a given time or more likely to work for longer hours (Card (1999)provides evidence for the latter in the US context). Therefore, the primary measure ofearnings used in this study is earnings per hour. Using information on monthly income andhours of work, we compute the hourly wages (monthly income/(weekly hours*4.3)), andwe use the log hourly wages as our dependent variable.

13We also examine the implications of this exclusion within the context of RDD, by comparing the frequency

distributions of the samples with and without college graduates over the running variable. To visualize this issuebetter, for each value of year of birth, we plot the ratio of the frequency of the sample without college graduates to thefrequency of the sample with college graduates in Figure A3 of the Appendix. The figure suggests no discontinuityaround the cut-off. We also conduct formal tests to examine whether there is any jump at the cut-off of the frequencydistribution of the running variable using RDD with split time trends and various polynomial orders, a la McCrary’s(2008) density test but using parametric specifications. We find no evidence of a jump.

14FigureA4 in theAppendix displays the distribution of years of schooling based on the 2008 TDHS for individuals

who are older than 18 years of age and who are born between 1958 and 1995 (in accordance with our full sample).There are few people who drop out of school in between two schooling attainment levels below the college level.There are clear spikes at 5, 8 and 11 years of schooling, which are the minimum required years to earn, respectively,a primary, middle and high school diploma. There are no clear spikes above the high school level because of theexistence of 2-year as well as 4-year colleges; however, this is not a problem as we exclude college graduates fromour main sample. Using information also on schooling attainment levels, we find that the average years of schoolingis 0.15 years for illiterates, 2.05 years for literates with no degrees, 5.11 years for primary school graduates and8.44 years for secondary school graduates. Thus, in generating the years of schooling variable, we take 0 years forilliterates, 2 years for literates with no degrees, 5 years for primary school graduates, 8 years for secondary schoolgraduates and 11 years for high school graduates. Since there are very few dropouts in non-degree-attaining schoolyears, the extent of measurement error is very small. The measurement error in the generated years of schoolingvariable, resulting from its grouping, is correlated with the true value of the years of schooling; hence, we have anon-classical measurement error problem. Our instrumental variable approach would solve this problem only if theinstrument is correlated only with the true value of years of schooling – but not with the measurement error in yearsof schooling.


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V. Identification method and estimation

Our goal is to establish a causal link between schooling and wages in the Turkish context.The well-known problem in establishing this causal link is the endogeneity of school-ing, which is brought about by omitted variables such as ability, motivation and parentalconnections. To solve this problem, we use a regression discontinuity design in whichwe compare the education attainment and earnings of individuals who are treated by theeducation reform with those of individuals who are not treated.

Under perfect enforcement of the education reform, completion of grade 8 would beuniversal for all cohorts affected by the reform. However, Figure 1 clearly shows that al-though there was a large jump at the cutoff, it took some years before the grade 8 comple-tion rate converged to one. This indicates imperfect compliance with the new compulsoryschool law. In addition, late implementation of the policy in certain areas (e.g. rural areasin which bussing schemes had to be established) could mean that some children who areborn within a year after December 1986 are not affected by the policy. Furthermore, somechildren who are born before December 1986 but start school later than the normal age,which is frequent in Turkey, would be bound by the policy. On the contrary, some who areborn after December 1986 but start school earlier than the normal age (and thus have aprimary school diploma by the time of the policy) would be exempt from the policy. Thisleads to further fuzziness around the cutoff date.

The imperfect compliance with the policy, as well as the other factors affecting theexposure to the policy discussed above, raises the possibility that those whose educationincreases due to the reform may be different in terms of unobserved characteristics thanthose whose education remains unaffected due imperfect enforcement. The fuzzy regres-sion discontinuity design – which is equivalent to a two-stage least squares estimation(Hahn et al., 2001) – addresses this problem using the random assignment of the instru-mental variable. In our context, we use exposure to the education reform as our instrument.Next, we outline how we use this method to find the causal link between schooling andwages. The first stage equation is given by:

si =�0 +�1Di +�1xi +· · ·+�jxji +X ′�+ui (1)

Here, s denotes the years of schooling, D is a dummy variable for the policy, xi is birth-yearof individual i – which is the running variable.To account for the time trends in the outcomevariable, we use polynomial terms of the running variable xi. The results are reported upto the fourth order (j =1, 2, 3 and 4). Covariates are shown by X , which include dummiesfor each age and a dummy for urban status.15 The second stage equation is:

log wi =�0 + �si +�1xi +· · ·+�jxji +X ′�+ vi (2)

where w denotes the wage rate.The key parameter of interest is �, which denotes the percentchange in wages when years of schooling are raised by one. To check the robustness of ourresults, we also estimate equations (1) and (2) using split time trends that allow the orderof the running variable to differ before and after policy cutoff.

15In an alternative specification, we also include dummies for 26 NUTS-2 level regions. We do not include them

in our main specification because region information is missing in the 2002 and 2003 data. Since the dataset is notlongitudinal, we cannot include survey year dummies in addition to the age and year of birth.



In the estimation of equations (1) and (2), we take different time windows of birthcohorts and define our samples accordingly. Since the youngest individual in our data setcovering the 2002–13 period is 18 years old, the latest birth cohort in our sample is 1995.As a result, we have nine birth cohorts after the cut-off (1987–95). Accordingly, we takenine birth cohorts before the cut-off and define sample C as the 1978–95 birth cohorts.In sample D, we widen our time window by adding 10 additional birth cohorts before thecut-off; thus, sample D contains the 1968–95 birth cohorts. In turn, sample E adds 10 morebirth cohorts before the cut-off, and thus includes the 1958–95 birth cohorts. The oldestindividual is 35 years old in sample C, 45 years old in sample D and 55 years old in sample E.Widening the sample time window allows us to specify higher order polynomials in therunning variable in equations (1) and (2), especially when we take split time trends on bothsides of the cut-off.

Using observations far away from the cut-off may raise concerns that these observationsexert a substantial influence on the estimates. Therefore, starting with sample C, we testthe sensitivity of our results by zooming in around the cut-off. For this purpose, we includetwo more time windows: sample A contains the 1982–91 time interval, which includesfive birth cohorts on either side of the cut-off, while sample B contains the 1980–93 timeinterval, which includes seven birth cohorts on either side.16

We use various specifications in terms of polynomial order of the running variablewith all samples. However, with the shorter time intervals, we prefer specifications withlower polynomial orders as the risk of overfitting increases with higher orders. The riskof misspecification of the functional form would fall as we take narrower time windowsaround the cut-off.17 In particular, fitting a fourth-order polynomial with all samples butthe full-sample in panel (E) and fitting a third-order polynomial with samples (A) and (B)(which include 5- and 7-year time intervals on each side of the cut-off, respectively) arevery demanding. Therefore, we use first and second order polynomials with samples (A)and (B), first- to third-order polynomials with samples (C) and (D), and first- to fourth-orderpolynomials with sample (E).

Finally, we put much effort in obtaining accurate standard errors in the estimation.In our data, each observation is not independent due to the group structure – the policyvariable does not vary within birth-year clusters. In this case, failure to account for within-cluster error correlation could significantly overstate estimator precision, which is wellknown since Moulton (1986). Therefore, we use cluster-robust standard errors. However,when the number of clusters is small, even clustered standard errors might not be goodenough (Angrist and Pischke, 2009; Cameron, Gelbach and Miller, 2008) because theasymptotic distribution for clustered standard errors is based on a large number of clusters.We have 18 clusters in our sample with the narrowest time window; however, since theclusters are unbalanced in terms of the sample size, the effective number of clusters couldbe fewer as illustrated by MacKinnon and Webb (2013). Hence, in order to address the few

16This is in the same sprit with the discontinuity samples of Angrist and Lavy (1999) and Grepin and Bharadwaj

(2014). To eliminate the concern that observations far away from the cut-off exert a substantial influence on theestimates, van der Klaauw (2002) also suggests to drop the outermost points and examine whether the estimatedimpacts remain approximately constant.

17van der Klaauw (2008, p. 235) argues that ‘A linear control function is likely to provide a reasonable approxi-

mation of the true functional form within a small neighbourhood of the cut-off’.


1058 Bulletin

clusters issue, we use a number of approaches – outlined in Cameron and Miller (2015) –in addition to the standard cluster-robust estimates, which include: (i) inference based ona T distribution with adjusted degrees-of-freedom, (ii) parametric Moulton correction ofstandard errors,18 (iii) wild cluster bootstrap.19

Since fuzzy regression discontinuity design is equivalent to 2SLS estimation, the usualassumptions about a valid instrument need to hold. In addition to random assignment, thatthe instrument is independent of wages conditional on covariates, the instrument must haveno direct effect on wages other than through its effect in the first stage.20 In our context,the timing of the reform has nothing to do with wages because its timing was the resultof political developments. As explained in detail in section III, the secular governmentthat came to power just before the 1997 reform, saw this reform as a means to curtailreligious education. In addition, there is no reason to expect birth year to be correlatedwith ability, motivation, or parental connections. At the same time, a potential confounderin our analysis is the change in labour market experience of individuals as the policyinduces more years of schooling. Individuals born after 1987 have more schooling due tothe reform but also less labour market experience at a given age. Thus, to the degree thatemployment occurs before age 15 (the ages that the policy targeted lie in this range) andexperience is rewarded in the labour market, our estimate of the return to education wouldbe biased downward. However, in the Turkish context, the incidence of employment wasvery low among children of age 11–13 who were targeted by the compulsory schoolingreform. Therefore, the change in labour market experience is unlikely to be an importantconfounder in our analysis.21

VI. Results

Policy effects on college degree attainment

The analysis above shows that the education reform substantially increases the fraction ofchildren who complete grade 8 and has some spillover effects on high-school completion.In this subsection, we check whether the policy has any effects on schooling beyond highschool. For this purpose, we estimate the following equation:

18Moulton-factor adjusted standard errors for OLS and 2SLS are calculated using the Stata program available at

http://economics.mit.edu/faculty/angrist/data1/data/anglavy99.19

Cameron et al. (2008) and Cameron and Miller (2015) implement wild-cluster bootstrap for the few-clustersproblem in the OLS setting and find that it performs much better than the standard cluster-robust inference (as wellas inference based on alternative techniques) in Monte-Carlo rejection rates of the null hypothesis. Davidson andMacKinnon (2010) develop wild cluster bootstrap methods for IV; however, their main concern is the weak-instrumentproblem and they do not allow for clustering. Gelbach, Klick and Stratman (2009) apply a variant of the wild-clusterbootstrap in Cameron et al. (2008) to an IV setting; in fact, for wild-cluster bootstrap we use the program by Gelbachat http://gelbach.law.upenn.edu/ado/wildbs new.ado.

20Another assumption of the LATE framework is monotonicity: the policy does not decrease individuals’ years of

education. We cannot test this using our data because we do not know the exact years of schooling.21

Prior to the reform, some children may have been working as wage employees after finishing the fifth grade(against the child labour laws). With the reform, 11- to 13-year-old children who would be employed in the absenceof the policy were forced to attend school. However, the incidence of wage employment among this group prior tothe reform was small. Using the 1990 Turkish Census, we find that about 3.5% of the children in this age range werewage employees.



Ci =�0 +�1Di +�1xi +· · ·+�jxji +X ′�+ui (4)

Here, Ci denotes a dummy variable that equals 1 if the individual has a university degreeand 0 otherwise. Since the outcome variable is college attainment, the sample is restrictedto individuals who are 22 years old or older in the 2002–13 Turkish Labor Force Surveys.Therefore, the youngest cohort in this sample is the 1991 birth-cohort, resulting in onlyfive birth cohorts after the sample, which decreases our capability of fitting high orderpolynomials in the running variable. Samples A–C of this subsection keep the oldest birthcohorts as they are defined in section V.

Table 1 presents the results on the policy effect on college degree by gender for the threedifferent samples defined by time window and for various orders of polynomials in the run-ning variable. For men, the estimates in general indicate no effect of the reform on collegeattainment. The coefficients are close to zero and statistically insignificant with samples(A)–(C), which have narrower time windows. The coefficients with samples (D) and (E) arestatistically significant with linear trends; however, significance vanishes once higher orderpolynomials are used, as it is apt with wider time windows, except for one case: sample Ewith a cubic polynomial. For women, the patterns over the samples and specifications aresimilar; however, the coefficient estimates are larger in magnitude. Consequently, with thelinear trends in column (6), statistical significance exists also with sample (A). However,with second and higher order polynomials, there is statistical significance only in one case:sample (E) with a cubic polynomial.

In Table A1 of the Appendix, we investigate whether the three potentially concerningstatistically significant cases with cluster-robust standard errors (sample E with a cubictrend for men, sample A with a linear trend for women and sample E with a cubic trendfor women) could be an artefact of the few-clusters problem. Table A1 shows that the onlystatistically significant case for men, which is only marginally significant, in fact vanisheswith the Moulton-factor adjustment. Moreover, several tests with wild cluster bootstrapindicate no evidence of a policy effect on college degree. The two statistically significantcases for women persist with the Moulton-factor adjustment. However, again the majorityof tests with wild cluster bootstrap indicate no evidence of a policy effect on college degree.

Overall, these results indicate no evidence of a policy effect on college degree for men.For women, while the estimated coefficients are larger, they are not statistically significantin most cases; and, whenever they are, they are not robust to further scrutiny on the few-clusters issue. Since no evidence for a spillover effect on college graduation exists, we canexclude college graduates from our sample and choose to do so for the reasons explainedearlier in the Data Section. Nonetheless, we check the robustness of our findings with asample that includes college graduates in section VII.

Policy effects on employment outcomes

The validity of our instrument in establishing the causal link between schooling and wagesrequires that the instrument have no effect on wages other than through its effect on school-ing. However, the policy could also change the employment status of individuals, therebyaffecting the distribution of observed wages. To understand this issue, we examine theeffects of the policy on employment and wage employment outcomes in this subsection.


1060 Bulletin

TAB

LE

1

Polic

yef

fect

onco

llege

degr

ee

Bir

thco

hort

s(1

)(2

)(3

)(4

)(5

)(6

)(7

)(8

)(9

)(1

0)M

enW

omen

OLS

OLS

OLS

OLS

Sam

ple

size

OLS

OLS

OLS

OLS

Sam

ple

size

(A)

1982

–91

0.00

20.

005

––

197,

298

0.01

8*0.

014

––

214,

211

[0.0

05]

[0.0

04]

––

[0.0

09]

[0.0

09]

––

(B)

1980

–91

−0.0

020.

005

––

283,

431

0.01

20.

013

––

310,

017

[0.0

04]

[0.0

04]

––

[0.0

07]

[0.0

10]

––

(C)

1978

–91

−0.0

010.

003

0.00

2–

366,

747

0.01

7**

0.01

10.

011

–40

2,40

7[0

.004

][0

.004

][0

.004

]–

[0.0

06]

[0.0

09]

[0.0

09]

–(D

)19

68–9

10.

008*

*−0

.001

0.00

3–

755,

815

0.02

9***

0.00

80.

017

–82

1,32

9[0

.003

][0

.004

][0

.004

]–

[0.0

06]

[0.0

07]

[0.0

10]

–(E

)19

58–9

10.

017*

**−0

.008

0.00

9*0.

000

1,10

9,85

50.

041*

**0.

007

0.01

5*0.

011

1,18

9,78

4[0

.004

][0

.005

][0

.005

][0

.006

][0

.007

][0

.006

][0

.008

][0

.008

]Po

lyno

mia

ldeg

ree

Firs

tSe

cond

Thi

rdFo

urth

Firs

tSe

cond

Thi

rdFo

urth

inbi

rth

year

Not

es:

The

depe

nden

tva

riab

leis

colle

gegr

adua

tion

stat

us.A

llre

gres

sion

sin

clud

eco

ntro

lsfo

rth

epo

licy

dum

my,

apo

lyno

mia

lin

the

runn

ing

vari

able

(yea

rof

birt

h)w

hose

orde

ris

spec

ified

inth

ela

stro

wof

the

tabl

e,ag

edu

mm

ies,

and

adu

mm

yfo

rur

ban

stat

us.A

llsa

mpl

esar

ere

stri

cted

toin

vidu

als

who

are

22or

olde

rin

the

2002

–13

Turk

ish

Lab

orFo

rce

Surv

eys;

ther

efor

e,th

eyo

unge

stin

divi

dual

inth

esa

mpl

eis

born

in19

91.C

lust

erin

gis

done

atth

eye

ar-o

f-bi

rth

leve

l.St

atis

tical

lysi

gnifi

cant

:**

*1%

leve

l;**

5%le

vel,

*10

%le

vel.



Table 2 presents the estimates of the policy effect on employment status for four differ-ent definitions of employment. The sample includes individuals who are 18 or older in the2002–13 Turkish Labor Force Surveys. The results are given for employment of either type(wage or salary worker and self-employed) in panel (A) and for wage employment (wageor salary worker only) in panel (C). Panels (B) and (D) are for full-time employment andfull-time wage employment respectively. Each panel reports results using the specificationin equation (4) where the dependent variable is replaced with the employment status indi-cators. As can be seen from the table, the policy has no effect on the employment statusof men; on the other hand, it increases the employment probability of women in panels(B)–(D). The estimated effects range between 0.4 and 1.1 percentage points. These effectsare substantial given that the wage employment probability for women in this age bracketis just above 14%.22

These findings imply that we need to be careful in interpreting the findings for womenbecause the reform not only increases the education of women who would be employedregardless of the policy, but it also pushes other women into wage employment who wouldotherwise not be employed as wage earners. Consequently, the pool of employed womenwho are affected by the policy might be different in ways that pertain to their wagesfrom employed women who are not affected by the policy. However, the women who arenew entrants to employment with the policy would be those who were on the margin ofemployment before the policy; therefore, they are not likely to be substantially differentfrom the average employed woman before the policy in terms of potential wages.

First-stage results: policy effects on schooling outcomes

Here, we examine how the policy changes schooling attainment in our sample of wageearners. Table 3 presents the first-stage results for men and women using different timewindows and orders of polynomials in the running variable. The estimates confirm thatour instrument is highly relevant. The policy increases the years of schooling by more thanhalf a year for both men and women. The estimates are very consistent over the majorityof samples and various degrees of polynomials. A comparison of estimates for men andwomen show that the effect on men is actually somewhat bigger, which seems to contradictFigures 1 and 2. However, the sample in Table 3 is restricted to wage earners whereas thesamples in Figures 1 and 2 are not. Since wage earners among women are more likely tohave higher levels of education than wage earners among men in Turkey (Dayioglu andKirdar, 2009), their schooling behaviour is less likely to change with the policy. In addition,the F-statistics are much higher than the recommended levels for both men and womenacross all samples and specifications in Table 3.

A closer look at changes in schooling distributions by gender

In order to understand the policy effect on schooling outcomes better, we examine thecumulative distribution function for education (specifically, one minus the cumulative

22In this section, we do not present the standard error estimates under alternative methods because while the

coefficients are already statistically insignificant for men, they are very highly statistically significant (many at the1% level) for women.


1062 Bulletin

TAB

LE

2

Polic

yef

fect

onem

ploy

men

tout

com

es

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

Men

Wom

en

OLS

OLS

OLS

OLS

Sam

ple

size

OLS

OLS

OLS

OLS

Sam

ple

size

(I)

Em

ploy

men

t(A

)19

82–9

1−0

.004

−0.0

03–

–26

9,51

9−0

.002

0.00

0–

–31

5,75

5[0

.004

][0

.004

]–

–[0

.005

][0

.001

]–

–(B

)19

80–9

3−0

.008

*−0

.006

––

367,

416

−0.0

040.

001

––

427,

070

[0.0

04]

[0.0

04]

––

[0.0

06]

[0.0

01]

––

(C)

1978

–95

−0.0

09*

−0.0

05−0

.004

–44

9,58

8−0

.006

0.00

10.

000

–51

9,65

1[0

.004

][0

.004

][0

.004

]–

[0.0

05]

[0.0

01]

[0.0

01]

–(D

)19

68–9

50.

001

−0.0

03−0

.003

–78

2,40

7−0

.021

***

0.00

20.

002

–90

0,10

3[0

.004

][0

.004

][0

.003

]–

[0.0

06]

[0.0

02]

[0.0

02]

–(E

)19

58–9

5−0

.004

0.00

6−0

.002

−0.0

07**

1,09

7,84

0−0

.030

***

−0.0

030.

002

0.00

31,

248,

630

[0.0

05]

[0.0

05]

[0.0

05]

[0.0

04]

[0.0

07]

[0.0

03]

[0.0

02]

[0.0

02]

(II)

Full-

time

empl

oym

ent

(A)

1982

–91

−0.0

03−0

.001

––

268,

555

0.00

20.

004*

*–

–31

4,93

5[0

.004

][0

.004

]–

–[0

.004

][0

.001

]–

–(B

)19

80–9

3−0

.008

−0.0

04–

–36

6,10

90.

003

0.00

7***

––

425,

989

[0.0

05]

[0.0

04]

––

[0.0

04]

[0.0

02]

––

(C)

1978

–95

−0.0

09−0

.003

−0.0

02–

448,

014

0.00

20.

007*

**0.

004*

**–

518,

311

[0.0

05]

[0.0

03]

[0.0

04]

–[0

.004

][0

.002

][0

.001

]–

(D)

1968

–95

−0.0

02−0

.001

−0.0

01–

779,

619

−0.0

09**

0.00

7***

0.00

8***

–89

7,56

3[0

.005

][0

.005

][0

.003

]–

[0.0

04]

[0.0

02]

[0.0

02]

–(E

)19

58–9

5−0

.005

0.00

40.

001

−0.0

06*

1,09

3,99

0−0

.015

***

0.00

4*0.

008*

**0.

008*

**1,

244,

885

[0.0

05]

[0.0

05]

[0.0

05]

[0.0

04]

[0.0

04]

[0.0

02]

[0.0

02]

[0.0

02]

cont

inue

d


Low wage returns to schooling in a developing country 1063TA

BL

E2

(Con

tinue

d)

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

(9)

(10)

Men

Wom

en

OLS

OLS

OLS

OLS

Sam

ple

size

OLS

OLS

OLS

OLS

Sam

ple

size

(III

)Wag

eem

ploy

men

t(A

)19

82–9

10.

009

0.01

1**

––

268,

555

0.00

30.

004*

**–

–31

4,93

5[0

.005

][0

.004

]–

–[0

.002

][0

.001

]–

–(B

)19

80–9

30.

000

0.00

5–

–36

6,11

00.

007*

*0.

009*

**–

–42

5,98

9[0

.007

][0

.005

]–

–[0

.003

][0

.002

]–

–(C

)19

78–9

5−0

.003

0.00

40.

006

–44

8,01

50.

005

0.00

9***

0.00

8***

–51

8,31

1[0

.007

][0

.004

][0

.004

]–

[0.0

03]

[0.0

02]

[0.0

02]

–(D

)19

68–9

50.

000

0.00

50.

005

–77

9,62

0−0

.005

*0.

009*

**0.

009*

**–

897,

563

[0.0

06]

[0.0

06]

[0.0

04]

–[0

.003

][0

.002

][0

.002

]–

(E)

1958

–95

0.00

20.

005

0.00

5−0

.002

1,09

3,99

1−0

.009

***

0.00

4*0.

009*

**0.

010*

**1,

244,

885

[0.0

06]

[0.0

06]

[0.0

06]

[0.0

05]

[0.0

03]

[0.0

02]

[0.0

02]

[0.0

02]

(IV

)Fu

ll-tim

ew

age

empl

oym

ent

(A)

1982

–91

0.00

90.

011*

*–

–26

8,55

50.

004

0.00

5***

––

314,

935

[0.0

06]

[0.0

04]

––

[0.0

03]

[0.0

01]

––

(B)

1980

–93

0.00

00.

006

––

366,

110

0.00

8*0.

011*

**–

–42

5,98

9[0

.008

][0

.004

]–

–[0

.004

][0

.003

]–

–(C

)19

78–9

5−0

.004

0.00

6*0.

007

–44

8,01

50.

006

0.01

1***

0.00

8***

–51

8,31

1[0

.009

][0

.003

][0

.004

]–

[0.0

04]

[0.0

02]

[0.0

02]

–(D

)19

68–9

5−0

.003

0.00

60.

006

–77

9,62

0−0

.004

0.01

1***

0.01

1***

–89

7,56

3[0

.007

][0

.007

][0

.004

]–

[0.0

03]

[0.0

03]

[0.0

03]

–(E

)19

58–9

5−0

.002

0.00

40.

007

−0.0

011,

093,

991

−0.0

07**

0.00

6**

0.01

1***

0.01

1***

1,24

4,88

5[0

.006

][0

.007

][0

.007

][0

.005

][0

.003

][0

.003

][0

.002

][0

.003

]Po

lyno

mia

ldeg

ree

Firs

tSe

cond

Thi

rdFo

urth

Firs

tSe

cond

Thi

rdFo

urth

Not

es:

The

depe

nden

tva

riab

leis

empl

oym

ent

stat

usin

pane

l(I

),fu

ll-tim

eem

ploy

men

tst

atus

inpa

nel

(II)

,w

age-

empl

oym

ent

stat

usin

pane

l(H

I)an

dfu

ll-tim

ew

age-

empl

oym

ents

tatu

sin

pane

l(IV

).A

llre

gres

sion

sin

clud

eco

ntro

lsfo

rthe

polic

ydu

mm

y,a

poly

nom

iali

nth

eru

nnin

gva

riab

le(y

earo

fbir

th)w

hose

orde

ris

spec

ified

inth

ela

stro

wof

the

tabl

e,ag

edu

mm

ies,

and

adu

mm

yfo

rur

ban

stat

us.A

llsa

mpl

esar

ere

stri

cted

toin

vidu

als

who

are

18or

olde

ran

dha

vean

educ

atio

nala

ttain

men

tbel

owco

llege

degr

eein

the

2002

–13

Turk

ish

Lab

orFo

rce

Surv

eys;

ther

efor

e,th

eyo

unge

stin

divi

dual

inth

esa

mpl

eis

born

in19

95.C

lust

erin

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1064 BulletinTA

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Primary School Degree or Higher High School Degree or HigherFemale Male Female Male

Figure 3. Difference in schooling distributions before and after the policyNotes:The distributions are one minus cumulative distributions.The sample includes 18- to 26-year-old fulltimewage earners. The distribution before the policy is for the 1984 and 1985 birth cohorts, and that after the policyis for the 1988 and 1989 birth cohorts.

distribution function) in our sample by gender. Figure 3 displays how this cumulativedistribution function changes with the policy; for this purpose, we compare the 18- to26-year-olds in the 1984 and 1985 birth cohorts in our sample (who are not affected by thepolicy) with the same age group in the 1988 and 1989 birth cohorts (who are affected).23 Ascan be seen from the figure, the fraction of men who finish eight or more years of schoolingincreases by 24.72 percentage points, whereas the fraction of men who finish high schoolor a higher level of schooling increases by 2.97 percentage points. Among women, therespective percentage-point changes are 14.78 and 5.34. In other words, the ratio of therise in the fraction earning a high-school degree or higher to the rise in the fraction earninga primary school degree or higher is much higher among women (0.36) than men (0.12).

Put differently, in our sample of wage earners, the policy pushes a higher fraction ofmen to finish 8 years of schooling because compared to women, a larger fraction of malewage earners have a terminal primary school degree. On the other hand, a larger fraction offemale wage earners have a high-school degree or higher; therefore, they are more likelyto include compliers who are induced to finish high school by the reform. Thus, withinthe LATE interpretation of our estimates, a much higher fraction of female compliers aredrawn from high school graduates. Therefore, potential differences in returns to schoolingacross grade levels could make a substantial difference between the returns to schoolingestimates for men and women. This issue is critical in understanding the differences inreturns to schooling by gender.

Second-stage results

Before we present our 2SLS estimation results on the effect of schooling on wages, weexamine the effect of the reform on wages. Figure 4 displays the evolution of mean log

23We take only these birth cohorts around the cutoff in order to minimize the potential effect of a time trend.


1066 Bulletin

0

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Figure 4. Log wages by year of birthNotes: The coefficients (symbols) and confidence intervals (dashed lines) indicate the estimates of birth-yeardummies from a regression of log wages on birth-year dummies, age dummies, and a dummy for urban status.The curves (thick lines) are quartic polynomials that are fit separately (on the coefficient estimates) on eachside of the cut-off. The sample includes fulltime wage earners who are 18 or older and have an educationalattainment lower than a college degree in the 2002–13 Turkish Labor Force Surveys.

wages across birth cohorts for men and women. This figure does not simply plot the meanlog wages by birth year because later birth-cohorts are on average younger and thus havelower wages. To account for this problem, we first regress log wages on a set of birth-yeardummies as well as age dummies; then, we plot the coefficients of birth-year dummies.The figure also displays quartic polynomials fit separately (on the coefficient estimates)on each side of the cut-off. There is no obvious discontinuity around the cut-off for men,which suggests that wages are not significantly affected by the policy. There is, however,a jump for women, suggesting an increase in wages for women with the policy. Given theremarkable policy effect on grade 8 and high school completion, presented in Figures 1and 2, these findings suggest that the effect of schooling on wages in Turkey is small formen but larger for women.

Table 4 presents the OLS and IV-RD estimates of returns to schooling by gender forthe five time windows defined earlier and various degrees of polynomials in the runningvariable. In these specifications, the time trend in the outcome variable is captured by acommon polynomial in the running variable on both sides of the cutoff. We present therobustness of the estimates in Table 4 to alternative methods of adjusting the standarderrors for the few-clusters issue in Table A2 of the Appendix for men and in Table A3 forwomen. Our benchmark case is the cluster-robust standard errors, given in panel (A2) ofboth tables. However, we first present the White heteroskedasticity-robust standard errorsin panel (A1) to gauge the potential importance of clustering. We carry out the parametric



TABLE 4

Instrumental-variable regression-discontinuity estimates

Birth cohorts (1) (2) (3) (4) (5) (6)Men

OLS IV-RD IV-RD IV-RD IV-RD Sample size

(A) 1982–91 0.027*** 0.020** 0.024** – – 107,089[0.002] [0.008] [0.010] – –

(B) 1980–93 0.029*** 0.017** 0.023*** – – 150,905[0.002] [0.007] [0.008] – –

(C) 1978–95 0.032*** 0.026*** 0.022* 0.016 – 191,162[0.002] [0.009] [0.011] [0.011] –

(D) 1968–95 0.051*** 0.102*** 0.025 0.025 – 365,369[0.004] [0.028] [0.017] [0.017] –

(E) 1958–95 0.062*** 0.120*** 0.019 0.023 0.021 494,495[0.004] [0.022] [0.024] [0.018] [0.015]

Degree of polynomial in birth year Fourth First Second Third Fourth

Women

(A) 1982–91 0.035*** 0.057** 0.063** – – 36,439[0.003] [0.026] [0.026] – –

(B) 1980–93 0.040*** 0.074*** 0.065*** – – 48,346[0.004] [0.021] [0.022] – –

(C) 1978–95 0.044*** 0.091*** 0.077*** 0.060** – 57,714[0.005] [0.020] [0.023] [0.026] –

(D) 1968–95 0.061*** 0.113*** 0.079*** 0.078*** – 92,781[0.005] [0.024] [0.023] [0.024] –

(E) 1958–95 0.069*** 0.108*** 0.094*** 0.080*** 0.083*** 113,551[0.005] [0.019] [0.028] [0.025] [0.027]


Notes: The dependent variable is log hourly wages. All regressions include controls for years of schooling (which isinstrumented by the policy dummy in columns (2)–(5)), a polynomial in the running variable (year of birth) whoseorder is specified in the last row of the table, age dummies, and a dummy for urban status. All samples are restricted toinviduals who are 18 or older and who have an educational attainment below college degree in the 2002–13 TurkishLabor Force Surveys; therefore, the youngest individual in the sample is born in 1995.The sample in panel (A) includesfive birth cohorts on both sides of the discontinuity (1982–86 and 1987–91), the sample in panel (B) includes sevenbirth cohorts on both sides (1980–86 and 1987–93) and the sample in panel (C) includes nine birth cohorts on bothsides (1978–86 and 1987–95). The sample in panel (D) is enlarged to include 10 more older birth-cohorts than thesample in panel (C), and the sample in panel (E) includes 10 more older birth-cohorts than the sample in panel (D).Clustering is done at the year-of-birth level. Statistically significant: *** 1% level; ** 5% level, * 10% level.

Moulton correction in panel (A3). In panel (B) of Tables A2 and A3, we carry out certainmethods which do not produce standard error estimates but instead provide P-values for therejection of the null hypothesis (that the returns to schooling is zero). The first two of theseare based on the cluster-robust estimates in panel (A2) but use different rejection methods:T distribution with G-1 and G-2 degrees of freedom.24 The next three P-values come fromwild cluster bootstrap estimations. In each one, a different distribution (Rademacher, Liuand Mammen) is used in generating the auxiliary wild random variable; symmetric tests

24Stata uses a standard normal distribution for P-values of the ivregress command with cluster option.


1068 Bulletin

of the null hypothesis are carried out in all. Using the same set of wild cluster bootstrapt-values, equal-tailed tests of the null hypothesis are carried out in the last three rows.25

The IV-RD estimates for men suggest that the return to an extra year of schooling formen is around 2–2.5%; however, the results are mixed in terms of statistical significance.While the coefficients are statistically significant with samples (A) and (B) under first- andsecond-order polynomials, they are not with samples (C)–(E) under second- or higher-orderpolynomials (except for the case with sample (C) and a second-order polynomial).TableA2of theAppendix shows that – with wild cluster bootstrap estimation – statistical significanceof the coefficients for sample (A) with a second-order polynomial and for sample (C)with a second-order polynomial also vanishes.26 In summary, the coefficients for men arestatistically insignificant for all samples with second- or higher-order polynomials, exceptfor sample (B) with a second-order polynomial.

The estimate for women is around 7–8% and highly statistically significant, regardlessof the time window and the order of the polynomial. The coefficient estimates are alsorelatively stable as we expand the sample from panel (C) to panel (E) and as we zoom inaround the cut-off in panels (A) and (B). Table A3 of the Appendix indicates that statisticalsignificance for all samples (B)–(E) with all orders of polynomials remains regardlessof the method used for the estimation of standard errors. Only for sample (A) and onlywhen standard errors are estimated using wild cluster bootstrap with the symmetric test,statistical significance vanishes. Therefore, we conclude that statistical significance of ourreturns to schooling estimates for women is quite robust.

Table 5 presents returns to schooling estimates from specifications with split time trends,which allow the order of the polynomial in the running variable to differ before and afterpolicy cutoff. Here, we take polynomials of order one in column (1) in all panels and oforder two in column (4) across panels (B)–(E). Since we have a maximum of nine birthcohorts after the cut-off, it becomes difficult to separate the policy effect from the timetrend with third-order polynomials after the cut-off. However, since the time windows insamples (D) and (E) are wider before the cut-off, we allow the polynomials before thecut-off to have higher orders than the polynomials after the cut-off in columns (2), (3), (5)and (6). In particular, we take a second-order polynomial before the cut-off with samples(D) and (E) in column (3) and a third-order polynomial before the cut-off with sample (E)in column (3) while taking a linear polynomial after the cut-off in both cases. Similarly, wetake a third-order polynomial before the cut-off with samples (D) and (E) in column (5) anda fourth-order polynomial before the cut-off with sample (E) in column (6) while takinga second-order polynomial after the cut-off in both cases. While there is some volatilityin the estimates across the specifications, the estimates in the right-most columns for agiven sample – adopting the most flexible split time trends before and after cutoff – are

25Suppose that w(1), w(2),… ,w(999) are the ordered values of the simulated t-ratios in bootstrap. The symmetric

P-value is equal to the proportion of times that |w|> |w(i)|, i = 1,…, 999, where w denotes the t-ratio with the originalsample. In the equaltailed test of 5% level, for instance, the lower 2.5 percentile and the upper 97.5 percentile ofthe ordered w(1), w(2),…,w(999) are taken, then it is tested whether the t-ratio with the original sample falls in thisinterval.

26The results for men in Table A2 of the Appendix are given for samples (A)–(C) with first- and second-order

polynomials, for which statistical significance exists in Table 4 and the number of clusters is smaller.



TABLE 5

Instrumental-variable regression-discontinuity estimates – split time trends around the discontinuity

Birth cohorts (1) (2) (3) (4) (5) (6) (7)Men

IV-RD IV-RD IV-RD IV-RD IV-RD IV-RD Sample size

(A) 1982–91 0.023** – – – – – 107,089[0.010] – – – – –

(B) 1980–93 0.021*** – – 0.030** – – 150,905[0.007] – – [0.015] – –

(C) 1978–95 0.025** – – 0.031** – – 191,162[0.010] – – [0.015] – –

(D) 1968–95 0.068*** 0.024* – 0.047*** 0.010 – 365,369[0.024] [0.012] – [0.014] [0.016] –

(E) 1958–95 0.083*** 0.027 0.014 0.059*** 0.035*** 0.028** 494,495[0.023] [0.018] [0.011] [0.022] [0.014] [0.012]

Degree of polynomial First Second Third Second Third Fourthbefore the cut-off

Degree of polynomial First First First Second Second Secondafter the cut-off

Women

(A) 1982–91 0.062** – – – – – 36,439[0.028] – – – – –

(B) 1980–93 0.069*** – – 0.071 – – 48,346[0.022] – – [0.065] – –

(C) 1978–95 0.083*** – – 0.065* – – 57,714[0.022] – – [0.034] – –

(D) 1968–95 0.094*** 0.077*** – 0.107*** 0.079*** – 92,781[0.026] [0.025] – [0.033] [0.025] –

(E) 1958–95 0.092*** 0.087*** 0.074*** 0.127*** 0.102*** 0.077*** 113,551[0.022] [0.029] [0.024] [0.042] [0.031] [0.025]

Degree of polynomial First Second Third Second Third Fourthbefore the cut-off

Degree of polynomial First First First Second Second Secondafter the cut-off

Notes: The dependent variable is log hourly wages. All regressions include controls for years of schooling (which isinstrumented by the policy dummy in columns (2)–(5)), a polynomial in the running variable (year of birth) – whichis allowed to be different before and after the discontinuity, age dummies, and a dummy for urban status. All samplesare restricted to inviduals who are 18 or older and who have an educational attainment below college degree in the2002–13 Turkish Labor Force Surveys; therefore, the youngest individual in the sample is born in 1995. The samplein panel (A) includes five birth cohorts on both sides of the discontinuity (1982–86 and 1987–91), the sample inpanel (B) includes seven birth cohorts on both sides (1980–86 and 1987–93), and the sample in panel (C) includesnine birth cohorts on both sides (1978–86 and 1987–95). The sample in panel (D) is enlarged to include 10 moreolder birth-cohorts than the sample in panel (C), and the sample in panel (E) includes 10 more older birth-cohortsthan the sample in panel (D). Clustering is done at the year-of-birth level. Statistically significant: *** 1% level;** 5% level, * 10% level.


1070 Bulletin

remarkably similar to those in Table 4, suggesting a 2–3% return for men and 7–8% forwomen.27

Overall, our 2SLS estimate of returns to schooling is around 2–2.5% for men, whichis not statistically significant in most specifications, and around 7–7.5% for women. Theseestimates are significantly lower than those estimated for other developing countries (e.g.Duflo (2001) for Indonesia; Spohr (2003) for Taiwan and Fang et al. (2012) for China),but the estimates for men are similar to those estimated for some European countries (e.g.Devereux and Hart (2010) for the UK and Pischke and von Wachter (2008) for Germany).In addition, the IV-RD coefficient of returns on schooling is lower than the OLS coefficientfor men and higher for women. However, this comparison may be misleading becausesince the IV-RD estimate is for the set of compliers only, the OLS and IV-RD estimatescalculate the average causal effects by assigning very different weights to the causal effectsconditional on schooling level. The next section investigates this issue further by imposingrestrictions on the sample by schooling level in the estimation of average causal effects.

Second-stage results with restrictions on educational attainment

We have already demonstrated that the policy affects schooling outcomes in various gradelevels. Moreover, the resulting changes in schooling distributions are quite different be-tween men and women; a much higher fraction of female compliers in our sample ofwage earners are drawn from high-school graduates. In this section, we try to understandthe variation in the returns to schooling at different schooling levels by placing an upperbound on educational attainment. For this purpose, we exclude high school graduates fromthe sample. The estimation results using a sample of individuals with an educational at-tainment below a high school degree are displayed in Table 6. In this restricted sample,the compliers include only those who are induced to finish grade 8 with the policy. Notethat these compliers include not only those who finish grade 8 with the policy but whowould otherwise only finish grade 5, but also those who finish grade 8 with the policy butwho would otherwise only finish any grade level from 0 to 7.28 Hence, the average causaleffect here is a weighted average of the average causal effect at 1–8 years of schooling;nonetheless, most of the weight comes from grades 6–8.

As can be seen in Table 6, the OLS estimates with samples excluding high schoolgraduates are much lower for both men and women. The 2SLS estimates for men alsoaverage lower than those in Table 4 for each sample but sample (A). For women, the 2SLS

27As an alternative approach, we also use a two-stage least squares estimation in which estimated equations are:

si =�0 +�1Di +X ′�+ui

log wi =�0 +�1si +X ′�+ vi

Covariates are shown by X ; these include dummies for each age and each calendar year, as well as a dummy forurban status. This methodology can be interpreted as an IV-DID method. The estimates of returns to schooling fromthis approach, given in Table A2 in the Appendix, yields estimates that are similar to the estimates of the IV-RDD.

28Although the policy made grades 6–8 compulsory, with the falling costs of enrolment in all primary school

grade levels via bussing and the construction of boarding schools, enrolment in grades 1 through 8 could change. Infact, Kirdar et al. (2015) provide evidence for rising enrolment in grades 1 through 3 in certain areas.



TABLE 6

Estimates of returns to schooling when individuals with a high-school or above degree are excluded

Birth cohorts (1) (2) (3) (4) (5) (6)Men

OLS IV-RD IV-RD IV-RD IV-RD Sample size

(A) 1982–91 0.015*** 0.025*** 0.029*** – – 63,055[0.003] [0.008] [0.010] – –

(B) 1980–93 0.016*** 0.014* 0.024** – – 89,628[0.003] [0.008] [0.009] – –

(C) 1978–95 0.018*** 0.014* 0.018 0.024** – 113,810[0.003] [0.008] [0.013] [0.011] –

(D) 1968–95 0.033*** 0.038*** 0.000 0.008 – 232,900[0.004] [0.011] [0.020] [0.015] –

(E) 1958–95 0.046*** 0.068*** −0.017 0.005 −0.001 325,321[0.005] [0.013] [0.015] [0.018] [0.013]


Women

(A) 1982–91 0.016*** 0.013 5.894 – – 16,090[0.004] [0.151] [660.205] – –

(B) 1980–93 0.017*** 0.026 0.129 – – 21,629[0.004] [0.058] [0.193] – –

(C) 1978–95 0.019*** 0.040 0.173 0.037 – 26,124[0.004] [0.055] [0.177] [0.087] –

(D) 1968–95 0.029*** 0.006 0.089 0.106 – 47,886[0.004] [0.019] [0.107] [0.088] –

(E) 1958–95 0.035*** −0.004 0.028 0.133 0.101 62,305[0.004] [0.016] [0.040] [0.120] [0.069]


Notes: The dependent variable is log hourly wages. All regressions include controls for years of schooling (which isinstrumented by the policy dummy in columns (2)–(5)), a polynomial in the running variable (year of birth) whoseorder is specified in the last row of the table, age dummies, and a dummy for urban status. All samples are restrictedto inviduals who are 18 or older and have an educational attainment lower than a high school degree in the 2002–13Turkish Labor Force Surveys; therefore, the youngest individual in the sample is born in 1995. The sample in panel (A)includes five birth cohorts on both sides of the discontinuity (1982–86 and 1987–91), the sample in panel (B) includesseven birth cohorts on both sides (1980–86 and 1987–93) and the sample in panel (C) includes nine birth cohorts onboth sides (1978–86 and 1987–95). The sample in panel (D) is enlarged to include 10 more older birth-cohorts thanthe sample in panel (C), and the sample in panel (E) includes 10 more older birth-cohorts than the sample in panel(D). Clustering is done at the year-of-birth level. Statistically significant: *** 1% level; ** 5% level, * 10% level.

estimates are much more volatile and they all become statistically insignificant. This ispartly due to the significant fall in the sample size for women with the exclusion of highschool graduates. Therefore, here, we prefer the specifications with lower-order polyno-mials, as identifying the policy effect with high-order polynomials becomes even moredifficult with smaller samples. With linear polynomials, given in column (2) of Table 6,the coefficients for women are much lower than the corresponding coefficients in Table 4.In fact, for samples (A)–(C) – where a linear specification is more acceptable – thecoefficients for women range from 0.13 to 0.40 (and are all statistically insignificant) incomparison to those in Table 4 where they range from 0.57 to 0.91 (and are all statistically


1072 Bulletin

significant). Overall, the comparison of results from Tables 4 and Table 6 indicates that thereturns to an extra year of schooling in high school are higher than the average returns to anextra year schooling in grade levels 1–8 for both men and women. This finding, along withthe difference between genders in the change in schooling distribution (which is illustratedin section ‘A closer look at changes in schooling distributions by gender’) is critical inunderstanding the difference in the estimated returns to schooling by gender, as discussedlater in section VIII.

VII. Robustness checks

In this section, we conduct two key robustness checks using different samples. In the firstone, we place alternative minimum-age restrictions on the initial sample. In the second one,we include college graduates in the sample but place a higher minimum-age restriction –not to have unbalanced groups of treated and non-treated individuals in terms of educationalattainment.

Alternative age restrictions

Tables 4 and 5 indicate low returns to schooling for men. Returns to schooling increase byage in the typical age-earnings profile. In fact, Figure A2 in the Appendix shows that, forboth men and women, the age-earnings profile varies much less across different educationgroups in the beginning of the work lifecycle, and there is less variation across men thanacross women. Therefore, the reported estimates in Tables 4 and 5 may be low simplybecause we observe many individuals in the part of lifecycle where returns to schoolingare lower. An important observation from Figure A2, however, is that differences in the ageearnings profile become already very significant beyond age 22. Thus, if low returns aredriven by the age composition of the sample, then one would expect to see the estimates ofreturns to schooling to become larger as the sample is restricted to older individuals. Wetest the robustness of our estimates by increasing the minimum age successively across thethree panels in Table 7. Panels I, II and III impose the minimum age restrictions of 20, 22and 24 respectively. The coefficient estimates for men are robust across panels suggestingvery low or no returns to schooling; in fact, the coefficients in panels (I) and (II) are evenlower than those in Tables 4 and 5. Similarly, the coefficient estimates for women changelittle across the first two panels and become somewhat larger but also more volatile in thelast panel, where the sample size is smaller. These results indicate that the age compositionof the sample cannot explain the low returns estimated in this context.

Sample with college graduates

Our sample in section VI excludes college graduates due to the reasons discussed earlier.Here, we conduct the same analysis using a sample that includes college graduates. Thisinclusion requires that we place a higher minimum-age restriction so that the treated andnon-treated individuals do not differ markedly in terms of educational distribution. Forthis reason, the sample is restricted to individuals who are 24 years or older. With thisrestriction, the youngest individuals remaining in the sample are born in 1989; thus, we



TAB

LE

7

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mpl

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IV-R

DIV

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mpl

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(A)

1982

–91

0.02

9***

−0.0

20−0

.019

––

92,9

080.

039*

**0.

046

0.05

4–

–30

,163

[0.0

02]

[0.0

14]

[0.0

18]

––

[0.0

03]

[0.0

33]

[0.0

35]

––

(B)

1980

–93

0.03

1***

−0.0

14−0

.013

––

132,

845

0.04

4***

0.06

7***

0.04

7*–

–40

,726

[0.0

02]

[0.0

10]

[0.0

14]

––

[0.0

04]

[0.0

25]

[0.0

27]

––

(C)

1978

–95

0.03

4***

0.00

6−0

.005

−0.0

17–

170,

144

0.04

9***

0.08

9***

0.05

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351

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,120

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[0.0

19]

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(E)

1958

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70.

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426

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156,

725

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cont

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1074 BulletinTA

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1958

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0.06

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460,

058

0.07

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0.08

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0.07

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94,7

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have only three birth cohorts after the cut-off. We define samples (A)–(C) accordingly:sample (A) includes three birth cohorts on both sides of the cut-off (1984–89), sample (B)is expanded to include six birth cohorts before the cut-off (1981–89) and sample (C) isfurther expanded to include nine birth cohorts before the cut-off (1978–89).

The results are given in Table 8 for men and women by the sample and degree ofpolynomial in the running variable. Here, the degree of polynomial is only one with thediscontinuity sample (A), goes up to two with sample (B) and up to three with sample(C). The IV-RD estimates for men are all statistically insignificant. On the other hand, forwomen, there is strong evidence for positive returns to schooling. Moreover, the range ofthe magnitude of the coefficients is similar to those in Tables 4 and 5. Here, the magnitudesof the coefficients are a bit volatile – especially when high-order polynomials are used withshorter time-windows and when low-order polynomials are used with wider time-windows,which is expected. These findings confirm that the exclusion of college graduates in ourprimary sample is not the reason for the low returns to schooling estimates for men or forthe much higher estimates for women.

VIII. Interpretation

In this section, we examine the potential causes of the low estimated returns to schoolingin Turkey and the reasons for the higher estimated returns for women. The low returns toschooling in Turkey might be surprising given that several previous studies report highreturns in developing countries (Patrinos and Psacharopoulos, 2010), including some thatuse plausibly exogenous sources of variation in schooling to estimate the causal link (Duflo,2001). There are two key reasons for the low returns to schooling estimate in our study.

First, for the grade levels at which the policy directly affects individuals (grades 6through 8), the wage–schooling locus is very flat. FigureA1 in theAppendix shows the wagepremium for completing various levels of schooling, calculated by regressing (for men andwomen separately) the logarithm of the wage rate on dummies for educational attainment,age, year and urban status. The sample is restricted to 18- to 26-year-old individuals bornbefore 1986 in order to limit the sample to individuals unaffected by the policy. For men(women), a secondary school diploma increases the wage rate by 6% (6%), compared to14% (21%) for a high-school diploma and 49% (48%) for a college degree (these denotemarginal increases from the lower education category). Obviously, the 6% increase inwages both for men and women resulting from the completion of secondary school isnot the causal effect of three additional years of schooling. Nevertheless, the very lowpremiums from completing secondary school suggest that the causal returns to schoolingmight not be high either. In fact, our findings in subsection ‘Second-stage results withrestrictions on educational attainment’ reveal that with a sample restricted to individualswith less than a high-school degree (where compliers include only those who are inducedto complete grade 8 (secondary school under the old system) with the policy), there is noevidence that returns to schooling are different from zero for either men or women.

Second, when we compare the earnings of the groups with 5 and 8 years of schoolingbefore the policy based on Figure A1, both the productivity effects of three more years ofschooling and the sheepskin effect of earning a secondary school diploma have effects. Onthe other hand, in the policy experiment we examine, the individuals who are induced to


1076 Bulletin

TABLE 8

Robustness check II – returns to schooling estimates with a sample including college graduates

Birth cohorts (1) (2) (3) (4) (5)MenOLS IV-RD IV-RD IV-RD Sample size

(A) 1984–89 0.065*** 0.019 – – 42,502[0.002] [0.044] – –

(B) 1981–89 0.069*** 0.001 −0.030 – 94,319[0.002] [0.032] [0.063] –

(C) 1978–89 0.073*** 0.011 −0.008 −0.029 162,192[0.002] [0.024] [0.044] [0.060]

Degree of polynomial in birth year Third First Second Third

Women

(A) 1984–89 0.090*** 0.066*** – – 16,057[0.003] [0.018] – –

(B) 1981–89 0.095*** 0.052*** 0.095*** – 34,221[0.002] [0.019] [0.010] –

(C) 1978–89 0.099*** 0.029 0.093*** 0.084*** 56,246[0.002] [0.026] [0.016] [0.025]

Degree of polynomial in birth year Third First Second Third

Notes: The dependent variable is log hourly wages. All regressions include controls for years of schooling (which isinstrumented by the policy dummy in columns (2)–(4)), a polynomial in the running variable (year of birth) whoseorder is specified in the last row of the table, age dummies, and a dummy for urban status. All samples are restrictedto inviduals who are 24 or older in the 2002–13 Turkish Labor Force Surveys; therefore, the youngest individual inthe sample is born in 1989. The sample in panel (A) includes three birth cohorts on both sides of the discontinuity(1984–86 and 1987–89), the sample in panel (B) is enlarged to include three more older birth-cohorts, an the sample inpanel (C) includes three more older birth-cohorts than the sample in panel (B). Clustering is done at the year-of-birthlevel. Statistically significant: *** 1% level; ** 5% level, * 10% level.

complete 8 years of schooling with the policy but who would otherwise complete 5 yearshold a primary school diploma both before and after the policy; it is only the years ofschooling that is different for them. Therefore, we measure only the productivity effects ofthree more years of schooling.29

As reviewed earlier, the compulsory schooling reform did not have an obvious negativeimpact on standard measures of schooling quality, such as student-to-teacher, student-to-classroom ratios or international test scores. However, it is important to note that thelow returns to primary and secondary education in Turkey could also reflect the qualityof schooling if school quality was already low before the reform. While school qualityis a potential factor for low returns, for Indonesia, where schooling quality is worse thanthat in Turkey according to international math and science tests,30 Duflo (2001) findsquite high returns to schooling. Moreover, for England and Germany, where the resultsof international tests indicate a better quality of schooling, Devereux and Hart (2010) and

29For only those who are induced to complete 8 years of schooling with the policy but would not finish 5 years of

schooling without it and those who are induced to finish high school with the policy but who would not otherwise,we measure both the productivity and sheepskin effects of schooling. However, since these groups are smaller thanthe former group, we are mostly measuring the productivity effects of additional schooling.

30National Center for Education Statistics (2014), Trends in International Mathematics and Science Study.



Pischke and von Wachter (2008), respectively, find quite low returns. Therefore, ratherthan the quality of schooling in terms of improving the cognitive skills of students, it mightbe the labour market relevance of the skills acquired in the grade levels at which studentschange their behaviour as a result of a particular policy, which determines the returns toschooling, as Pischke and von Wachter (2008) argue.

Our other key finding is that returns to schooling are higher for women than for men.A potential reason for the higher estimated returns in Turkey for women is that since thefemale labour-force participation rate in Turkey is much lower, women in the labour marketform a much more select group in terms of average ability conditional on years of schoolingthan men in the labour market. Nonetheless, an investigation of the characteristics of thecompliers among men and women gives us another strong argument as to why there aregender differences in returns to schooling in Turkey.

The difference in the estimated average causal effects between men and women couldresult from differential weighting of the causal effects conditional on years of schooling.As shown earlier, the policy increases the completion of not only grade 8 but also highschool. Moreover, as displayed in Figure 3, the rise in the fraction completing high schoolor a higher schooling level compared to the rise in the fraction completing grade 8 or ahigher schooling level is much higher among women than men. In other words, a muchlarger fraction of female compliers complete high-school grade levels. At the same time,our findings on the returns to schooling with restrictions on educational attainment insubsection ‘Second-stage results with restrictions on educational attainment’ suggest thatthe returns to an extra year in high school are higher than the average returns to an extrayear in primary school. In essence, returns to schooling are higher for high-school gradelevels than for earlier grade levels and the female compliers include a higher share of thosewho complete high-school grade levels, resulting in a higher returns to schooling estimatefor women in our sample.

IX. Conclusion

In this paper, we estimate the causal wage returns to schooling for young men and womenin Turkey and thus contribute to the small body of literature on the causal monetary returnsof education in developing countries. For this purpose, we use the exogenous variationin schooling brought about by the 1997 reform in compulsory schooling within a fuzzyregression-discontinuity design. The features of this reform make it very close to beingan ideal instrument. The reform brings about a tremendous change in schooling outcomesbecause of both the length of the extension and the high fraction of students who drop outafter completing compulsory education.

Our empirical analysis reveals that the return to an extra year of schooling is about2–2.5% for men – but this is statistically insignificant – whereas it is about 7–8% forwomen and highly statistically significant. An important feature of these local averagetreatment effect estimates is that they come close to the average treatment effect estimatesbecause the policy affects the schooling outcomes of a large section of the population.

Our estimates of returns to schooling are relatively low for two primary reasons. First, inthe grade levels at which the policy changes the schooling distribution, returns to schoolingare in fact low. Our analysis shows that in grades 6 through 8, there is no evidence that returns


1078 Bulletin

to schooling are different from zero for either men or women; however, they are higher forthe high-school grade levels, particularly for women. Second, while the policy mandatesthree more years of schooling, a new diploma is not awarded for its completion. Therefore,there are no new sheepskin effects; only the productivity effects of extra schooling are ineffect.

An important reason for the higher returns to schooling for women than for men in ourcontext is that the policy changes the schooling distributions of men and women differently.Our estimate, which is an average of the causal returns at different grade levels, puts moreweight on high-school grade levels for women than for men, and the returns to an extrayear of schooling in high school are higher than the returns to an extra year in primaryeducation. In other words, female compliers are more likely to come from those whoare induced to finish high school with the policy. This is because women’s employmentprobability increases substantially with education. Thus, the women in our sample of wageearners have higher education on average than the men in our sample.

In our analysis, conditional on schooling attainment, women are a more select groupbecause of the much lower employment rate for women than for men in Turkey. Thiswould be another reason for the higher returns to schooling for women if selection intoemployment is associated with ability. This issue also highlights a potential limitation ofour estimate for women: we estimate the returns to schooling for a select group who arewage earners. However, this group is actually relevant for our purpose even though it is aselect group because the women who are on the margin of becoming wage earners would besimilar to the women in our sample. Another potential contaminating factor in our returnsto schooling estimate for women is that the policy also increases the probability of wageemployment among women. This would be problematic if the women who become wageearners with the policy are different from those who are already wage earners in waysrelated to their earnings potential. However, again, since the new entrants to employmentwith the policy were on the margin of employment before the policy, they are not likelyto be substantially different from those who were already employed before the policy interms of earnings potential.



Appendix

Figure A1. Wage-schooling locus by genderNotes: The data include 18- to 26-year-old fulltime wage earners who were born before 1986 (i.e. those whowere not affected by the policy).

0

.5

1

1.5

2

2.5

18 26 34 42 50 18 26 34 42 50

Male Female

Illiterate Literate, No DegreePrimary School Secondary SchoolHigh School University

Log

Hou

rly W

age

Age

Figure A2. Age profile of hourly wages by genderNotes: The data include fulltime wage earners who were born before 1986 (i.e. those who were not affected bythe policy).


1080 Bulletin

.75

.8

.85

.9

.95

1

No

obs.

with

out c

olle

ge g

radu

ates

/N

o ob

s. w

ith c

olle

ge g

radu

ates

78 79 80 81 82 83 84 85 86 87 88 89 90 91 92 93 94 95

Year of Birth (19xx)

Figure A3. College graduation and potential manipulation of the running variable

0.1

.2.3

.4

Frac

tion

0 5 10 15 20

education in single years

Figure A4. Distribution of years of schooling (Source: 2008 DHS data)



TABLE A1

Robustness of policy effect on college degree to alternative methods of standard-error estimation

Gender Men Women WomenSample Sample E Sample A Sample EDegree of polynomial in birth year Third Linear Third

(1) (2) (3)

(A) Estimates with different ways of calculating the standard errors(1) White heteroskedasticity-robust SE 0.009*** 0.018*** 0.015***

[0.003] [0.003] [0.003](2) Cluster-robust SE 0.009* 0.018* 0.015*

[0.005] [0.009] [0.008](3) Moulton-factor adjusted SE 0.009 0.018** 0.015*

[0.006] [0.007] [0.006]

Observations 1,109,855 214,211 1,189,784

(B) P-values with different rejection methods1) Cluster on birth-year, T(G-2) for

critical value0.080 0.072 0.053

2) Wild cluster bootstrap: Liu r.v.,symmetric test

0.121 0.157 0.106

3) Wild cluster bootstrap: Rademacherr.v., symmetric test

0.115 0.259 0.132

4) Wild cluster bootstrap: Mammen r.v.,symmetric test

0.135 0.227 0.145

5) Wild cluster bootstrap: Liu r.v.,equaltailed test

Reject at 10% Fail to reject at 10% Reject at 10%

6) Wild cluster bootstrap: Rademacherr.v., equaltailed test

Fail to reject at 10% Fail to reject at 10% Fail to reject at 10%

7) Wild cluster bootstrap: Mammen r.v.,equaltailed test

Reject at 10% Fail to reject at 10% Reject at 10%

Notes: The dependent variable is college graduation status. All regressions include controls for the policy dummy, apolynomial in the running variable (year of birth) whose order is specified in the top of each column, age dummies,and a dummy for urban status.All samples are restricted to inviduals who are 22 or older in the 2002–13 Turkish LaborForce Surveys; therefore, the youngest individual in the sample is born in 1991. In panel (A2), clustering is done atthe birth-year level. The number of clusters (G) is 28 in column (2), but 38 in columns (1) and (3). In cluster-robuststandard errors in panel (A2), Stata calculates p values using T(G-l) degrees of freedom with the ‘regress’ command.Statistically significant: *** 1% level; ** 5% level, * 10% level.


1082 Bulletin

TAB

LE

A2

Rob

ustn

ess

ofin

stru

men

tal-

vari

able

regr

essi

on-d

isco

ntin

uity

estim

ates

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tern

ativ

em

etho

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ion

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ple

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ple

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ple

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ree

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arF

irst

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ndF

irst

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ndF

irst

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nd(1

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imat

esw

ithdi

ffer

entw

ays

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lcul

atin

gth

est

anda

rder

rors

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hite

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ticity

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024*

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lust

er-r

obus

tSE

0.02

0**

0.02

4**

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7**

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3***

0.02

6***

0.02

2*[0

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1][0

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1]

Obs

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tions

B)

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sw

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tion

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034

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12)

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ster

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10.

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3)W

ildcl

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poly

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nth

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gva

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ear

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rth)

who

seor

der

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edin

the

top

ofea

chco

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edu

mm

ies,

and

adu

mm

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ban

stat

us.A

llsa

mpl

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ere

stri

cted

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als

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).St

atis

tical

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**5%

leve

l,*

10%

leve

l.



TAB

LE

A3

Rob

ustn

ess

ofin

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men

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vari

able

regr

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rror

estim

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n

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ple

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ple

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ple

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mpl

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ple

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mpl

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ree

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lyno

mia

lin

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irst

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cond

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d(1

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(A)

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imat

esw

ithdi

ffer

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ays

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lcul

atin

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hite

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ticity

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lust

er-r

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0.05

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3**

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0.06

5***

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7***

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0**

[0.0

26]

[0.0

26]

[0.0

21]

[0.0

22]

[0.0

23]

[0.0

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(3)

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*[0

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][0

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]B

)P

-val

ues

with

diff

eren

trej

ectio

nm

etho

ds1)

Clu

ster

onbi

rth-

year

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-l)

for

criti

calv

alue

0.05

60.

040

0.00

40.

012

0.00

30.

031

2)C

lust

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rcr

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004

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30.

004

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23)

Wild

clus

ter

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p:L

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mm

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008

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90.

020

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54)

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ter

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p:R

adem

ache

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.,sy

mm

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169

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60.

037

0.08

15)

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clus

ter

boot

stra

p:M

amm

enr.v

.,sy

mm

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cte

st0.

128

0.17

10.

013

0.09

50.

048

0.09

66)

Wild

clus

ter

boot

stra

p:L

iur.v

.,eq

ualta

iled

test

Rej

ecta

t10%

Rej

ecta

t10%

Rej

ecta

t1%

Rej

ecta

t5%

Rej

ecta

t1%

Rej

ecta

t10%

7)W

ildcl

uste

rbo

otst

rap:

Rad

emac

her

r.v.,

equa

ltaile

dte

stFa

ilto

reje

ctat

10%

Fail

tore

ject

at10

%R

ejec

tat5

%R

ejec

tat1

0%R

ejec

tat5

%R

ejec

tat1

0%8)

Wild

clus

ter

boot

stra

p:M

amm

enr.v

.,eq

ualta

iled

test

Rej

ecta

t10%

Rej

ecta

t10%

Rej

ecta

t1%

Rej

ecta

t5%

Rej

ecta

t5%

Rej

ecta

t5%

Not

es:T

hede

pend

entv

aria

ble

islo

gho

urly

wag

es.A

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sin

clud

eco

ntro

lsfo

rye

ars

ofsc

hool

ing

(whi

chis

inst

rum

ente

dby

the

polic

ydu

mm

y),a

poly

nom

iali

nth

eru

nnin

gva

riab

le(y

ear

ofbi

rth)

who

seor

der

issp

ecifi

edin

the

top

ofea

chco

lum

n,ag

edu

mm

ies,

and

adu

mm

yfo

rur

ban

stat

us.A

llsa

mpl

esar

ere

stri

cted

toin

vidu

als

who

are

18or

olde

ran

dw

hoha

vean

educ

atio

nala

ttain

men

tbel

owco

llege

degr

eein

the

2002

–13

Turk

ish

Lab

orFo

rce

Surv

eys.

Inpa

nel(

A2)

,clu

ster

ing

isdo

neat

the

birt

h-ye

arle

vel.h

enu

mbe

rof

clus

ters

(G)

is10

with

sam

ple

(A),

14w

ithsa

mpl

e(B

),an

d18

with

sam

ple

(C).

Stat

istic

ally

sign

ifica

nt:*

**1%

leve

l;**

5%le

vel,

*10

%le

vel.


1084 Bulletin

TABLE A4

Instrumental variable difference-in-differences estimates

Birth cohorts (1) (2) (3) (4) (5) (6)Men Women

OLS IV-DID Sample size OLS IV-DID Sample size

(A) 1982–91 0.027*** 0.017** 107,089 0.035*** 0.058* 36,439[0.002] [0.008] [0.003] [0.031]

(B) 1980–93 0.029*** 0.008 150,905 0.040*** 0.072*** 48,346[0.002] [0.006] [0.004] [0.028]

(C) 1978–95 0.032*** 0.020** 191,162 0.045*** 0.090*** 57,714[0.002] [0.010] [0.005] [0.023]

(D) Ages 18–26 0.027*** 0.014* 116,933 0.036*** 0.071*** 41,665[0.002] [0.007] [0.003] [0.026]

Notes: The dependent variable is log hourly wages. All regressions include controls for years of schooling (which isinstrumented by the policy dummy in columns (2) and (5)), age dummies, year dummies, and a dummy for urbanstatus. All samples are restricted to inviduals who are 18 or older and who have an educational attainment belowcollege degree in the 2002–13 Turkish Labor Force Surveys; therefore, the youngest individual in the sample isborn in 1995. The sample in panel (A) includes five birth cohorts on both sides of the discontinuity (1982–86 and1987–91), the sample in panel (B) includes seven birth cohorts on both sides (1980–86 and 1987–93), and the samplein panel (C) includes nine birth cohorts on both sides (1978–86 and 1987–95). The sample in panel (D) is restrictedto individuals aged 18–26. Clustering is done at the year-of-birth level. Statistically significant: *** 1% level; ** 5%level, * 10% level.

Final Manuscript Received: November 2016

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LowWageReturnstoSchoolinginaDeveloping Country ...faculty.smu.edu/millimet/classes/eco7377/papers/aydemir kirdar 201… · school level (grades 6–8) was 52.8%.2 Thus, the 1997 reform