metadata: authors: 0: author: Li,Tianshu
1: author: Sekhri,Sheetal
count: India
docna: 0: docna: The Spillovers of Employment Guarantee
            Programs on Child Labor and Education
docty: Policy Research Working Paper
subtopic: Education Finance,Economics of Education,Educational Sciences,Labor Markets,Child Labor Law,Labor Standards,Rural Labor Markets,Child Labor,Educational Institutions & Facilities,Effective Schools and Teachers
teratopic: Law and Development,Education,Social Protections and Labor,Rural Development
abstracts: cdata!: Many developing countries use employment
            guarantee programs to combat poverty. This paper examines
            the consequences of such employment guarantee programs for
            the human capital accumulation of children. It exploits the
            phased roll-out of India's flagship Mahatma Gandhi
            National Rural Employment Guarantee Scheme (MGNREGA) to
            study the effects on enrollment in schools and child labor.
            Introduction of MGNREGA results in lower relative school
            enrollment in treated districts. The authors find that the
            drop in enrollment is driven by primary school children.
            Children in higher grades are just as likely to attend
            school under MGNREGA, but their school performance
            deteriorates. Using nationally representative employment
            data, they find evidence indicating an increase in child
            labor highlighting the unintentional perverse effects of the
            employment guarantee schemes for Human capital.
geo_reg_key: 517198,517191,517212
repnme: repnme: The Spillovers of Employment Guarantee
            Programs on Child Labor and Education
display_title: The Spillovers of Employment
            Guarantee Programs on Child Labor and Education
listing_relative_url: /research/2020/01/31686540/spillovers-employment-guarantee-programs-child-labor-education
topicv3: Child Labor m1326042 1859,Teachers Management m1326119 1523,Education m1327048 470,Private Education m1327271 1490,Population, Aging and Health m1327736 640
publishtoextweb_dt: 2020-01-07T00:00:00Z
historic_topic: Law and Development,Education,Social Protections and Labor,Rural Development
origu: DEC-Knowledge and Strategy (DECKS)
no_of_pages: 39
author_keys: 0: author_key: 1209340
1: author_key: 1345256
model_extractions: Policy Research Working Paper 9106 The Spillovers of Employment Guarantee Programs on Child Labor and Education _Tianshu Li Sheetal Sekhri_ Development Economics Knowledge and Strategy Team January 2020
Policy Research Working Paper 9106

# **Abstract**

Many developing countries use employment guarantee programs to combat poverty. This paper examines the consequences of such employment guarantee programs for the human capital accumulation of children. It exploits the phased roll-out of India’s flagship Mahatma Gandhi National Rural Employment Guarantee Scheme (MGNREGA) to study the effects on enrollment in schools and child labor. Introduction of MGNREGA results in lower relative school enrollment in treated districts. The authors find that the drop in enrollment is driven by primary school children. Children in higher grades are just as likely to attend school under MGNREGA, but their school performance deteriorates. Using nationally representative employment data, they find evidence indicating an increase in child labor highlighting the unintentional perverse effects of the employment guarantee schemes for Human capital.

This paper is a product of the Knowledge and Strategy Team, Development Economics. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://www.worldbank.org/prwp. The authors may be contacted at ssekhri@virginia.edu.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
The Spillovers of Employment Guarantee Programs on Child Labor and Education Tianshu Li and Sheetal Sekhri<sup>_∗_</sup>

# **1 Introduction**

Both developed and developing countries use employment guarantee programs as a safety net mechanism to reduce poverty and economic vulnerability.<sup>1</sup> This paper uses the temporal and spatial variation in the roll-out of the Indian government’s 2005 National Rural Employment Guarantee Act (NREGA, now named MGNREGA) to evaluate the impact of the policy on children’s educational and employment outcomes. Several studies have shown that MGNREGA increased the demand for labor and increased rural wages (Imbert and Papp, 2015; Zimmerman, 2012). In light of this, the scheme can have profound effects on childrens education and employment as it influences the opportunity cost of schooling. Potentially, the value of childrens time both in the labor force and at home can increase.

> _<u>∗</u>_ Sheetal Sekhri (corresponding author) is an associate professor at the University of Virginia, Charlottesville; her email is ssekhri@virginia.edu. Tianshu Li is an assistant professor at the Institute of Urban Development of Nanjing Audit University; his email address is tl4bz@virginia.edu. The authors thank Leora Friedberg, Kartini Shastry, and Heidi Schramm for insightful comments. A supplemental appendix is available with this article at the World Bank Economic Review website.

> 1The earliest experiments with this policy lever date back to the 1817 Poor Employment Act and the 1834 Poor Law Amendment Act in Great Britain (Blaug, 1963, 1964), and the New Deal program of the 1930s in the United States (Kesselman, 1978; Bernstein, 1968). More recently Chile in 1987, India in 1978 and 2001, Pakistan in 1992, Bangladesh in 1983, Philippines in 1990, Botswana in 1960, and Kenya in 1992 have implemented variants of employment guarantee schemes. See Mukherjee and Sinha (2013) for details.
A number of factors make India’s flagship MGNREGA program an ideal setting to study the impact of employment guarantee schemes on schooling and child labor. First, the scale of the program is massive. By its fifth year, the program provided employment opportunities to 53 million households for 2.3 billion man-days, making it the world’s largest operating employment guarantee scheme. Second, the program was gradually rolled out in the districts of India based on pre-determined characteristics measured 10-15 years prior to the program. This variation provides an excellent opportunity to evaluate the impact of this program.

Using a longitudinal data set of 1.13 million primary and upper-primary schools in India, the study compares within school enrollment across the districts which received the program early versus late. We find that, conditional on school characteristics, school enrollment grew more slowly in districts where the program was phased in early. This result is driven by primary schools rather than upper primary schools. Using nationally representative survey data, we examine the effect on children’s employment both outside and within the house. We find that children are more likely to be employed in early phase districts post treatment.<sup>2</sup> Responses to the program are heterogeneous. Responses to the program vary by age, type of school and quality of private schools within private schools. Enrollment falls for younger primary school children whereas school outcomes deteriorate for upper primary children. Grade 7 school outcomes in early treated districts get worse for both government and private schools but effects are larger for private schools. Within private schools, the effects are driven by low quality private schools.

The timing of the roll-out was not random and was largely ascertained by three district characteristics: district Scheduled Castes and Scheduled Tribes population in the 1991 Census of India, 1996-97 agricultural wages, and the 1990-1993 output per 2In many settings, children who work a significant number of days in a year are less likely to be enrolled in school (Jensen, 2000). Our results show that safety net schemes can result in an increase in this phenomenon.

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agricultural worker. We control these characteristics in our analysis. We also include both school and year fixed effects to control for school-specific time-invariant heterogeneity, and macro trends in enrollment. We also include state time trends to control for state-specific funding decisions that may affect school enrollment or performance. Additionally, we include a very comprehensive set of school- and district-level controls in our empirical analysis. Finally, we control for school-type by year fixed effects to allow for differential enrollment trends in government and private schools.

To further bolster the confidence in our identification, we conduct a series of robustness tests. First , using the data for three years before the policy was implemented (2003-2005) for a large subsample of the states,<sup>3</sup> we compare the pre-trends in the districts that received the program early to the ones that received it late. We do not see any evidence of differential pre-trends in enrollment. Second, using this sample, we demonstrate that controlling for changes in yearly enrollment from 2003 to 2005 and allowing the trend to vary over time in subsequent years does not change our results. Note that we also show that results are similar in the full sample and in the subsample for which we have pre-treatment data to rule out bias emerging from selection into the sample. Finally, we demonstrate that the timing of the change in enrollment coincides with the introduction of MGNREGA in early districts.

Our paper contributes to two strands of literature. The first strand examines the causal effects of employment guarantee schemes and other safety net programs on development outcomes. Several other studies have evaluated safety net programs, and in particular, this program.<sup>4</sup> Previous evaluations have shown that MGNREGA increased unskilled wages (Imbert and Papp, 2015; Azam, 2012; Berg et al, 2012; Zimmermann,

> 3Only 10 states and union territories covering a very small fraction of rural India are excluded in the pre-trend comparison.

> 4See Skoufias and Parker (2003) for an in-depth analysis of the effects of Mexico’s Progresa on child outcomes and Skoufias et al. (2001) for effects of Progresa on child labor and schooling outcomes. Progresa is a conditional cash transfer program where transfers to the households were conditioned on children attending school. So the incentives households face are very different from MGNREGA. Berhane et al. (2014) study the effects of safety net schemes on food security and economic vulnerability.

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2012), female labor force participation (Azam, 2012) and household consumption (Ravi and Engler, 2015). We complement this literature and examine the effects of the program on schooling outcomes. Our paper does not refute these clear benefits of the program but rather shows that there is an opportunity cost.

There are two studies that are closely related to our paper. Afridi et al (2012) find that MNREGA increases mothers income and through this channel improves childrens educational outcomes. Unlike Afridi et al (2012), we do not find an improvement in schooling outcomes. There are a number of differences between our paper and their study. First, Afridi et al (2012) focus on one state, whereas we use data from the entire country from 2005 to 2008. Hence, our design allows us to understand nation wide effects of the program. Second, they use data from 2007 to 2009. By 2007, MGNREGA was already implemented in the poorest parts of the country, and was being implemented in the rest of the districts. Hence, their study only makes post introduction comparisons and uses the intensity of exposure for identification. In contrast, the strength of this study design is that it uses the roll-out timing for identification and compare outcomes pre- and post-implementation. We also examine a very rich set of schooling outcomes, whereas they focus on time spent in school. Importantly, we show that the program has an unintended effect on child labor increasing likelihood of being employed. In a subsequent study, Shah and Steinberg (2015) use test score data and evaluate the impact of MGNREGA on human capital. Their paper reinforces our findings. However, there are important dissimilarities. Their study uses the Annual Status of Education Report (ASER) data on test scores<sup>5</sup> and finds that test scores worsen for children in early roll-out districts. They focus on gender based age specific differences in labor outcomes. Our study, on the other hand, uses school level data and highlights the heterogeneity in outcomes by school type, quality of private schools and age. There are two major differences that underscore the contributions of our paper. First, a novel result

> 5This data is collated by an NGO Pratham and is publicly available.

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in our paper shows that the enrollment falls in private schools which are expensive rather than in the public schools and there is heterogeneity even within private schools. Low quality schools drive the fall in enrollment in private schools. Second, from identification perspective, a clear advantage of our paper is that we have three years of pre-treatment data for a large subset of our schools. Thus, we can strengthen the confidence in our findings by demonstrating that there are no differential pre-trends. However, their study design is limited by only 1 year of pre-treatment data in the ASER sample.<sup>6</sup> Finally, our paper also complements the literature on child labor.<sup>7</sup> Basu and Van (1998) provide a theoretical model that examines conditions under which children work in the labor market. Edmonds (2005) uses data from Vietnam to examine whether improving standards of living reduces child labor. Edmonds and Pavnick (2005) examine the effect of international trade on children’s outcomes. Jacoby and Skoufias (1997) study the effects of financial market incompleteness on human capital accumulation and document that seasonal fluctuation in school attendance is a form of self-insurance by households. More recently Cascio and Narayan (2015) demonstrate that economic booms resulting from increased fracking in the US increase high school dropout rates due to an increase in the demand for unskilled labor. We contribute to this literature by examining the effects of employment guarantee schemes on child labor. Program induced increased labor opportunities for adults induce an increase in child labor.

Our findings have important policy implications: without adequate changes in incentives to attend school, large scale safety net programs designed to smooth household consumption may result in decreased school enrollment and worsening of performance in schools.

The rest of the paper is organized as follows: In Section 2, we offer more detailed information on the MGNREGA in India. Section 3 presents the data used, and Section

> 6Both these studies use the National Sample Survey Office (NSSO) employment and unemployment survey data to substantiate that the program indeed results in higher labor supply of children.

> 7See Basu (1999) for a review of this literature.

5
4 presents the empirical strategy. Section 5 documents the results. Section 6 offers concluding remarks.

# **2 Contextual Information**

## **2.1 Background-National Rural Employment Guarantee Act**

The National Rural Employment Guarantee Act, passed in 2005 (now called Mahatma Gandhi National Rural Employment Guarantee Act), provides 100 days of guaranteed wage employment per financial year to every individual residing in rural India. The program provides unskilled manual work at the officially determined minimum wage of about 2 USD per day. In any district covered by the program, an adult can apply for work under MGNREGA and is entitled to public works employment works within 15 days; otherwise, the state government provides an unemployment allowance (Ministry of Rural Development, 2008b).<sup>8</sup> This program has been widely claimed to have increased rural wages despite significant leakages from the program. Imbert and Papp (2015) claim that despite its shortcomings, the program is effective at attracting casual labor relative to the private sector.

The budget for the program is almost 4 billion USD, 2.3 percent of total central government spending, which makes the program the best funded anti-poverty program in India (Ministry of Rural Development, 2008a; Azam, 2012). The program provided 2.27 billions person-days of employment to 53 millions households in 2010-11 with the whole budget in the country Rs. 345 billions (7.64 billions USD); representing 0.6% of the GDP (Imbert and Papp, 2015).

> 8We discuss some additional program details in the supplementary online appendix, available with this article at the World Bank Economic Review website - Section MGNREGA Implementation Details.

6
## **2.2 Roll-out of the MGNREGA Program**

MGNREGA was implemented in three phases. Backwardness status of the districts was used to determine roll-out priority. However, each state was provided representation in Phase I. The Planning Commission of India calculated and ranked the backward status of Indian districts (Planning Commission, 2003). The official ranking of backwardness of the districts in each state was based on the Scheduled Castes and Scheduled Tribes population in 1991, agricultural wages in 1996-97, and output per agricultural worker in 1990-93. In Phase I, 200 backward districts implemented the program in February 2006. The program was then introduced in additional 130 districts in Phase II in April 2007,<sup>9</sup> and all the remaining 270 districts received the program in the last phase in April 2008.<sup>10</sup> This variation in the timing of the program roll-out enables us to identify the causal effect of this scheme on schooling outcomes.<sup>11</sup>

# **3 Data**

The principal source of data is the annual panel of Indian schools called the District Information System for Education (DISE).<sup>12</sup> The data covers grades 1 through 8 in 1.13 million schools. School characteristics include: staff characteristics such as gender and qualification of teachers, infrastructure measures including availability of common toilets, gender specific toilets, drinking water facilities, and electrification, and enrollment by gender and grade. The data also include appearance and pass rates for school ex-

> 9The program commenced in May 2007 for 17 Phase II districts in Uttar Pradesh due to state legislative assembly elections

> 10Due to splitting of districts for which data for the parent and split district was not available in all years, the number of districts in our sample are 193, 123, and 254, respectively.

> 11Prior to February 2006, the government experimented with a pilot program (the Food for Work Program) in November 2004 in 150 of the 200 Phase I districts. Field observations (Bhatia and Dreze, 2006) and research studies (Imbert and Papp, 2015) have found little evidence of increase in public works due to this pilot.

> 12DISE is collected every year in a joint collaboration between the Government of India, UNICEF, and the National University of Educational Planning and Administration (NUEPA). The data is publicly available from NEUPA.

7
aminations for grades 5 and 7 and grade repetition for all grades. Primary schools in India may have only primary classes (grades 1 through 5), only upper-primary classes (grade 6 through 8), or both (grade 1 through 8). The data provide information about whether the school offers only primary classes, only upper-primary classes, or both. The school management categories in the data include (1) Department of Education, (2) Tribal/Social Welfare Department, (3) Local body, (4) Private Aided, (5) Private U- naided, (6) Others, and (7) Un-recognized. We construct three aggregate categories - government run schools (1 and 2), private schools (4 and 5) and others (3 , 6, and 7). In addition to these features, the data report ongoing incentive schemes in various schools to increase enrollment. Various schemes running in schools before MGNREGA provide free uniforms, textbooks, stationery, and attendance fellowships. One concern with the DISE data is that since schools self-report the data, there is measurement error in the data.<sup>13</sup> We address the implications of measurement error in the data for our results in subsequent sections.

The district level characteristics are from the Census of India 1991 and 2001. These include total population, population growth rate, percentage of female population, literacy rate, female literacy rate, percentage of the Scheduled Castes and Scheduled Tribes population, and percentage of working population. Agricultural wages for 1996-97 and total output per agricultural worker for 1990-93 come from the Planning Commission’s 2003 report.

Table 1 provides the summary statistics of outcome variables by phases of MGNREGA districts. Consistent with the roll-out criterion, the better-off Phase III districts have better educational outcomes. Conditional on being enrolled, 92 percent of the children pass exams in grade 5 in Phase III districts, whereas 88 percent do in Phase I districts.

> 13These data are collected using a district level administrative structure. School principals fill a standardized survey about the school. The data are manually checked at various levels for completeness, accuracy, and inconsistencies. States also implement checks. NEUPA has commissioned an external audit of the school data. These audits check 5 percent of the schools chosen randomly from at least 10 percent of the districts from each state. The auditors also visit the schools. These audits have established that the enrollment data reported by the principals are remarkably accurate.

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In Phase III districts, 49 percent of students enrolled score more than 60 percent marks in grade 5 examinations, whereas in Phase I districts only 38 percent do. Similarly, these percentages for grade 7 examinations are 43 percent in Phase III districts and 36 percent in Phase I districts. Additional summary statistics about the schools and districts in different phases are presented in Appendix Tables S1 and S2 and the details are discussed in the online Supplemental Appendix.

# **4 Empirical Strategy**

We use the timing of roll-out of the MGNREGA program across districts of India for identification. Phase I districts received the program in February 2006, Phase II in April/May 2007, and Phase III in April 2008. We use 2005 as the baseline year and include data from 2005-2008 in our analysis. Later we use data from 2003 for the districts we have it for to provide support to our identifying assumption.

## **4.1 Roll-out and Selection**

The timing of the roll-out of the program was not randomly determined. Thus, a simple comparison of the districts across different phases is not likely to generate causal estimates of the program. In order to circumvent this issue, we compare outcomes within districts that received program in different phases over time. This allows us to control for time invariant differences in unobserved characteristics of districts that received the program in different phases. We also use within-school variation for identification by including school fixed effects to purge any time invariant school level characteristics that may be correlated with the treatment.

We further interact the three variables determining selection into the phase of roll-out with year indicators to control for trends in these variables. In addition, we include a rich set of district specific controls including: 2001 levels of total population, percentage 9
of rural population, population growth rate, overall literacy rate and female literacy rate interacted with year indicators. We also control for a state-specific time trend to control for state specific time-varying unobserved heterogeneity, such as discretionary state-level education funding. We allow for a differential trend for government and private schools over time by interacting school type with year indicators.

Our identifying assumption is that the outcomes in districts that received the program in different phases are not trending differentially prior to treatment after controlling for trending program criteria. We test this assumption on a sub-sample of states for which we have pre-treatment data. We show that growth in school enrollment in districts that received the program in different phases is similar prior to the program. We also show that the within-school results are invariant to including changes in enrollment from 2003 to 2005. We do not have data from 2003-2005 for 10 small states and union territories. We verify that excluding these 10 states in our empirical analysis does not influence the results to rule out selection into the sample.

# **4.2 Estimation Procedure**

We use school level data from 1.13 million schools from 2005 to 2008 to test our hypotheses. Our empirical specification is as follows: _Yidst_ = _α_ 0+ _α_ 1 _MGNREGAdt_ + _α_ 2 _Xidst_ + _α_ 3 _Zds∗Tt_ + _α_ 4 _States∗trend_ + _Tt_ + _Iids_ + _εidst_ (1) where _Yidst_ is the outcome variable for school _i_ in district _d_ in state _s_ in year _t_ . _MGNREGAdt_ is an indicator that takes value 1 if district _d_ in state _s_ has started the MGNREGA program in year _t_ , and 0 otherwise; _Xidst_ is a vector of school level controls including different kinds of incentives received by the students, and the characteristics of the teachers and infrastructure of the school _i_ in district _d_ in state _s_ in year _t_ ; _Zds_ is a vector of district-level controls for demographic characteristics, and these are interacted with year indicators 10
to control for trends in these characteristics starting at specific levels for which we have values; _States_ is a vector of state indicators, and is interacted with a linear time _trend_ to control for state-specific trends and account for state spending priorities; _Tt_ and _Iids_ are year- and school-fixed effects, respectively, and _εidst_ is the idiosyncratic error term. We drop the MGNREGA phase indicators due to multi-collinearity in our school fixed effects model. We cluster errors at the district level to account for arbitrary correlation over time.

In order to examine the school choices by school type, we interact the introduction of MGNREGA with the type of school. The empirical model is as follows: _Yidst_ = _β_ 0 + _β_ 1 _MGNREGAdt_ + _β_ 2 _Pids ∗ MGNREGAdt_ + _β_ 3 _Gids ∗ MGNREGAdt_ + _β_ 4 _Xidst_ + _β_ 5 _Zds ∗ Tt_ + _β_ 6 _States ∗ trend_ + _β_ 7 _Schooltypei ∗ Tt_ + _Tt_ + _Iids_ + _εidst_ where _Yidst_ is the outcome variable for school _i_ in district _d_ in state _s_ in year _t_ . _Pids_ is an indicator equal to 1 for private schools and 0 otherwise and _Gids_ is an indicator which takes value 1 for government schools and 0 otherwise. The omitted category is others. We include the the interaction of the MGNREGA policy indicator with each of these type indicators to examine whether effects of the program differ by school type. _Schooltypei_ are indicators for government and private schools, and these are interacted with year indicators to control for differential trends in different types of schools. Note that once we include the school fixed effects, indicators for school type (private and government) are not included as these are time invariant properties of schools. As before, we also drop the phase indicators due to multi-collinearity in the school fixed effects model.

The outcomes we examine are: enrollment, pass rate, pass rate conditional on taking the exams, pass rate of those who pass with more than 60 percent marks.<sup>14</sup> Note that we do not have age specific population data so we are unable to normalize our results

> 14In India, more than 60 percent marks are considered first division.

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by this age-specific population. Instead, we control for trends in district-specific total population.<sup>15</sup> There are three concerns that may confound the interpretation of our results. First, we may be spuriously attributing to MGNREGA the effects of other government programs aimed at influencing enrollment. The Government of India introduced two programs in the early 2000s to promote direct enrollment in schools. The first program, the Sarva Shiksha Abhiyan (SSA), was intended to provide universal access to elementary education. The second program was the Mid-day meal which provided cooked meals for children in attendance at schools. However, both programs were launched much earlier than the MGNREGA. The second concern might be that the increase in private schools driven by growth in the private school market, independent of the program, affects our results. We see significant declines in the enrollment in the private schools. Hence, an increase in number of schools cannot be causing this decline. Further, our estimates are robust to including state- specific trends, and school type by year fixed effects. Therefore, different trajectories of growth across states is not generating our results. In Appendix Figure S1 (in the supplementary online appendix, available with this article at the World Bank Economic Review website), we also show that phase wise trends in expansion of schools both for private and public schools were similar. Thus, an independent increase in demand for private schools is unlikely to be driving our results.

Finally, if MGNREGA attracts migrants into districts, then the results could be driven by changes in population. Across district migration in India is very low (Topolova, 2010). Further, if migration were responsible for the changes in enrollment, then we would expect similar sized effects for primary and upper primary grades and individual classes within these grades. In Tables 2 and 3, the size of the effect is much larger in primary school with no effect discerned in upper primary school. It seems implausible that households with children only in specific age groups would migrate into the MGNREGA

> 15We also get similar results using log specifications.

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districts to work.<sup>16</sup>

# **5 Results**

## **5.1 Overall Enrollment**

In order to evaluate the effect of MGNREGA on enrollment, we estimate equation 1 and present the results in Table 2. Column (i) presents the basic difference-in-difference specification with school and year fixed effects. This result is robust to controlling for state specific time trends as reported in Column (ii). Both specifications control for district level controls that influenced the roll-out timing. The study controls for the Scheduled Castes and Scheduled Tribes population from the Census of India 1991, agricultural wage in 199697, and output per agricultural worker in 199093, interacted with time indicators. This accounts for differential trends in districts with the backward district status that influenced selection into the program. In addition, we control for trends in districts level total population, percentage of urban population, population growth rate, overall literacy rate, and women’s literacy rate in a similar manner.<sup>17</sup> The school-level controls include any attendance scholarships being offered at the time, uniform, books, stationery and other such subsidies offered to girls, the number of classrooms, the number of classrooms in good condition, availability of common toilets, girls toilets, drinking water facilities, electrification status, number of male teachers, and number of female teachers.

The coefficient in Columns (i) and (ii) is -2.23 and is statistically significant at the 5 percent level. Overall, enrollment in this period is increasing and thus this coefficient indicates that introduction of MGNREGA results in a smaller annual increase in school

> 16Also, anecdotal evidence suggests that beneficiaries use the employment guarantee in summer months. One concern might be that schools are already closed for vacation. However, schools in India generally close for only around 40 days and the timing varies spatially ranging from mid-May to end of June in North to mid-June to end-July in the South. Also, Imbert and Papp (2015) show that the program impacts rural wages in a general equilibrium framework. Given that, there is an incentive to substitute for adult labor year round.

> 17We observe that the effects are no different if we do not include these co-variates.

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enrollment in treated districts. Hence, implementation of MGNREGA results in relative slower growth in enrollment, with 2 fewer children enrolled per school in the treated districts.

When split by primary and upper primary grades, it is clear that this effect is driven by primary classes where the magnitude is 2.23 (Columns (iv) and (v)). We do not find any change in the enrollment of children in upper-primary classes. Since these children are already past elementary school (which is free in case of government schools), it is possible that households do not want to withdraw these children from schools as they have invested in their schooling substantially.<sup>18</sup>

# **5.2 Effects on Enrollment by Type of Schools**

In order to examine if the type of school that children attend is affected, we evaluate equation 2 and report the results in Table 3. In Table 3, we show the interaction of the MGNREGA dummy interacted with school types indicators. The excluded category is ‘other types’ schools. Columns (i), (iii), and (v) repeat the results of the estimation of equation 1 for overall enrollment, primary enrollment and upper-primary enrollment with additional controls for school type by year fixed effects.

Overall enrollment in government schools is unaffected, whereas enrollment reduces significantly for private schools (Column (ii)). The coefficient on the interaction term with the private school indicator is significant at the 5 percent level. This result is driven by primary schools (Columns (iii) - (vi)).<sup>19</sup> Since 66 percent schools in the data are government schools and only 13 percent are private schools, the decrease in enrollment

> 18However, it is also possible that households who are employed in MGNREGA sites are younger and do not have children beyond the primary grades. In our subsequent analysis, we do observe heterogenous effects on children in upper primary schools as well. Hence we do not think that participating household’s demographic composition is driving these results.

> 19In the previous version of the paper, where we did not include the school type (private, public or others) by year fixed effects, the decreases in enrollment were being driven by public schools, and private school enrollment actually seem to have improved. However, we thank an anonymous referee for suggesting that enrollment in different school types could be trending differentially and we need to account for that by including the school type times year fixed effects.

14
per private school is much larger in magnitude. The effect of the program on overall enrollment is small in magnitude. Using the average number of government, private and other schools per district in the sample period, our results indicate that 9,824 children per district are not attending school due to the program.<sup>20</sup> Our identifying assumption is that there are no pre-trends in enrollment in districts belonging to different phases prior to MGNREGA’s implementation. DISE data is not available for all states prior to 2005, although major states are covered since 2003. We use data from 2003 to 2005 to check if there are differential pre-trends in enrollment by phases of MGNREGA roll-out.<sup>21</sup> In Appendix Table S4, we control for district-specific changes in enrollment from 2003 to 2005 (pre-treatment years) and allow this to vary over time by interacting with year indicators for the states for which we have pre-program data.<sup>22</sup> The overall effect on enrollment and enrollment by primary and upper primary are similar to those reported in Table 3.

Prior to the program implementation, we observe that the Phase III districts are better in levels. But the growth rate in enrollment is similar. Appendix Figures S2 and S3 show that between 2003 and 2005, the growth in enrollment and number of schools looks similar across districts in different phases. These two tests together show that pre-trends in enrollment are not biasing our results.<sup>23</sup> As we discussed earlier, a concern with the DISE data is that there is measurement error in reporting. Since school headmasters provide the information, it could be inaccu-

> 20In results not shown, we do not find any differences in effects for girls versus boys.

> 21In the Appendix, we discuss that our main results are no different if we exclude or include the states for which we do not have DISE data prior to 2005, we are reassured that the sample for which we have data prior to 2005 is not systematically different. The results are reported in Appendix Table S3. Limited data for a few states is also available for 2001 and 2002 but the coverage is not as expansive. Since data for many states and many variables is not available, we do not use these years.

> 22The study lost 0.7 percent of the sample schools as new districts were carved in 2004 and we are unable to use their pre-trend data. The study also checks the consistency of results when excluding those schools without pre-trends in Appendix Table S3.3.

23Appendix S3 on robustness tests further substantiate our identification by showing in a year-by-year comparison of early versus late districts, that the decline in enrollment occurs in 2006 after the early phases are treated. Appendix Figure S4 depicts this in a graph. We also conduct a placebo test to rule out pre-trends in our results for children’s employment to ensure credibility of our findings. The results are discussed in Subsection D3 in the online Supplemental Appendix.

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rate as they may have incentives to inflate enrollment numbers . If the policy change does not change the reporting behavior of the headmasters differently in districts of different phases, our double differencing approach should yield unbiased estimates. However, if the policy change systematically changes the reporting behavior then our estimates could be biased. For our results to be generated by measurement error, the schools in the early phases districts would have to under-report enrollment and this would have to vary across public and private schools and primary and upper primary schools which is highly unlikely.

There is also a tremendous amount of heterogeneity in the quality of private schools. Hence, we examine if the quality of the private schools influences household decisions. Private schools are expensive but may not necessarily be of good quality. If we split the private schools in quartiles of the student-teacher ratio, we see that the drop in enrollment in private schools is driven by poor quality private schools which have very high student-teacher ratio. The interactions of highest two quartiles with thresholds of 1.35 teachers to 100 children and 2.3 teachers to 100 children with the NREGA commenced indicator are negative, large, and statistically significant. These results are presented in Table 4 and are very important from policy perspective. These findings indicate that households are responsive to the quality of the schools when making investment decisions about children’s human capital. Low quality private schools could have lower returns to schooling or could be admitting more marginal students. Hence, when the opportunity cost of a child’s time in school increases, parents withdraw their children from such low quality schools. This also highlights that the private schools are not always an optimal schooling choice for the households.

# **5.3 Schooling Outcomes**

Absenteeism from school or devoting fewer hours to school work can influence performance outcomes even if the child is enrolled in school. Hence, we also examine effects on 16
schooling outcomes.For grades 5 and 7, the data reports whether a student passed the exam and if they passed with more than 60 percent marks.

In Table 5, we show that the passing rate in government schools falls by 1.8 percent for grade 7 students (Columns (ii) and (iv)) with the coefficient significant at the 10 percent significance level, whereas there is no effect on grade 5 (Columns (i) and (iii)). The program effects passing with more than 60 percent marks much more significantly. Both private and government school 7th graders do worse on this measure. This effect is almost twice as large for government schools than the private schools and the difference is statistically significant (Columns (vi) and (viii)).<sup>24</sup>

# **5.4 Mechanisms**

In order to shed light on the mechanism, we examine the employment outcomes of children in our DID framework. The data on child labor come from the National Sample Survey Organization (NSSO) employment and unemployment surveys (rounds 2004-05 to 2008-09) and we employ earlier rounds to carry out a falsification check. The data asks individuals to identify their principal occupation in the last month. We examine two outcome variables: Child reports working (employed, self employed or unpaid family labor) and child reports doing chores (housework or free collection of goods). We restrict our sample to 206,321 non-disabled children aged between 5 and 15 from the two rounds and look at their reported principal activities. The indicator for ‘working’ equals to 1 if a child’s reported principal activity is working in the household enterprises (paid or unpaid), as wage employee, or in other types of work, and 0 otherwise. The indicator for doing chores is 1 if a child’s reported principal activity is attending to domestic duty or doing any other housework, and 0 otherwise.<sup>25</sup>

> 24The program does not affect the students’ appearing at exams conditional on enrollment, as reported in Appendix Table S6.

> 25Other alternatives for principal activity include attending educational institution, seeking jobs, rentiers, pensioners, remittance recipients, and others.

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The empirical model is as follows: _Lidst_ = _γ_ 0 + _γ_ 1 _PhaseI ∗ Post_ + _γ_ 2 _PhaseII ∗ Post_ + _γ_ 3 _Zds ∗ Tt_ + _Tt_ + _Ids_ + _εidst_ (2) where _Lidst_ is the reported labor outcome of child _i_ in district _d_ in state _s_ at time _t_ . _PhaseI_ and _PhaseII_ are the indicators for the respective phases; _Zds_ is a vector of district-level controls for demographic characteristics, and is interacted with year indicators to control for trends in these characteristics; _Tt_ and _Ids_ are year- and districtfixed effects, respectively, and _εidst_ is the idiosyncratic error term. After the program, there is a 1.33 percent increase in the likelihood of child reporting working in Phase I districts relative to Phase III districts (Column (i) of Table 6). This is significant at the 5 percent significance level. In Phase II districts, this effect is 1.17 percent increase marginally significant at the 10 percent significance level. We cannot reject the equality of these two coefficients. In column (ii), the coefficient for doing chores is small and positive but indistinguishable from 0. Our findings indicate that child labor supply increases in response to the program.

# **6 Conclusion**

We use the phased roll-out of MGNREGA to estimate the impact of employment based safety net programs on schooling and labor market outcomes of children. We find that fewer children enroll in schools in primary grades due to the introduction of the program and their likelihood of being employed increases. This is surprising especially because the schooling aspirations for children have become stronger in the country and large strides have been made in ensuring universal enrollment in primary schools. The drop in enrollment is driven by low quality private schools implying that school quality affects enrollment choices when the opportunity cost of attending school shifts.

We also find that among the enrolled, school pass rate with more than 60 percent 18