The World Bank Economic Review, 36(2), 2022, 514–532 https://doi.org10.1093/wber/lhab019 Article A Tale of Two Programs: Assessing Treatment Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 and Control in NREGA Studies Girish Bahal Abstract This article revisits impact evaluation studies on the largest public workfare in the world, NREGA. In an en- vironment where randomization is not feasible, I show why an impact evaluation exercise on NREGA should acknowledge the existence of an older program, SGRY. Using novel district-level expenditure data on SGRY, this article shows how ignoring the older program is likely to underestimate the general equilibrium impact of the employment policy on various relevant socioeconomic outcomes. In most cases, ignoring SGRY underestimates NREGA’s impact by 30–40 percent. JEL classification: H53, I38, J38 Keywords: impact evaluation, treatment-control, public workfares, SGRY, NREGA 1. Introduction Often, similar older policy initiatives precede “new” antipoverty programs implemented by governments across the world. For example, Brazil’s flagship antipoverty program Bolsa Escola, a conditional cash transfer program, was replaced with Bolsa Familia in 2003. In 2011, Bolsa Familia was extended to Brasil Sem Miséria (Brazil without poverty). In Mexico, Prospera was preceded by Oportunidades, which in turn was built on Progresa. Similarly, when India introduced the largest public works program in the world in 2006—the National Rural Employment Guarantee Act (henceforth NREGA)—it replaced an older program—Sampoorna Grameen Rozgar Yojana (henceforth SGRY). Such government interventions naturally raise important questions for research and policy. In an environment where randomization is not feasible, quasi-experimental pretest–posttest designs often identify the impact of a change in eco- nomic policy. For example, a difference-in-differences model identifies the policy impact by comparing the average change over time in the outcome variable in the treatment and control groups. Girish Bahal is Assistant Professor at the Business School, University of Western Australia, Perth, Australia; his email address is girish.bahal@gmail.com. The author is very grateful to the editor in charge of this article, Eric Edmonds, and three anony- mous referees for thoughtful and constructive comments. The author thanks Toke Aidt, Tiago Cavalcanti, Giancarlo Corsetti, Douglas Gollin, Rema Hanna, Clément Imbert, Sriya Iyer, Michael Jetter, Kaivan Munshi, Anand Shrivastava, Laura Zim- mermann, and seminar participants at the University of Cambridge, Delhi School of Economics, Indian Statistical Institute Delhi, and International Association for Applied Econometrics for helpful comments and suggestions. The author also thanks Thiemo Fetzer for sharing TRMM rainfall data and Manisha Shah and Bryce Millett Steinberg for sharing data and codes for their study on NREGA’s impact on human capital outcomes. Finally, the author gratefully acknowledges the Ministry of Rural Development, Government of India, for help in data collection. A supplementary online appendix is available with this article at The World Bank Economic Review website. © The Author(s) 2021. Published by Oxford University Press on behalf of the International Bank for Reconstruction and Development / THE WORLD BANK. All rights reserved. For permissions, please e-mail: journals.permissions@oup.com The World Bank Economic Review 515 This article highlights an important aspect of impact evaluation studies on NREGA. While estimating the general equilibrium impact of the program, it is crucial to control for a similar older workfare that was exclusively present in the “control” districts that received NREGA late. This article shows how ignoring the continued existence of the SGRY program has first-order effects on estimating the employment policy’s real impact. I show how ignoring SGRY overestimates the gap in employment provision (or the treatment dosage) between the treatment and control districts and underestimates the effect on various Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 relevant socioeconomic outcomes studied in the literature.1 Specifically, I analyze the general equilibrium impact of NREGA on (a) agricultural wages, (b) casual earnings, (c) casual employment in the public and private labor markets (for men and women), and (d) human capital outcomes in terms of children’s school enrollments and child labor. For all outcomes, the impact of NREGA is more pronounced when we control for SGRY. The extent of underestimation of program impact without SGRY is expectedly heterogeneous across outcomes. However, in most cases, the program impact without controlling for SGRY is underestimated by between 30 and 40 percent. I use a novel dataset of annual program expenditure for every district in the country for the SGRY and NREGA programs. The expenditure data for SGRY is from its implementation in 2001 until its last op- erational year in 2007. For NREGA, the expenditure data are between 2006 and 2010. To the best of my knowledge, these are the most detailed and disaggregated expenditure data used in any comparable analy- sis on public works in a developing country. The data reveal three salient findings. First, the two programs never coexisted in a district at any point in time. Next, NREGA was implemented in phases, covering 200, 330, and all the districts of the country by 2006, 2007, and 2008, respectively. The second finding is that during the staggered rollout of NREGA, SGRY continued to be present exclusively in the “non-NREGA” or “control” districts during 2006 and 2007. Third, the availability of public employment under SGRY was not inconsequentially small relative to NREGA. Approximately 14 percent of the districts covered under NREGA during 2006 and 2007 spent less than the average per capita program expenditure incurred under SGRY in the control districts during both these years. These findings blur the distinction between treatment and control districts where NREGA substituted and not supplemented the older program. I start by estimating the general equilibrium impact of large public workfares on short-term wages for comparable manual labor work in the private sector. The question itself is of policy relevance since wage income from casual labor is a principal source of income for the poor in a developing country like India (Banerjee and Duflo 2007). A consensus among the recent literature on NREGA is that the pro- gram did lead to modest increases in private wages (Azam 2012; Berg et al. 2018; Imbert and Papp 2015; Muralidharan, Niehaus, and Sukhtankar 2017; Zimmermann 2012). Notably, the income gain due to higher private wages is not limited to program beneficiaries but also applies to non-beneficiaries. For ex- ample, Muralidharan, Niehaus, and Sukhtankar (2017) note that the general equilibrium effect of NREGA is “a much more important driver of poverty reduction than the direct income provided by the program.”2 First, I estimate the impact of the employment policy on agricultural wages. Since agricultural wage data are available at annual frequency, I control SGRY by redefining “treatment” as spending in a district under public workfares. Analogous to the study on Minimum Legal Drinking Age (MLDA) laws in the United States by Angrist and Pischke (2014), I use program expenditure as a measure of “exposure to the policy” and use the within and across district variation in program expenditure to estimate the effect of public workfares on private wages. A limitation of this approach is that program spending may correlate with local labor-market conditions, which can influence wage rates in the private sector. I partially address this issue by controlling for district and year fixed effects and other relevant time-varying district controls. I also control for “potentially endogenous” changes in program expenditure at a district-year 1 See Sukhtankar (2017) for a thorough review of the literature on NREGA. 2 Similarly, Imbert and Papp (2015) find that increases in private sector wages represent “a third of the total welfare gain for the poor.” 516 Bahal level that represent under- (or over-) utilization of funds made available by the government.3 The critical point is the extent of underestimation in the results when we ignore SGRY. Controlling for expenditure under SGRY, the results indicate public workfares to have increased agricultural wages between 0.4 and 1 percent per annum. However, if one assumes no expenditure to have occurred under the older program, this underestimates NREGA’s impact on agricultural wages by 43 percent, making it insignificantly different from zero. This null result without SGRY is consistent with the findings reported by Berg et al. Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 (2018) who also use Agricultural Wages in India (AWI) data.4 This supports the hypothesis that ignoring the older program leads to an overestimation of the “dosage” of treatment by public workfares, which downward biases the results. Second, I use data from National Sample Surveys (NSS) to estimate a baseline specification that evaluates the effect of NREGA on daily casual earnings without controlling for expenditure under SGRY. The results indicate NREGA increased daily private earnings in the lean or “dry” agricultural season by approximately 4.9 percent in the districts that received NREGA early during 2006 and 2007. I find no significant increase in daily private earnings in the peak or “rainy” agricultural season. These baseline results are very similar to the results reported by Imbert and Papp (2015). Keeping the exact baseline specifications, I then control for per capita expenditure under SGRY during 2004, 2005, and 2007. Comparing the results with and without SGRY, I find that not controlling for SGRY underestimates NREGA’s impact on daily casual earnings by approximately 34–40 percent. Third, I study the general equilibrium effect of NREGA on casual employment in the public and private labor markets. Consistent with the results reported in the literature, I find NREGA to significantly increase (decrease) casual work in the public (private) labor market during the dry season when agri- cultural work in the private sector is scarce. Not controlling for SGRY, I find NREGA to have increased work in public employment by approximately 1 percentage point and decreased private sector work by 1.8 percentage points in the dry season. Not controlling for expenditure under SGRY underestimates the impact on public and private employment by approximately 25 percent and 34 percent, respectively. The same pattern emerges when I estimate employment outcomes for men and women separately. Finally, I study NREGA’s impact on human capital outcomes. Recent studies like Li and Sekhri (2020), Islam and Sivasankaran (2015), and Shah and Steinberg (2021) conclude that school enrollment numbers declined while child labor increased due to the spillover effects of the public workfare. Adukia (2020) also finds small negative effects of NREGA on educational outcomes. However, Adukia (2020) notes that the declines in education are not substantial, especially when the cost of every one-child decline in school en- rollment is compared to the benefit of the number of households employed through NREGA.5 Using data and replication codes from Shah and Steinberg (2021), I reassess the effect of NREGA on school enroll- ment and child labor after controlling for SGRY. While the change in coefficients is not nearly as significant as the change in labor-market outcomes for adults reported above, the results are more pronounced with SGRY. Controlling for SGRY, NREGA’s impact on school enrollment and child labor is more negative and positive, respectively. The marginal change in children’s outcomes is expected if, consistent with Adukia (2020), NREGA has a much more pronounced effect on adult outcomes relative to outcomes for children. 3 I acknowledge the possibility of some residual omitted variable bias even in the preferred specification with all possible controls. However, using statistics on the selection of observables and unobservables (Altonji, Elder, and Taber 2005; Oster 2019), I show that the degree of omitted variable bias is inconsequential and unlikely to overturn the main results. 4 Berg et al. (2018) do find NREGA to increase wages by 4.3 percent in a different specification where they use “exposure” to NREGA by adding the number of months a district is under NREGA. I abstain from discussing this specification since the focus of this paper is to highlight how the contemporaneous impact of public works policy may be under-reported if we ignore SGRY. See Bahal (2016) for a theoretical and empirical exposition on the spot vs. stock effects of public works. 5 See also Afridi, Mukhopadhyay, and Sahoo (2016), Das and Singh (2013), Das (2018), and Mani et al. (2020). The World Bank Economic Review 517 Overall, this article’s findings are consistent with the existing literature and reaffirm the significant gen- eral equilibrium effects of large public workfares. The key contribution of this study is to underscore the relevance of controlling for an older program while conducting an impact evaluation of a new policy inter- vention. In the absence of random treatment-control designs, ignoring relevant previous policies can sub- stantially underestimate a new policy’s impact. Using different outcome variables and data, I show how ig- noring the older program may considerably underestimate the workfare’s effect on the variable of interest. Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 The rest of the article is structured as follows. The next section discusses SGRY and NREGA in detail. The next two sections discuss data and the empirical model and results. The final section concludes. 2. NREGA and Its Predecessor Pan-India public workfare programs did not start from SGRY and date back to the Food for Work program in 1977. We restrict our analysis to these two programs due to two key reasons. First, both SGRY and NREGA were “integrated workfare programs” with employment generation and rural infrastructure creation as their dual objectives. Before 2001, these two objectives were addressed by multiple, smaller programs. Hence, no program before 2001 was structurally similar to SGRY and NREGA. See Bahal (2020) for a detailed discussion on India’s major rural welfare programs since 1980. Second, district-level expenditure information is not available for any program before SGRY. District-level program expendi- ture data are publicly available only for NREGA. The expenditure data for SGRY used in this paper was specially sourced from the Ministry of Rural Development, Government of India. The subsections below discuss and compare SGRY and NREGA in detail. 2.1. SGRY Sampoorna Grameen Rozgar Yojana (SGRY) was launched as a nationwide program on 25 September 2001 to address rural employment and infrastructure-related issues. With the introduction of SGRY, the government discontinued previous employment programs like Jawahar Gram Samridhi Yojana (JGSY) and Employment Assurance Schemes (EAS). The motivation to implement SGRY was to integrate differ- ent programs for wage employment into one universal scheme. Initially, SGRY operated as two streams with approximately equal outlays. From 2004, SGRY worked as a single program. Like NREGA, SGRY envisaged the generation of wage employment and rural infrastructure creation through labor-intensive public projects. The central (federal) and the state governments shared the program’s overall cost in the ratio of 75:25. 2.2. NREGA NREGA guarantees 100 days of unskilled manual work per annum to every rural household at the state- defined minimum wage. The ministry of rural development implemented NREGA in three phases. Starting from 2006, NREGA covered the country’s 200 most economically backward districts in its first year. The criteria for judging a district’s backwardness were based on measures like agricultural productivity, past agricultural wage level, and the density of scheduled castes and scheduled tribes in a district.6 In NREGA’s second phase, an additional 130 districts were covered by 2007. By the third phase in 2008, every district in the country had NREGA. Like its predecessor, NREGA aims to generate wage employment and develop rural infrastructure through public works. NREGA is a self-targeting antipoverty policy where the govern- ment, as an employer of last resort, provides income insurance to the rural poor while creating productive public infrastructure. During the financial year 2009–2010, NREGA generated around 2.6 billion work- days and employed approximately 55 million households. The total expenditure under NREGA amounted to about 0.6 percent of the GDP (nearly 5 percent of the agricultural output) during the same year. 6 This index was primarily based on district-specific and time-invariant fixed effects. 518 Bahal Figure 1. Program Expenditure and Employment Generated for NREGA and SGRY Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 Source: Annual physical and financial statements of SGRY and NREGA, Ministry of Rural Development (MoRD). Note: SGRY: Sampoorna Grameen Rozgar Yojana. NREGA: National Rural Employment Guarantee Act. Panel (a) shows the annual national expenditure for SGRY and NREGA (billion rupees, 2000 prices). Panel (b) shows total employment generated (in millions of person-days) every year by SGRY and NREGA. 2.3. SGRY during NREGA Implementation This section highlights the similarities between the two programs and discusses the continued existence of SGRY during the phasewise implementation of NREGA. As panel (a) in fig. 1 shows, adjusted for 2000 prices, nearly 40 billion Indian rupees were spent on SGRY at the national level in its first year in 2001. The expenditure at the national level under SGRY progressively increased to nearly 60 billion rupees by 2005. In comparison, the federal spending under NREGA in 2006 was approximately 70 billion rupees, which substantially increased to 118 billion and 178 billion in 2007 and 2008, respectively. This increase was primarily due to the scale-up of NREGA during its second and third phases. Panel (b) in fig. 1 shows the annual employment generated under SGRY and NREGA at the national level in millions of person-days. As expected, the employment trend under the two programs closely matches the trend in national expenditure. Panels (a) and (b) of fig. 1 highlight that although at a relatively smaller scale, a significant amount of spending and employment generation did occur under SGRY. It is important not to infer from the overlap of program expenditure in fig. 1, panel (a) that both programs were simultaneously in operation in some districts during 2006 and 2007. Rather, SGRY was exclusively present only in those districts that NREGA did not cover. Figure 2 illustrates this point more clearly by showing district level maps for southern India.7 Panel (a) of fig. 2 shows the rollout of NREGA in its first phase in 2006. The “non-NREGA” or “late- phase” districts are in white, while the shaded districts are the phase-I districts. In contrast, panel (b) of fig. 2 shows the employment expenditure that occurred in SGRY or NREGA in 2006. Similarly, panels (c) and (d) of fig. 2 show that even during the phase-II implementation of NREGA in 2007, SGRY was operational in the non-NREGA districts. Therefore, the district-level expenditure maps show that SGRY continued to operate in the non-NREGA districts during the phasewise implementation of NREGA in 2006 and 2007. 7 Maps for the whole country haven’t been displayed due to restrictions from the Cartography Unit at the World Bank. See the working paper version for the country maps. The World Bank Economic Review 519 Figure 2. Expenditure under NREGA and SGRY during 2006 and 2007 Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 Source: District level financial statements of SGRY and NREGA, Ministry of Rural Development (MoRD). Note: SGRY: Sampoorna Grameen Rozgar Yojana. NREGA: National Rural Employment Guarantee Act. The maps above represent do not represent India’s official map. Unit of observation is a district-year. Panels (a) and (c) plot per capita expenditure (in rupees) for NREGA in 2006 and 2007, respectively. Panels (b) and (d) plot per capita expenditure (in rupees) for NREGA and SGRY in 2006 and 2007, respectively. Further, the size and scale of public works under SGRY were consequential relative to NREGA during 2006 and 2007. Nearly 14 percent of the districts covered under NREGA during 2006 and 2007 spent less than the average per capita expenditure incurred under SGRY in the “non-NREGA” districts during both these years. These findings blur the distinction between treatment and control groups defined by the 520 Bahal presence or absence of NREGA. In fact, it was by design and not by accident that no district was without a workfare program during 2006 and 2007. According to the implementation design of NREGA, the late-phase districts were supposed to have SGRY operational in them until NREGA finally enveloped them in phase II or III. The Act itself notes that until any such Scheme [NREGA] is notified by the state government...Sampoorna Grameen Rozgar Yojana (SGRY)...shall be deemed to be the action plan for the Scheme [NREGA] for the purposes of this Act. (NREGA, Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 2005, p. 3). Therefore, the government did not implement NREGA independently of SGRY. Instead, it systematically and gradually replaced SGRY. The two programs were also strikingly similar to each other in their scope and objectives (see table S4.1 in the supplementary online appendix). As table S4.1 shows, both programs covered all of the country’s districts. The primary targets for both programs were the provision of wage employment and infrastructure creation. Both schemes involved similar types of labor-intensive public works and were funded mainly by the central government. Finally, both programs encouraged female par- ticipation in the program by keeping a minimum female participation target of 33 percent. NREGA can be best understood as an intensification of an already existing public workfare policy of the government. A valid concern can be that NREGA “guaranteed” employment and was hence structurally different from SGRY, where the program budget dictated the level of employment provision. This theoretical distinction, however, did not precipitate into ground reality. Despite providing a de jure entitlement to employment on demand, NREGA is de facto rationed. Dutta et al. (2012), for example, report a country average rationing rate of around 44 percent, with some states rationing more than 80 percent of the demand for work under NREGA. Rationing may as well be unavoidable if the maximum budget for NREGA is finite, and the offered wage rate cannot fall below a socially acceptable minimum wage. Muralidharan, Niehaus, and Sukhtankar (2016) highlight the case of unmet demand in NREGA due to the limited “state capacity” to implement welfare programs in developing countries like India. 3. Data 3.1. Program Expenditure Data Data on program expenditure is collected from the Ministry of Rural Development (MoRD). Although the information on NREGA is publicly available, data on SGRY was specially sourced from MoRD and Datanet (India).8 MoRD reports districtwise annual physical and financial statements for both the programs. Physical statements provide information on the number of public works completed and employment generated, while financial statements give statistics on the availability of funds and actual expenditure. I use data on “actual expenditure” when referring to program expenditure in the empirical models below. Data on SGRY is from its implementation in 2001 to 2007, its last operational year. Data on NREGA is from 2006 to 2010. In total, I use 10 years (2001–2010) of district-level data on employment expenditure. The data used in this article is the most disaggregated and detailed data on program expenditure used in any comparable analysis on public workfares. 3.2. Agricultural Wage Data I use data on agricultural wages from the AWI series published by the Ministry of Agriculture. The AWI data has been extensively used for time series analysis on agricultural wages in India (see, for example, Ravallion, Datt, and Chaudhuri 1993, Özler, Dutt, and Ravallion 1996, and Berg et al. 2018). The AWI district-level wage data provide monthly information on daily wage rates. I construct a measure of the 8 To check the reliability of the SGRY district-level data, I aggregate district-level expenditure estimates to state level. Apart from minor differences, the state-level figures match with the official state-level estimates published in MoRD reports. The World Bank Economic Review 521 agricultural wage rate from 2001 to 2010 by taking the average daily wage rates for men and women for agricultural activities like plowing, sowing, reaping, and weeding. Matching AWI Wage Data with Expenditure Data: The AWI data, unlike the program expenditure data, are not reported for all districts. Data for nearly 40 percent of the districts are available for fewer than 6 out of 10 years. To improve the signal-to-noise ratio of agricultural wages, I convert the monthly AWI data to annual frequency by taking 12-month averages in the Indian fiscal year format to match the Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 program expenditure data. I further improve the quality of the wage data by focusing on a balanced panel of 134 districts from 12 major Indian states for 10 years. For the analysis of agricultural wages, I have a total of 1,340 observations. Since I lose districts with incomplete wage data, a possible objection could be the correlation of a district’s backwardness with the unavailability of wage data. If this is true, then restricting the analysis to 134 districts should result in the proportion of early-phase NREGA districts being substantially lower in this subsample than the aggregate sample. Encouragingly, this is not the case. The percentage of phase-I and phase-II districts in the full sample—approximately 37 percent and 58 percent, respectively— closely matches the subsample proportion of 42 percent and 63 percent, respectively. Both the wage and expenditure data are deflated to 2001 prices using the labor bureau’s consumer price index for rural laborers (CPI-RL). Unless otherwise mentioned, all variables in the empirical analysis are in real, per capita terms. 3.3. National Sample Survey Data Casual Earnings and Employment Outcomes: Alternative data used in the literature are from the nationally representative employment and unemployment surveys carried out by the National Sample Survey Organization (NSSO). The nationally representative rounds with a large sample size usually happen every three to five years. This study also employs NSS data to compare the impact of NREGA on daily casual earnings with and without controlling for SGRY. Since both programs apply only to persons living in rural areas, I restrict the analysis to persons in rural areas and persons aged between 18 and 60. The sample includes 440 districts within the 17 largest states of India. I use data from July 2004 to June 2005 (round 61) to form the pre-NREGA period. For the post-NREGA period, I use data from July 2007 to June 2008 (round 64). Consistent with the methodology used in Imbert and Papp (2015), all statistics and estimates computed using the NSS data are adjusted using sampling weights. For earnings, the key outcome variable in the NSS data is an individual measure of daily casual earnings. The NSSO surveys distinguish whether the waged work is “salaried,” which is long term and often involves a formal contract, or “casual,” which is temporary and informal. The survey records total earnings from casual labor over the past seven days for individuals working in casual labor. I compute casual earnings for each individual as the average earnings per day worked in casual labor. I then use a monthly, state-level price index for agricultural laborers from the Indian Labour Bureau to construct real earnings. For employment outcomes, I compute for each person the percentage of days in the past seven days spent in mutually exclusive activities: private sector work and public works. Private sector work includes waged work, self-employment, and domestic work. Child Labor and Human Capital Outcomes: Consistent with Shah and Steinberg (2021), I use the NSS rounds 61 (2004–2005), 64 (2007–2008), and 66 (2009–2010) to examine the impact of NREGA on schooling outcomes and child labor. Since this data set has information about the “primary activity” of each household member, this allows the construction of employment and schooling status at the individual level. An individual whose primary activity is going to school is defined as “attends school.” “Child labor” equals 1 if the child’s primary activity is domestic work, work at home, or work outside 522 Bahal the home. For more details about the data and construction of child labor and human capital outcomes, see Shah and Steinberg (2021).9 Controlling for SGRY in NSS Data: To identify the impact of NREGA on an outcome variable, studies using NSS data have relied on an indicator variable for the phasewise implementation of NREGA. However, controlling for SGRY in the form of an indicator is not possible as expenditures under SGRY and NREGA were perfectly negatively correlated with each other. In other words, if NREGAd,t takes Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 the value 1 (0) for a district d when NREGA is present (absent) in year t, then an analogous indicator for SGRY is SGRYd,t = 1 − NREGAd,t . Therefore, in the NSS regressions, the key SGRY control is the per capita program expenditure in a district under SGRY during 2004, 2005, and 2007. I match this expenditure data with data from NSS rounds 61 and 64. For human capital regressions, SGRY expenditure is zero for round 66 (2009–2010). 3.4. Rainfall Data I use remotely sensed rainfall data from the Tropical Rainfall Measuring Mission (TRMM) satellite. See Fetzer (2020) for a detailed discussion on the consistency and the quality of TRMM data over any other remote sensed or ground-based data.10 4. Empirical Model and Results This section discusses the impact of NREGA after controlling for SGRY on a variety of outcome variables. First, I use AWI data and estimate the effect of public workfares on agricultural wages. Here, I define treatment as a continuous measure using program expenditure. In this specification, I show how the impact of workfares on agricultural wages is underestimated by approximately 43 percent if we ignore spending under SGRY. Second, I use NSS data and estimate NREGA’s impact on casual earnings. Analogous to agricultural wages, daily casual earnings are underestimated by 34–40 percent if we do not control for expenditure under SGRY. Third, I estimate NREGA’s impact on employment outcomes: private sector work and public works. The effect on both employment outcomes is again underestimated by 25–34 percent without SGRY. Finally, I reassess child labor and human capital outcomes with and without SGRY. 4.1. Impact on Agricultural Wages 4.1.1. Using Binary Treatment I begin by estimating the general equilibrium effects of public workfares on private wages by estimating equation (1) à la Berg et al. (2018). In equation (1), wd,t is agricultural wage, α is a constant, and NREGAd,t is an indicator that takes the value 1 for a district from the year NREGA was introduced and 0 before that. Thus, given the staggered implementation of NREGA, NREGAd,t takes the value 1 for different districts at different points in time. The coefficient ζ is the DD estimate that captures the impact of NREGA on private wages. District and year fixed effects are controlled by α d and θ t respectively, while ξ d t are district-specific trends. The subscripts d and t denote district and year, respectively. To account for serial correlation, all regressions report standard errors clustered at the district level that are robust to heteroskedasticity as well. Given 9 As Shah and Steinberg (2021) report, 71 percent of adolescents aged 13–17 attend school (as main activity), while 25 percent report working. Younger children aged 5–12 are much more likely to attend school (85 percent) and much less likely to report working (about 3 percent). 10 Thanks to Thiemo Fetzer for sharing the rainfall data. The World Bank Economic Review 523 the heterogeneity in the size of districts, all regressions use weights based on the district population :11 log(wd,t ) = α + αd + θt + ξd t + ζ NREGAd,t + υd,t . (1) Consistent with Berg et al. (2018), I find the DD estimate ζ to be positive and significant at 7.2 percent without any controls, but ζ becomes statistically insignificant from 0 once I control for district and year fixed effects (see table S4.2). Equation (1) likely underestimates the true impact of the program on wages Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 by overestimating the gap in program provision between treated and control districts. 4.1.2. Using Program Expenditure as Treatment Here, I redefine treatment as the amount of real per capita spending under the two programs in any given district. Measuring treatment using program expenditure helps circumvent the overestimation of employment provision between NREGA and SGRY districts in a binary treatment model. Here, I study the effects of public workfares on agricultural wages by estimating the elasticity of wages with respect to program expenditure. I estimate various specifications of the following model: −1 log(wd,t ) = α + αd + θt + β sinh (ed,t ) + φ Xd,t + ξd t + υd,t , (2) where α , α d , θ t , and ξ d t have the same interpretation as in equation (1) and Xd,t is a vector of controls discussed below. The key regressor, sinh −1 (ed,t ), is the inverse hyperbolic sine (IHS) transformation of expenditure in a district d and year t under SGRY or NREGA. IHS transformation can be interpreted in exactly the same way as a standard log transformation since sinh −1 (ed,t ) ≈ log (2) + log (ed,t ). A key advantage of IHS transformation is that it allows for zero-valued observations, which is relevant in this case as I will compare equation (2) with and without SGRY expenditure. Therefore, β is the elasticity of wage with respect to expenditure. An obvious challenge in identifying the policy impact on wages using the expenditure approach is that program expenditure can be endogenous to local economic conditions, district characteristics, and wages. For example, if program expenditure is correlated with time-invariant district effects like demographics, susceptibility to droughts, and general agricultural productivity, then β may suffer from omitted variable bias. To illustrate this point, column 1 of table 1 reports β obtained from estimating equation (2) with sinh −1 (ed,t ) and an intercept as the only regressors. As can be seen, β is estimated to be around −0.045, significant at a 95 percent confidence level. Intuitively, if the level of program expenditure is higher for economically backward districts, then β should be expected to suffer from a negative bias. To address the omitted variable bias, column 2 reports the elasticity estimate after including the district and year fixed effects. While α d controls for any time-invariant district effects, θ t controls for any endogenous change in outlays for public workfares at the national level in response to aggregate shocks like widespread droughts. As expected, adding these controls substantially increases β from −0.045 to 0.043, where the coefficient estimate is highly significant (t ≈ 3.5). The specification in column 2 may still be susceptible to omitted variable bias due to district-year shocks that may simultaneously influence field wages and program expenditure. For example, local ad- verse weather events may adversely affect the agriculture sector (and agricultural wages) while resulting in higher than expected program spending due to increased demand for public works.12 Such local stresses like conflicts or weather abnormalities may negatively impact wages and result in higher than expected expenditure. If true, the estimated wage elasticity in column 2 is still likely to suffer from a downward bias. I exploit the two programs’ fund allocation process to construct a variable UtilizationRatiod,t that captures unexpected increases or decreases in spending that may represent potentially endogenous expenditure fluctuations. 11 The results largely remain the same if all observations are weighted equally. 12 For example, Drèze (1990) discusses the increased take-up of public employment by laborers under Maharashtra’s public workfare during the famine of 1970–1973. 524 Bahal Table 1. Impact of Public Works on Agricultural Wages SGRY + NREGA Only NREGA (1) (2) (3) (4) (5) sinh −1 (ed,t ) −4.493** 4.250*** 5.936*** 2.342** 1.341 [−2.123] [1.215] [1.295] [1.021] [1.034] Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 District effects No Yes Yes Yes Yes Year effects No Yes Yes Yes Yes Oth. controls No No Yes Yes Yes Het. trends No No No Yes Yes Observations 1,340 1,340 1,340 1,340 1,340 Source: Author’s analysis based on Agricultural Wages in India data (for field wages) and program expenditure data for SGRY and NREGA from 2001 to 2010. Program expenditure data are from the Ministry of Rural Development, Government of India. Note: All estimates are of order 10−2 . The unit of observation is a district-year. The dependent variable in all the regressions is the log of field wages. Columns 1–5 have sinh −1 (ed,t ) as the key regressor. In columns 1–4, program expenditure is for SGRY (b/w 2001 and 2007) and NREGA (b/w 2006 and 2010). In column 5, only expenditure under NREGA is considered (all expenditure values under SGRY are substituted by zero). The inverse hyperbolic sine (IHS) transformation of the expenditure variable sinh −1 (ed,t ) has the same interpretation as log (ed,t ). Other controls include NREGAd,t , UtilizationRatiod,t , Raini, t , state elections-year indicator, and density of scheduled caste and scheduled tribe population in a district. All regressions are weighted by district-level population. The standard errors reported in square brackets are clustered at the district level and are robust to heteroskedasticity. SGRY: Sampoorna Grameen Rozgar Yojana. NREGA: National Rural Employment Guarantee Act. *p < 0.10, **p < 0.05, ***p < 0.01 For both SGRY and NREGA, the central government releases program funds to the states. The states, in turn, distribute the funds at the district level. Since both programs are in principle demand driven, actual expenditure (or program liabilities) at the district level can be higher or lower relative to the total funds made available in any given year. The central government fulfills any excess expenditure in the next cycle. Hence, financial accounts roll over from one financial year to the next. Since there is information on both fund availability and actual expenditure at the district-year level, I construct UtilizationRatiod,t = 100 ∗ Actual_expenditured,t /Funds_made_availabled,t . Consistent with public workfares being demand driven, if deviations in actual expenditure relative to fund availability represent demand shocks, then this may confound the impact of employment policy on wages as reported in column 2 of table 1. Specifically, if overutilization (underutilization) of funds reflects more (less) demand for work under public workfares when the private labor market is slack (tight), then the elasticity estimate in column 2 of table 1 will be downward biased. To address these concerns, I estimate β after controlling for such potentially endogenous observations by adding UtilizationRatiod,t as an additional regressor in column 3.13 In addition, the specification in column 3 also adds a vector of other important time-varying district controls like (a) average annual rainfall (in millimeters), (b) an indicator for state elections, (c) the density of scheduled castes and scheduled tribes in a district, and (d) the NREGA implementation indicator NREGAd,t , which controls for a change in program regime. These variables further control for changes in program expenditure that may be correlated with (a) local weather shocks, (b) political motivations at the time of state elections, (c) a change in program regime, or (d) time-varying district demographics that may be correlated with program expenditure and agricultural wages. The inclusion of this vector of additional controls Xd,t increases the elasticity estimate to 0.06, which is highly significant (t > 4.5). Based on the average growth in per capita program expenditure of 16.1 percent per annum, the specification in column 3 suggests public workfares have increased private wages by approximately 0.95 percent per annum. 13 From 2012, funds are directly transferred from the state to the worker’s account through the electronic fund management system (eFMS). Therefore, more recent data have little scope for an accounting design where fund availability and actual expenditure are different. The change in fund management is a key reason I limit the data in this study up to 2010–2011. The World Bank Economic Review 525 4.1.3. Parallel Trends Assumption The specifications in columns 1–3 of table 1 assume the existence of parallel trends. However, assuming that all districts experienced a similar growth path between 2000 and 2010 may be a strong assumption. To control for district-specific trends, I add 134 district-specific trends ξ d t to the model in equation (2).14 Adding heterogeneous trends corrects any bias in β if growth in spending is correlated with economic progress at the district level. For example, if the change in program expenditure is correlated with Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 improvements in general development indicators and institutional capacity to implement government programs, then the elasticity estimate in column 3 of table 1 would be overstated. The inclusion of district-specific trends allows inference independent of the parallel trends assumption. However, adding multiple trends may lead to a very strict specification that fails to distinguish the policy impact from differential trends, especially if treatment effects emerge only gradually (Angrist and Pischke 2014). Column 4 of table 1 reports the elasticity of wages after adding heterogeneous trends as additional controls. Adding district-specific trends lowers β to 0.023, which is significantly different from zero at the standard 95 percent confidence level. The elasticity estimate in column 2 suggests wage increases of approximately 0.4 percent per annum. As explained above, the estimate in column 4 likely represents a lower bound of the impact of workfare programs on the private labor market if the policy does not lead to a sharp contemporaneous jump in private wages. I, however, treat column 4 as the preferred specification as it corrects for any time-varying district controls that may confound the elasticity estimate reported in column 3 of table 1. I further acknowledge the possibility of some residual omitted variable bias even in the preferred specification of column 4. However, using statistics on the selection of observables and unobservables (Altonji, Elder, and Taber 2005; Oster 2019), I show in the supplementary online appendix (table S1.1) that the size of omitted variable bias is inconsequential and unlikely to explain away the impact of public workfares on wages. Specifically, the unobservable variables would need to be an order of magnitude more strongly negatively correlated with program expenditure than all other controls accounted for to explain away the estimated coefficient. This is a very strong assumption, especially since observables in column 4 explain more than 92 percent of the variation in wages. Indeed, the bias-adjusted coefficient of program expenditure is strictly higher than 0.023. Consistent with the idea of public workfares, if program expenditure is positively correlated with unobservables that, in turn, negatively affect wages in the private sector, then the elasticity estimate in column 4 of table 1 represents a lower bound of the true parameter. A case in point is a productivity-diminishing weather event that leads to higher program expenditure on the one hand and lowers agricultural wages on the other. Therefore, based on the elasticities reported in columns 3 and 4 of table 1, public workfares appear to have increased private wages in the agriculture sector between 0.4 and 1 percent per annum. 4.1.4. Ignoring SGRY Finally, I estimate the effect of ignoring SGRY when measuring treatment based on program expenditure. Column 5 of table 1 reports the impact of program expenditure on wages but after replacing expenditure values under SGRY by zero. As can be seen, keeping the same set of controls as in column 4, column 5 underestimates the effect of public workfares by approximately 43 percent when I ignore expenditure under SGRY. In column 5, β is equal to 0.013 which is insignificantly different from zero. Consistent with the result in the baseline model with binary treatment, ignoring SGRY underestimates the impact on wages even with continuous treatment. 14 An unbiased estimate of the program impact requires that there are no contemporaneous district-level trends that are correlated with program expenditure and agricultural wages. See, for example, Hoynes, Page, and Stevens (2011) who follow a similar strategy to identify the effect of the Women Infants and Children (WIC) program on birth outcomes in the United States. 526 Bahal In the supplementary online appendix, I check for the stability of the elasticity estimate over the two program regimes in table S2.1. Thereafter, I test whether there is any subsample heterogeneity based on how well the employment programs were implemented (table S2.2). The results are consistent with previous studies like Imbert and Papp (2015) that report a more significant impact for states that implemented NREGA well. Table S3.1 reports wage elasticities based on gender and over different program regimes. Finally, table S4.3 reports table 1 but for wages for relatively skilled labor such as a Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 carpenter, cobbler, and blacksmith.15 We do see a positive impact on wages for skilled labor as well but, consistent with the expectation, there is a greater impact on wages for unskilled laborers. Not controlling for SGRY underestimates the impact on wages for skilled labor by 47 percent. 4.2. Impact on Casual Earnings I now estimate a baseline model on casual earnings with NSS data. Here, I estimate the impact of NREGA on daily casual earnings by comparing the growth in the outcome variable over time between districts that received NREGA early (before 2008) to those that received it late (from 2008). Similar to Imbert and Papp (2015), I estimate equation (3): log(wi,d,t ) = α + β NREGAd,t + δ Zd × 1{t >2006} + γ Xd,t + λXd,t × 1{Early} + μHi + θt + αd + υi,d,t , (3) where log (wi,d,t ) refers to the log average daily earnings in casual work for individual i surveyed in district d in quarter t. Also, Zd are district controls like rainfall, agricultural productivity, etc.16 District controls that do not vary over time are interacted with a dummy 1{t >2006} for 2007–08 (post-NREGA). To ease concerns that NREGA’s impact on wages is not driven by worker selection, I control for individual controls Hi . The individual-level controls include dummy variables for age group, education level, gender, caste, religion, and marital status. Further, Xd,t represents time-varying district control like rainfall, which is also interacted with an indicator 1{Early} equal to 1 for observations within early districts, and θ t represents year-quarter fixed effects. All other variables have the same interpretation as equation (1).17 Following Imbert and Papp (2015), I include interactions of NREGAd,t with season dummies to exploit the variation in public employment provision across seasons. Table 2 reports the results. Panels A and B report regressions where the dependent variable is nominal earnings and real earnings, respectively. In both panels, columns 1, 2, and 3 report NREGA’s impact on the dependent variable without any additional control, with worker controls, and with worker and district controls, respectively. Columns 4, 5, and 6 report estimates from the same specification as columns 1, 2, and 3, respectively but with SGRY expenditure in district d at time t as an additional control. This control takes the value 0 once NREGA covers a district. The key regressors in all the regressions are the interaction of NREGAd,t with Dry and Rainy indicators for the first six months and the last six months of a calendar year, respectively. Consistent with findings reported in Imbert and Papp (2015), NREGA’s effect on private earnings in the early-phase districts is significantly positive (column 3, panels A and B) during the dry/lean agricultural season when the demand for workers in the private sector (public works) is low (high). The effect on earnings during the rainy/peak agricultural season is positive but insignificantly different from zero (column 3, panels A and B). 15 Wages for these occupations are reported only for men. Skilled wage is taken as the average across the three occupations. 16 See table 2 for a full list of district and worker controls. 17 Strictly speaking, I do not replicate results from Imbert and Papp (2015) as I do not control for some additional district- level controls that are constructed using data that is not freely available. This, however, is not a concern as my baseline NSS results are close to the results reported by Imbert and Papp (2015) and the key objective of this exercise is to compare the change in results once we control for SGRY expenditure. The World Bank Economic Review 527 Table 2. Effect of NREGA on Earnings Using NSS Data Panel A. Dependent variable: Nominal earnings Without SGRY control With SGRY control NREGAd,t × Dry 4.497** 4.310* 4.173** 6.794*** 6.873*** 7.052*** [2.218] [2.225] [2.071] [2.441] [2.438] [2.202] Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 NREGAd,t × Rainy 3.540 3.590* 3.631* 4.835** 5.035** 5.261** [2.234] [2.157] [1.982] [2.322] [2.254] [2.049] Observations 59,130 59,130 59,130 59,130 59,130 59,130 Worker controls No Yes Yes No Yes Yes District controls FEs No No Yes No No Yes SGRY control No No No Yes Yes Yes Panel B. Dependent variable: Real earnings Without SGRY control With SGRY control NREGAd,t × Dry 4.494** 4.308** 4.909** 6.540*** 6.621*** 7.487*** [2.175] [2.176] [2.016] [2.411] [2.400] [2.162] NREGAd,t × Rainy 2.345 2.389 3.099 3.498 3.692 4.558** [2.257] [2.184] [1.987] [2.351] [2.284] [2.061] Observations 59,130 59,130 59,130 59,130 59,130 59,130 Worker controls No Yes Yes No Yes Yes District controls FEs No No Yes No No Yes SGRY control No No No Yes Yes Yes Source: Author’s analysis based on National Sample Surveys (NSS) 2004–2008 (rounds 61 and 64) and program expenditure data for SGRY from 2004 to 2007. Program expenditure data are from the Ministry of Rural Development, Government of India. Note: All estimates are of order 10−2 . Each column presents results from a separate regression. All regressions include district and year-quarter fixed effects. The dependent variable in panel A is the log of nominal daily earnings in casual work. The dependent variable in panel B is the log of real daily earnings in casual work. The sample is composed of all adults aged 18 to 60 interviewed from July 2004 to June 2005 and from July 2007 to June 2008. Real earnings are deflated using the monthly, state-level price index for agricultural laborers from the Indian Labour Bureau. The variable NREGAd,t is a dummy equal to 1 for early districts from July 2007 to June 2008. The variable Dry is a dummy equal to 1 for the first two quarters of the year. The variable Rainy is a dummy equal to 1 for the second two quarters of the year. Worker controls include dummy variables for gender, age group, education levels, caste, religion, and marital status. District controls are rainfall, agricultural productivity, fraction of workers who are categorized as casual (agriculture), casual (nonagriculture), cultivators, business (nonagriculture), and salaried. District controls that do not vary over time are interacted with a dummy for 2007–2008 (post-NREGA). All estimates are computed using sampling weights. The standard errors in square brackets are clustered at the district level. SGRY: Sampoorna Grameen Rozgar Yojana. NREGA: National Rural Employment Guarantee Act. *p < 0.10, **p < 0.05, ***p < 0.01 The results reported in column 3, panel B show real daily casual earnings to be approximately 4.9 (3.1) log points more in early relative to late districts during the dry (rainy) season. These results match very closely with the 4.7 (2.9) log points increase during the dry (rainy) season in Imbert and Papp (2015). As columns 4–6 (panels A and B) show, controlling for SGRY expenditure substantially increases both the size and significance of NREGA’s impact on daily casual earnings during dry and rainy seasons for all specifications. Comparing the results reported in column 6 and column 3, not controlling for SGRY underestimates NREGA’s impact on earnings in the dry season by approximately 40 percent and 34 percent for nominal and real earnings, respectively. The program impact during the rainy season is similarly underestimated in the specifications without SGRY by approximately 31 percent and 32 percent for nominal and real earnings, respectively. Hence, the program impact is substantially underestimated in tables 1 and 2 when we do not control for SGRY.18 Given the large sampling variability (standard errors), the coefficients in the specification with 18 Note, the estimates obtained from AWI and NSS data are different and they need not be the same. First, the NSS data are of lower frequency relative to AWI data. Small annual changes in wages may compound when the treatment and 528 Bahal SGRY are not statistically different from the corresponding specification without SGRY in tables 1 and 2. This does not undermine the relevance of controlling for SGRY for two reasons. First, the omitted variable bias for both outcomes is economically large, which warrants regressions with the SGRY control as the preferred specification. Second, the estimates with and without SGRY control are different in a statistical sense as well. For example, in table 2, while the impact of NREGA on real earnings during the dry season is statistically different from 0 in column 3, the coefficient is not statistically different (at the 5 percent Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 level) from 1. On the other hand, the same coefficient in column 6 is statistically different (at the 5 percent level) from 3, implying that real earnings increased by at least 3 percentage points during the dry season. In the supplementary online appendix, table S4.4 compares the effect of NREGA on star states that implemented NREGA well relative to all other states during the dry and rainy seasons (see Imbert and Papp 2015 for the definition of star states). Overall, the results without SGRY are consistent with Imbert and Papp (2015). The specifications with SGRY remain more pronounced in all cases and the extent of underestimation (without SGRY) is greatest for other states in the dry season. 4.3. Impact on Public and Private Employment This section compares how controlling for SGRY affects NREGA’s impact on public and private employment outcomes. I estimate various specifications of the following equation (4): Empi,d,t = α + β NREGAd,t + δ Zd × 1{t >2006} + γ Xd,t + λXd,t × 1{Early} + μHi + θt + αd + υi,d,t , (4) where all controls have the same interpretation as equation (3). The outcome variable Empi,d,t can be the percentage of days in the past seven days that an individual i in district d at time t spent in each of the two mutually exclusive activities: private sector work and public works. Private sector work includes waged work, self-employment, and domestic work. Table 3 reports the results. Panels A and B report results with the dependent variable as public and private employment, respectively. Focusing on columns 1–3, NREGA increases public employment by approximately 1 percentage point in the dry season and decreases private employment by approximately 1.9 percentage points. The program’s impact during the rainy season is small and insignificant for both employment outcomes. These results are broadly consistent with Imbert and Papp (2015). As can be seen from columns 4–6, the impact on both outcome variables is substantially more pronounced once we control for SGRY. Comparing column 6 with column 3, not controlling for SGRY underestimates (in absolute terms) NREGA’s impact on public employment by approximately 25 percent and private employment by 34 percent in the dry season. The impact on both outcome variables during the rainy season is similarly more pronounced after controlling for SGRY. In panel A, the coefficient for NREGAd,t × Rainy with all controls and SGRY is 0.35, which is significantly different from 0 at the 1 percent level). The coefficient for NREGAd,t × Rainy in panel B is more negative in column 6 (relative to column 3), but the estimate is not significantly different from 0. All estimates of column 6 are statistically different from the corresponding estimates in column 3 at the 1 percent level. Tables S4.5 and S4.6 in the supplementary online appendix show table 3 separately for men and women, respectively. The results continue to be more pronounced after controlling for SGRY for the subsamples split by gender. 4.4. Impact on Human Capital Outcomes Finally, I estimate the impact of human capital outcomes in terms of school enrollments and child labor. It has been established in the literature that income effects result in higher investment in control districts are compared over a few years. Second, the AWI data reports agricultural wages, while the NSS data provides information on income from casual work. The two measures, while correlated, are not necessarily the same. The World Bank Economic Review 529 Table 3. Effect of NREGA on Public and Private Work Panel A. Dependent variable: Public employment Without SGRY control With SGRY control NREGAd,t × Dry 0.982*** 0.970*** 0.981*** 1.313*** 1.298*** 1.316*** [0.267] [0.266] [0.271] [0.271] [0.270] [0.280] Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 NREGAd,t × Rainy 0.194** 0.188** 0.185* 0.351*** 0.345*** 0.345*** [0.077] [0.077] [0.100] [0.090] [0.089] [0.112] Observations 315,481 315,481 315,481 315,481 315,481 315,481 Worker controls No Yes Yes No Yes Yes District controls FEs No No Yes No No Yes SGRY controls No No No Yes Yes Yes Panel B. Dependent variable: Private employment Without SGRY control With SGRY control NREGAd,t × Dry −1.868*** −1.970*** −1.790** −2.780*** −2.859*** −2.700*** [0.710] [0.695] [0.720] [0.773] [0.753] [0.784] NREGAd,t × Rainy −0.291 −0.400 −0.168 −0.726 −0.824 −0.603 [0.707] [0.629] [0.688] [0.744] [0.667] [0.723] Observations 315,481 315,481 315,481 315,481 315,481 315,481 Worker controls No Yes Yes No Yes Yes District controls FEs No No Yes No No Yes SGRY controls No No No Yes Yes Yes Source: Author’s analysis based on National Sample Surveys (NSS) 2004–2008 (rounds 61 and 64) and program expenditure data for SGRY from 2004 to 2007. Program expenditure data are from the Ministry of Rural Development, Government of India. Note: All estimates are of order 10−2 . Each column presents results from a separate regression. All regressions include district and year-quarter fixed effects. All dependent variables are in logs. The sample is composed of all adults aged 18 to 60 interviewed from July 2004 to June 2005 and from July 2007 to June 2008. The dependent variable in panel A is the percentage of days in the past seven days that an individual spent in public works. The dependent variable in panel B is the percentage of days in the past seven days that an individual spent in private works. All other controls are the same as in table 2. All estimates are computed using sampling weights. The standard errors in square brackets are clustered at the district level. SGRY: Sampoorna Grameen Rozgar Yojana. NREGA: National Rural Employment Guarantee Act. *p < 0.10, **p < 0.05, ***p < 0.01 education when returns to education are higher (Jacoby and Skoufias 1997; Jensen 2000; Bharadwaj, Lakdawala, and Li 2020; Maccini and Yang 2009). On the other hand, there is increasing evi- dence that increases in low-skill wages can decrease investment in human capital as adolescents substitute education with work to benefit from higher wages (Atkin 2016; Shah and Steinberg 2017; Cascio and Narayan Forthcoming; Charles, Hurst, and Notowidigdo 2018). The direction and magni- tude of this effect are relevant for policy as public workfares are a popular means of redistribution in developing economies. A recent and growing literature on NREGA has examined how NREGA has affected human capital outcomes. Using Young Lives data from Andhra Pradesh (one state), Afridi, Mukhopadhyay, and Sahoo (2016) and Mani et al. (2020) find NREGA to increase human capital investment. On the other hand, Li and Sekhri (2020), Islam and Sivasankaran (2015), and Shah and Steinberg (2021) conclude, using nationally representative data sets, that school enrollment numbers declined while child labor increased due to the spillover effects of NREGA. Using District Information System for Education (DISE) and Annual Status of Education Report (ASER) data, Adukia (2020) also finds small negative effects of NREGA on educational outcomes but concludes the magnitude of these spillovers to be inconsequential, especially relative to the positive spillovers on adult employment outcomes.19 19 Das (2018) finds a positive impact of higher days of work and earnings on expenditure on private coaching. 530 Bahal Table 4. Effect of NREGA on School Attendance and Work Without SGRY control With SGRY control Attends school Works Attends school Works Panel A: Full sample NREGA −1.097 1.808*** −1.275* 1.863*** Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 [0.718] [0.495] [0.748] [0.516] Observations 238,479 238,479 238,479 238,479 Mean DV 0.80 0.11 0.80 0.11 Panel B: Ages 13–17 NREGA −3.541*** 4.195*** −3.693*** 4.360*** [1.065] [1.003] [1.119] [1.054] Observations 84,619 84,619 84,619 84,619 Mean DV 0.70 0.25 0.70 0.25 Panel C: Ages 5–12 NREGA 0.202 0.677* 0.056 0.609 [0.787] [0.366] [0.805] [0.384] Observations 153,860 153,860 153,860 153,860 Mean DV 0.85 0.027 0.85 0.027 District FEs Yes Yes Yes Yes Year FEs Yes Yes Yes Yes Age FEs Yes Yes Yes Yes Source: Author’s analysis based on National Sample Surveys (NSS) 2004–2010 (rounds 61, 64, and 66) and program expenditure data for SGRY from 2004 to 2007. Expenditure data are from the Ministry of Rural Development, Government of India. Note: All estimates are of order 10−2 . This table reports estimates of β , the effect of NREGA on children who report their “primary activity” as school attendance or work. The coefficients are from the OLS estimation of equation (5). The dependent variable in columns 1 and 3 is a dummy if the primary activity of the individual is “attends school.” The dependent variable in columns 2 and 4 is a dummy if the primary activity of the individual is any kind of work. Other controls include district fixed effects, year fixed effects, and a vector of year-child-age fixed effects. The standard errors in square brackets are clustered at the district level. All regressions include district, year, age, and sex fixed effects. SGRY: Sampoorna Grameen Rozgar Yojana. NREGA: National Rural Employment Guarantee Act. *p < 0.10, **p < 0.05, ***p < 0.01. I replicate results from Shah and Steinberg (2021) to estimate NREGA’s impact on school enrollments and child labor using the following equation: Sidty = α + β NREGAdt + θt + αd + ψy + υidty , (5) where Sidty is an outcome of interest (such as enrollment status or child labor) for individual i in district d in year t who is age y, and ψ y is a vector of year-child-age fixed effects. All other controls have the same interpretation as before. The coefficient of interest is β , and it measures the effect of NREGA on the outcome variable S. Following Shah and Steinberg (2021), panels A, B, and C of table 4 report results for schooling and child labor for the full sample (children aged 5–17), adolescents (children aged 13–17), and young children (aged 5–12), respectively. Since SGRY data are not available for some states like Jammu and Kashmir, the (NSS and SGRY) matched data set is approximately 90 percent of the data used by Shah and Steinberg (2021). The comparison of results with and without SGRY is made on the matched sample so that any changes in coefficients can be attributed to the presence or absence of the SGRY control and not to a change in observations.20 Consistent with Shah and Steinberg (2021), NREGA decreases school enrollments in the full sample by 1.1 percentage points and increases child labor by 1.8 percentage points. The results are mostly driven by the adolescents aged 13–17 while there are no consequential spillovers on young children aged 20 The “without SGRY” results reported in table 4 are essentially the same as the results reported in table 2 of Shah and Steinberg (2021). The World Bank Economic Review 531 5–12. Encouragingly, controlling for SGRY makes the impact on school enrollments and child labor more pronounced in the relevant samples (panels A and B). The extent of underestimation of coefficient estimates without SGRY, however, is not as large as those reported in tables 1, 2, and 3. In panel B, for example, the impact on schooling and child labor is underestimated by only 3–4 percent. The smaller “correction” in the presence of SGRY is expected since NREGA’s spillover on adults’ outcomes is much more pronounced relative to outcomes for children (see Adukia 2020 for a detailed discussion on this). Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 5. Conclusion New antipoverty programs implemented by governments across the world often have similar predecessor programs. Taking evidence from India’s public works programs, this article highlights the need to be cau- tious while using the initial rollout of “new” programs as quasi-experimental research designs. This article shows how ignoring an older public works program, SGRY, can substantially underestimate the general equilibrium effect of the new employment policy, NREGA, on a variety of outcomes. The underestimation of program impact can be attributed to the actual gap in employment provision between the treatment and control districts, which is lower than what is initially assumed. Using a novel dataset of program ex- penditure at the district level for SGRY, I find that ignoring the older program underestimates the general equilibrium impact of public workfares on labor-market outcomes for adults by 30–40 percent in most instances. This paper, therefore, shows how ignoring the continued existence of a similar older program can have first-order effects on measuring the true impact of the policy. A key area for future research is identifying the exact mechanisms through which public workfares affect the private labor market. 6. Data Availability Statement The data on SGRY was provided by the Ministry of Rural Development, Government of India. The SGRY data will be shared on request to the corresponding author with permission from the Ministry of Rural Development. All other data underlying this article will be shared on reasonable request to the corresponding author. References Adukia, A. 2020. “Spillover Impacts on Education from Employment Guarantees.” Education Finance and Policy. https://direct.mit.edu/edfp/article/doi/10.1162/edfp_a_00323/97135/Spillover-Impacts-on-Education-from- Employment Afridi, F., A. Mukhopadhyay, and S. Sahoo. 2016. “Female Labor Force Participation and Child Education in India: Evidence from the National Rural Employment Guarantee Scheme.” IZA Journal of Labor and Development 5 (7): 164–78. Altonji, J. G., T. E. Elder, and C. R. Taber. 2005. “Selection on Observed and Unobserved Variables: Assessing the Effectiveness of Catholic Schools.” Journal of Political Economy 113 (1): 151–84. Angrist, J. D., and J.-S. Pischke. 2014. Mastering ’Metrics: The Path from Cause to Effect. Princeton University Press. Atkin, D. 2016. “Endogenous Skill Acquisition and Export Manufacturing in Mexico.” American Economic Review 106 (8): 2046–85. Azam, M. 2012. “The Impact of Indian Job Guarantee Scheme on Labor Market Outcomes: Evidence from a Natural Experiment.” IZA Discussion Paper No. 6548. Bahal, G. 2016. “Employment Guarantee Schemes and Wages in India.” Cambridge Economics Working Paper No. 1626. ———. 2020. “Estimating the Impact of Welfare Programs on Agricultural Output: Evidence from India.” American Journal of Agricultural Economics 102 (3): 982–98. Banerjee, A. V., and E. Duflo. 2007. “The Economic Lives of the Poor.” Journal of Economic Perspectives 21 (1): 141–68. 532 Bahal Berg, E., S. Bhattacharyya, R. Durgam, and M. Ramachandra. 2018. “Can Public Works Increase Equilibrium Wages? Evidence from India’s National Rural Employment Guarantee.” World Development 103: 239–54. Bharadwaj, P., L. K. Lakdawala, and N. Li. 2020, 11. “Perverse Consequences of Well Intentioned Regulation: Evidence from India’s Child Labor Ban.” Journal of the European Economic Association 18 (3): 1158–95. Cascio, E. U., and A. Narayan. Forthcoming. “Who Needs a Fracking Education? The Educational Response to Low-Skill-Biased Technological Change.” ILR Review. https://journals.sagepub.com/doi/abs/ 10.1177/0019793920947422?journalCode=ilra. Downloaded from https://academic.oup.com/wber/article/36/2/514/6364496 by LEGVP Law Library user on 08 December 2023 Charles, K. K., E. Hurst, and M. J. Notowidigdo. 2018. “Housing Booms and Busts, Labor Market Opportunities, and College Attendance.” American Economic Review 108 (10): 2947–94. Das, S., and A. Singh. 2013. “The Impact of Temporary Work Guarantee Programs on Children’s Education: Evidence from the Mahatma Gandhi National Rural Guarantee Act from India.” Working Papers 13-03, UW-Whitewater, Department of Economics. Das, U. 2018. “Rural Employment Guarantee Programme in India and Its Impact on Household Educational Deci- sions: A Focus on Private Coaching.” Unpublished. Drèze, J. 1990. “Famine Prevention in India.” In The Political Economy of Hunger, edited by J. Drèze and A. Sen, 13–122. Oxford University Press. Dutta, P., R. Murgai, M. Ravallion, and D. van de Walle. 2012. “Does India’s Employment Guarantee Scheme Guar- antee Employment?” World Bank Policy Research Working Paper no. 6003. Fetzer, T. 2020. “Can Workfare Programs Moderate Conflict? Evidence from India.” Journal of the European Eco- nomics Association 18(6): 3337–75. Hoynes, H., M. Page, and A. H. Stevens. 2011. “Can Targeted Transfers Improve Birth Outcomes?: Evidence from the Introduction of the WIC program.” Journal of Public Economics 95 (7): 813–27. Imbert, C., and J. Papp. 2015. “Labor Market Effects of Social Programs: Evidence from India’s Employment Guar- antee.” American Economic Journal: Applied Economics 7 (2): 233–63. Islam, M., and A. Sivasankaran. 2015. “How Does Child Labor Respond to Changes in Adult Work Opportunities? Evidence from Nrega.” Unpublished. Jacoby, H. G., and E. Skoufias. 1997. “Risk, Financial Markets, and Human Capital in a Developing Country.” Review of Economic Studies 64 (3): 311–35. Jensen, R. 2000. “Agricultural Volatility and Investments in Children.” American Economic Review 90 (2): 399–404. Li, T., and S. Sekhri. 2020, 08. “The Spillovers of Employment Guarantee Programs on Child Labor and Education.” World Bank Economic Review 34 (1): 164–78. Maccini, S., and D. Yang. 2009, June. “Under the Weather: Health, Schooling, and Economic Consequences of Early- Life Rainfall.” American Economic Review 99 (3): 1006–26. Mani, S., J. R. Behrman, S. Galab, P. Reddy, Y. L. Determinants, and C. of Child Growth Project Team. 2020. “Impact of the NREGS on Children’s Intellectual Human Capital.” Journal of Development Studies 56 (5): 929–45. Muralidharan, K., P. Niehaus, and S. Sukhtankar. 2016. “Building State Capacity: Evidence from Biometric Smartcards in India.” American Economic Review 106 (10): 2895–929. ———. 2017. “General Equilibrium Effects of (Improving) Public Employment Programs: Experimental Evidence from India.” Working Paper 23838, National Bureau of Economic Research. Oster, E. 2019. “Unobservable Selection and Coefficient Stability: Theory and Evidence.” Journal of Business & Economic Statistics 37 (2): 187–204. Özler, B., G. Dutt, and M. Ravallion. 1996. “A Database on Growth and Poverty in India.” The World Bank. Ravallion, M., G. Datt, and S. Chaudhuri. 1993. “Does Maharashtra’s Employment Guarantee Scheme Guarantee Employment? Effects of the 1988 Wage Increase.” Economic Development and Cultural Change 41 (2): 251–75. Shah, M., and B. M. Steinberg. 2017. “Drought of Opportunities: Contemporaneous and Long-Term Impacts of Rainfall Shocks on Human Capital.” Journal of Political Economy 125 (2): 527–61. ———. 2021. “Workfare and Human Capital Investment: Evidence from India.” Journal of Human Resources 56 (2): 380–405. Sukhtankar, S. 2017. “India’s National Rural Employment Guarantee Scheme: What Do We Really Know about the World’s Largest Workfare Program?” Brookings-NCAER India Policy Forum 13: 231–86. Zimmermann, L. 2012. “Labor Market Impacts of a Large-Scale Public Works Program: Evidence from the Indian Employment Guarantee Scheme.” IZA Discussion Paper No. 6858.