Spatially heterogeneous effects of a public works program

Accepted Manuscript Spatially heterogeneous effects of a public works program Joshua D. Merfeld PII:

S0304-3878(18)30478-4

DOI:

https://doi.org/10.1016/j.jdeveco.2018.10.007

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DEVEC 2299

To appear in:

Journal of Development Economics

Received Date: 3 August 2017 Revised Date:

8 September 2018

Accepted Date: 25 October 2018

Please cite this article as: Merfeld, J.D., Spatially heterogeneous effects of a public works program, Journal of Development Economics (2018), doi: https://doi.org/10.1016/j.jdeveco.2018.10.007. This is a PDF file of an unedited manuscript that has been accepted for publication. As a service to our customers we are providing this early version of the manuscript. The manuscript will undergo copyediting, typesetting, and review of the resulting proof before it is published in its final form. Please note that during the production process errors may be discovered which could affect the content, and all legal disclaimers that apply to the journal pertain.

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October 26, 2018

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Joshua D. Merfeld*

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Spatially Heterogeneous Effects of a Public Works Program

Abstract

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Most research on labor market effects of the Mahatma Gandhi National Rural Employment Guarantee Scheme focuses on outcomes at the district level. This paper shows that such a focus masks substantial spatial heterogeneity: treated villages located near untreated areas see smaller increases in casual wages than treated villages located farther from untreated areas. Spatial differences in implementation or program leakages do not appear to drive this spatial heterogeneity. The effects of the program on private-sector employment display similar intra-district heterogeneity and these effects on employment are highly correlated with the effect on wages. Overall, these results suggest that worker mobility leads a district-level focus to underestimate the true effect of the program on wages. Quantifying this underestimate using two separate methods produces very similar results; the overall effect on wages appears to be approximately twice as large as district-level estimates suggest.

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Keywords: India, Public Works, Labor, Wages, Spillovers JEL Codes: D50, H53, I38, J38, J46

* Robert F. Wagner Graduate School of Public Service, New York University; [email protected]. Conversations with and comments from Leigh Anderson, Justin Downs, James Long, Mark Long, Karthik Muralidharan, Katya Roshchina, and Jagori Saha were extremely helpful. I also thank participants at various seminars and conferences for helpful comments and suggestions. I especially thank two anonymous referees for greatly improving this paper. Any remaining errors are my own.

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Spatially Heterogeneous Effects of a Public Works Program

Introduction

India’s Mahatma Gandhi National Rural Employment Guarantee Scheme (NREGS)1 , which

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was launched in 2006 and is now rolled out throughout the country, is the largest public works program in the world. In fiscal year 2015/16, the program generated more than two billion persondays of employment and amounted to more than two percent of the fed-

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eral government budget.2 Given the program’s size, it is perhaps unsurprising that it has spawned a vast body of literature.

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The program was phased in over three rounds, starting in 2006. However, this rollout was not randomized; the poorest districts were generally the first to receive the program. As such, while the phased rollout makes differences-in-differences attractive, the systematic differences in district characteristics make the identification assumption of parallel trends somewhat tenuous (Zimmermann, 2012; Sukhtankar, 2016). In addition, it is not clear what

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treatment effect estimates averaged over the entire country measure, as implementation of the program varies substantially from state to state and even from district to district (Liu and Barrett, 2012; Ravallion et al., 2013; Dutta et al., 2014; Banerjee et al., 2015; Imbert and Papp, 2015). In reality, these estimates are the net effect of the program, inclusive of

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implementation efficacy (Sukhtankar, 2016).

Despite these difficulties, a growing body of literature has analyzed the performance

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and far-reaching effects of the program. These include human capital investments (Afridi et al., 2012; Li and Sekhri, 2013; Shah and Steinberg, 2015; Merfeld and Saha, 2018), nutrition and consumption/income (Liu and Deininger, 2010; Jha et al., 2011; Ravi and Engler, 2015), and corruption (Imbert and Papp, 2011; Niehaus and Sukhtankar, 2013; 1

The program was originally passed as the National Rural Employment Guarantee Act in 2005 and implemented as the scheme starting in 2006. The program was renamed in 2009, but I use the old acronym throughout this paper. 2 Figures are from http://nrega.nic.in/, the official program website.

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Banerjee et al., 2015; Muralidharan et al., 2016). However, given the aims and scope of the program, much of the literature has focused on its labor market effects. While findings

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vary, there is broad agreement with one basic fact: the program led to a modest increase in prevailing casual wages in rural India (Azam, 2012; Berg et al., 2014; Imbert and Papp, 2015; Muralidharan et al., 2018; Sukhtankar, 2016).3

In addition to a common finding, much of the literature examining the effects of the

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program’s rollout on labor market outcomes shares another characteristic: it analyzes the effects of the program at the district level. This level of analysis is attractive for two rea-

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sons. First, the program was rolled out at the district level. Second, given low levels of rural-to-rural migration in India (Rosenzweig, 1988; Behrman, 1999; Anant et al., 2006; Munshi and Rosenzweig, 2009), districts are often considered to be relatively distinct labor markets. Empirical work in India has long focused on districts, especially for labor-market outcomes; for non-NREGS examples, see, for example, Rosenzweig (1978, 1984), Jay-

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achandran (2006), Topalova (2010), Kaur (2018), and Shah and Steinberg (2017). In this paper, I show that a district-level focus obscures substantial heterogeneity, with important policy implications. I use the Additional Rural Incomes Survey/Rural Economic

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Demographic Survey (ARIS/REDS), collected by the National Council of Applied Economics Research, to show that wage changes due to the program are spatially heteroge-

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neous. The first wave of the survey was collected prior to the implementation of NREGS and the second wave was collected between the second and third phases of the rollout. Importantly, unlike other datasets, I am able to identify the location of each village in the survey using GPS data.4 For each district, I construct two geospatial variables: whether phase one or phase two districts (“treated” districts) share a border with phase three dis3

In this context, “casual wages” refer to wages in daily markets for labor. The duration of this type of contract is generally only a day and the contract carries no expectation or promise of future work. 4 Throughout this paper, I refer to the location of a household and the location of a village interchangeably, though the GPS measurement is technically at the village level.

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tricts (“untreated” districts), and vice versa; and how long that border is. For districts that border a district of the opposite treatment status (“border districts”), I construct a variable

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for surveyed villages equal to their distance to the nearest district of the opposite treatment status.

In line with previous NREGS studies, I first show that phase one and two districts had much lower wage rates prior to implementation of the program than phase three districts

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(Zimmermann, 2012; Imbert and Papp, 2015). I then estimate the effects of NREGS by slowly restricting estimation to villages closer and closer to the border. While there are

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large effects on casual wages when all households are included in the estimation, the estimated effect starts to attenuate around 30-40 kilometers from the border between a treated and untreated district and the estimated effect completely disappears when looking only at households located within 15 kilometers of the border. I show that this general pattern holds for three separate specifications, including simple specifications as well as specifi-

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cations with a number of controls, including variables that determined the roll-out of the program. These patterns also hold when an alternative measure of labor market exposure – percentage of the area around an observation belonging to districts of the opposite treatment

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status – is used.

A preponderance of evidence suggests that treated areas closer to untreated areas have

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lower estimated wage increases than treated areas farther from untreated areas. In theory, if “wage arbitrage” is responsible, then these results could be indicative of bias in previous estimates for two reasons. First, district-level estimates may be underestimating the wage increase in treated districts. Second, district-level estimates may be overestimating the counterfactual wage increase in untreated districts. Interestingly, I find evidence of only the first possibility. I attempt to quantify the bias in previous estimates in two separate ways. First, I estimate the effect for households located more than 20 kilometers from a

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district of the opposite treatment status. Second, I estimate the effect of NREGS on wage increases on districts that do not border districts of the opposite treatment status at all.

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These two different methods produce almost identical estimates. Both suggest previous estimates of the wage increase are about half as large as the true effect of the program on prevailing rural wages.

A number of additional results suggest that this effect is not an artifact of pre-existing

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trends. First, I find insignificant overall effects of the program on private-sector employment. However, this finding again masks substantial heterogeneity: the effects on private

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employment appear to mirror the effects on wages, with interior areas seeing decreases in private employment relative to border areas. Moreover, the spatial patterns themselves are almost identical for both wages and employment, as the effects have a correlation of −0.792. I show that there were no differential pre-program trends in employment across treated and untreated districts, suggesting the spatial heterogeneity is driven by the program

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itself. Further evidence suggests better program implementation is not responsible for spatial heterogeneity. Finally, changes in individual characteristics are indicative of decreased migration of men, more educated individuals, and older individuals. These changes are

2018).

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consistent with the estimated wage heterogeneity caused by the program (Imbert and Papp,

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This paper contributes to three separate bodies of literature. First, I provide further evidence of the broad labor-market impacts of NREGS (Azam, 2012; Zimmermann, 2012; Berg et al., 2014; Imbert and Papp, 2015; Muralidharan et al., 2018) as well as public works programs, more generally (see, e.g., Subbarao et al. (2003) and Beegle et al. (2017)). However, unlike most previous studies, I am able to explore the spatially heterogeneous impacts of the rollout of the program. Consistent with the literature, I find overall increases in the wage rate. However, I also find that the estimated increase disappears at the border with

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untreated districts. In addition, some previous research finds that NREGS had a larger impact on female wages than male wages (Azam, 2012). This study presents evidence that

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men are more likely to move towards wage increase than women. If true, district-level difference-in-differences estimates of the effect on male wages may be underestimating the true impact of the program more than the estimates of the effect on female wages, explaining part of the gender effects. Unfortunately, I do not have the power to test this explicitly,

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as I have relatively few female wage observations.

Second, this study sheds some light on the functioning of labor markets in India (Jay-

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achandran, 2006; Kaur, 2018). While spot markets for casual labor in India are generally assumed to work relatively well (Rosenzweig, 1980), it is unlikely that markets are complete (Rosenzweig, 1988; Behrman, 1999). These results suggest that labor is somewhat mobile. In addition, while the minimum wage is unlikely to bind or be enforced in many developing country contexts (Behrman, 1999), NREGS appears to operate as a de facto

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minimum wage, increasing the bargaining power of casual laborers (Basu et al., 2009). Moreover, recent research finds that NREGS decreases rural-to-urban migration in three states and that certain individuals are particularly likely to reduce migration in response to

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the program (Imbert and Papp, 2018). The results in this paper support that argument. Finally, I contribute to the literature on treatment effects and spillovers of public policy

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interventions in developing countries (Duflo, 2001; Miguel and Kremer, 2004; Angelucci and De Giorgi, 2009; Cunha et al., 2011). In particular, this study reinforces the importance of capturing general equilibrium effects when evaluating large public programs and that failure to do so may result in biased estimates of the program’s impact (Muralidharan et al., 2018). In addition, the focus on the district-level effects of NREGS theoretically underestimates the true effect of the program in two ways: the wage in untreated districts increases more in areas closer to treated districts than in areas farther from treated districts,

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while the wage in treated districts increases less in areas closer to untreated districts than in areas farther from untreated districts. The treatment effect we are interested in is the effect

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of the program on wages absent spillovers since the program will be expanded throughout the country. Yet, a district-level focus overestimates the counterfactual wage in untreated districts and underestimates the wage in treated districts, although the latter effect apparently dominates in the present study. This leads to an underestimate of the true wage effect

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of the program. With this in mind and insofar as increasing rural wages is an explicit goal of policymakers, NREGS may have been more effective than previously estimated.

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The closest paper to this one is Muralidharan et al. (2018), who study the randomized rollout of an improvement in the implementation of NREGS. They find similar spatial effects. Their paper is different in two important respects. First, their randomized intervention provides a cleaner identification strategy and cleaner estimates of the intervention’s impacts. Indeed, the biggest disadvantage of my approach is the inability to test for pre-program

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trends using a specification identical to that in this paper. However, they randomize improvements only in Andhra Pradesh. Since Andhra Pradesh consistently performs better than other states in implementation of NREGS (Banerjee et al., 2015; Imbert and Papp,

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2015), it is not clear whether their findings would translate to other Indian states. Second, they do not study the implementation of the program itself. Rather, they estimate the effects

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of a technological reform that improved implementation of the program. This study, on the other hand, examines the effects of the program when it is first rolled out. Given these differences, one might expect findings to differ. However, the patterns overall findings from both studies are largely similar, suggesting that the effects found in both studies are driven by mechanisms common to all of India and not specific to Andhra Pradesh.

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Spatially Heterogeneous Effects of a Public Works Program

The Program

The Mahatma Gandhi National Rural Employment Guarantee Act was passed in 2005 after

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“more than a decade of sustained high growth in GDP... was perceived not to have made a sufficient dent in poverty in the rural India” (Azam, 2012, p. 1). The program guarantees up to 100 days of employment to any rural household that requests it. Employment is varied,

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but is generally focused on improving productivity in rural areas by building infrastructure, including irrigation, roads, and land improvements (Liu and Deininger, 2010). Unlike previous workfare programs, NREGS is explicitly designed as an employment guarantee;

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a household has the right to demand – and receive – employment. However, in practice, supply-side constraints are often binding, resulting in substantial unmet demand (Ravallion et al., 2013; Dutta et al., 2014; Mukhopadhyay et al., 2015).

In order to demand employment, households must first apply for a job card. The house-

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hold applies for the card at the local Gram Panchayat (GP)5 and the card includes a picture of every household member eligible for the program. With this card in hand, household members can request employment. According to the design of the program, individuals request work from their local GP, and the legislation stipulates that work be assigned within

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five kilometers of the individual’s place of residence, otherwise a travel stipend is to be provided (Azam, 2012). If individuals do not receive employment within 15 days of re-

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questing it, they are eligible for unemployment allowance. However, underreporting of unemployment is common and unemployment compensation is rare (Sharma, 2009). The program’s design begets a relatively complicated funding structure. The federal government is responsible for all unskilled wages and 75% of skilled wages and materials, while states are responsible for the remaining 25% (Azam, 2012). As such, funding flows 5

The Gram Panchayat is the lowest level of administration in the Indian federal structure and generally consists of several villages.

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from the federal government to the state before being dispersed through lower administrative levels and eventually to the GP’s account, while funding requests from GPs to the state

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also flow through two separate administrative levels (Banerjee et al., 2015).6 Several specific features of the program are worth noting. First, the minimum wages set by the program7 are self-targeting and are relatively low (and the labor relatively difficult) so that only needy households will apply for employment. Nonetheless, program wages

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vary from state to state, and some wages were set above prevailing wage rates at the start of the program. In some cases, program wages were more than double the prevailing wage rate

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at the time, especially for women.8 Second, the program guarantees equal wages to both men and women and also mandates that a certain number of beneficiaries be women.9 In addition, childcare at worksites is required so that mothers with young children can participate in the program. However, many worksites do not adhere to this childcare requirement (Khawlneikim and Mital, 2016; Khera and Nayak, 2009; Reddy and Upendranadh, 2010;

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Sharma, 2009).

Given the demand-driven nature of the program, implementation is relatively decentralized, with employment and worksites started and administered by the GP. While the GP

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is the basis for employment generation, the program was rolled out at the district level, in three phases. Districts in the first phase received the program in 2006, districts in the

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second phase received the program in 2007, and districts in the third phase received the program in 2008. Given the phased rollout, the majority of research on the labor-market effects of NREGS utilize differences-in-differences. However, the rollout was not random6

GPs request funding from the block, which is one administrative level above the GP. Subsequently, the block forwards requests to the district, which then requests funding from the state pool. Banerjee et al. (2015) provide an excellent overview of this process. 7 The original legislation allows the states to define the program wage, as long as it is above the legislated minimum. 8 http://www.levyinstitute.org/pubs/EFFE/Mehrotra_Rio_May9_08.pdf 9 The legislation state that “priority shall be given to women in such a way that at least one-third of the beneficiaries shall be women who have registered and requested for work under this Act” (Ministry of Law and Justice, 2005, p. 14).

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ized. Rather, the Indian government assigned districts to phases based on a governmentconstructed rating, which resulted in the poorest districts generally receiving the program

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first (Zimmermann, 2012). While the rating used to assign districts to phases is not publicly available, underlying data used in the construction of this rating are available in the 2003 report from the Planning Commission (Planning Commission, 2003; cited in Zimmerman, 2012). These ratings show that earlier phase districts tended to be poorer and have more

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scheduled castes/tribes, lower agricultural productivity, and lower wages. As such, there are concerns regarding the identification assumption of differences-in-differences, that treated

of the program.

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Data and Methods

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districts and untreated districts had identical labor-market trends prior to implementation

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To analyze the effects of NREGS, I mainly use the Additional Rural Incomes Survey/Rural Economic Demographic Survey (ARIS/REDS), collected by the National Council of Applied Economic Research. The ARIS/REDS is a panel survey that has been conducted periodically since 1969. When first collected, the data was nationally representative, although

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it oversampled high-income households and areas suitable to green-revolution crops. However, with recent changes in demographics and administration, the data are no longer rep-

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resentative of the entire country (Foster and Rosenzweig, 2010). As such, I interpret the results as representative of overall spatial patterns – including ratios of magnitudes – but not as representative of the actual magnitude of effects. I use the fifth and sixth rounds of the survey – collected in 1999 and 2008, respectively – for my main analyses. Additionally, I use the Indian National Sample Survey to analyze pre-program trends. I make use of the 1999/2000 and 2004/05 waves of the data. Since the second wave of ARIS/REDS data (2008) was collected after implementation of 10

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the first two NREGS phases but before implementation of the third phase, I refer to phase one and phase two districts as “treated” districts and phase three districts as “untreated”

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districts. Figure 1 provides an overview of the phased rollout of NREGS along with the location of ARIS/REDS villages. There is a lot of geographic variation in the location of surveyed villages, with all of the major Indian states covered except Jammu and Kashmir. Since the main strategy of this paper is to compare villages near borders of treated

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and untreated districts, it is instructive to look at the geographic variation in this specific characteristic. In particular, there appears to be a concentration of villages located near

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the border between treated and untreated districts in the southern and central regions. On the other hand, treated villages far from untreated districts tend to be located in the eastern half of the country, while untreated villages far from treated districts tend to be in the northwestern region of the country.

Methods

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This paper employs differences-in-differences estimates to examine the effects of NREGS

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on wages. I estimate regressions of the form

yidt = αh + α1 N REGSd + α2 P ostt + α3 N REGSd × P ostt (1)

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+ Xidt + Zvdt + Dd × P ostt + States × P ostt + εidt ,

where yidt is the outcome of interest for individual i in district d in wave t; αh is household fixed effects; N REGSd is an indicator variable equal to one if the district is a treated (phase-one or phase-two) district; P ostt is an indicator variable for observations in the second wave, 2008; Xidt is a vector of time-variant individual controls, which in practice include just age, age squared, and gender; Zvdt is village characteristics, which include distance to district headquarters, distance to nearest road, distance to nearest town, and 11

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population density; Dd × P ostt is a vector of district controls – which include the preprogram wage, total border, total area, population, percent rural, percent scheduled caste,

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percent scheduled tribe, percent literate, labor force percentage, employment characteristics, and agricultural productivity – interacted with the post indicator to allow these characteristics to differentially affect trends in y; States × P ostt is state by wave fixed effects; and εidt is a conditional mean-zero error term. The inclusion of state by wave fixed effects

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means the post dummy is generally not interpretable (without significant context) and the dummy is thus omitted from tables. If households never moved, the household fixed ef-

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fects would absorb the NREGS dummy. However, there are some movers in the data. As such, the NREGS dummy is technically identified. However, there are very few households that move and these are clearly a very select subset of households. As such, the NREGS dummy is also difficult to interpret and is thus also omitted from tables for simplicity. I only present the main, district-level effects using the full specification. In the rest of the

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analyses, I include only age, age squared, gender, and state by wave fixed effects (along with household fixed effects).

The main goal of this paper is to estimate the effects of NREGS at different locations

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in a district. To isolate these difference, I restrict estimation to individuals living within a certain distance of the border. For example, after presenting results for all individuals,

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I then restrict estimation to only individuals within 50 kilometers of a border between a treated and untreated district. I then restrict estimation to only individuals within 40 kilometers, and so on. In general, I am not able to estimate effects at any distance less than 15 kilometers from the border; I discuss this more in the results section. An alternative strategy would be to estimate the effects of the program using different windows of distances from the border – for example, comparing households between 40 and 50 kilometers of the border, then households between 35 and 45 kilometers of the border, etc., all the way down to within six kilometers of the border. However, this strategy suffers from severe power 12

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issues and the sample size is simply not large enough to provide meaningful estimates. The coefficient of interest is α3 , which gives the difference-in-differences estimate of the

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effect of NREGS on outcomes. This coefficient captures the difference, across treatment status, in changes of each outcome at the district level. This implies a very specific assumption required for unbiased estimates of the effect of NREGS: the trends, across time, of outcomes in treated and untreated districts are identical in the absence of the program.

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In other words, if treated districts had not received the program, then treated and untreated districts would have had the same change, from 1999 to 2008, in each of the outcomes. I

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discuss possible failure of this assumption of difference-in-differences in the results section.

I employ two separate distance variables and present results using a triple interaction:10 yidt = αh + α1 N REGSd + α2 P ostt + α3 Distancev + α4 N REGSd × P ostt (2)

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+ α5 N REGSd × Distancev + α6 Distancev × P ostt + α7 Distancev × P ostt × N REGSd + εidt ,

where Distancev is the village-specific distance variable. These regressions allow an

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empirical estimate of how the effect of NREGS on the wage differs by distance.11 One of the distance variables I use is the distance of the border shared with districts of the

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opposite treatment status. In other words, for treated districts, the length of border shared with untreated districts is the key variable, while for untreated districts it is the length of border shared with treated districts. The assumption here is that treated districts surrounded by untreated districts should see a smaller wage effect than treated districts surrounded by other treated districts. This specification is used in two ways. First, it allows me to quantify 10 11

The non-interaction variables are omitted for simplicity of presentation. The triple interaction and all interactions with Post are included in tables for the same reasons listed above.

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the bias in previous estimates. Second, I am not able to empirically estimate pre-program trends with the ARIS/REDS data. In order to explore pre-program trends, I turn instead to

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data from the National Sample Survey (NSS), which is a nationally representative survey conducted by the Ministry of Statistics and Programme Implementation.12 Since these data are only aggregated to the district level, I am unable to measure distances to border for each village. Instead, I use this border length variable to explore pre-program trends.

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I construct several geovariables for use in this analysis. For each district in the country, I first assign it a value of treated (if in the first or second phase) or untreated (if in the third

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phase). I then construct a variable, which I call border district, that equals one if a treated district borders an untreated district or if an untreated district borders a treated district and zero otherwise. In other words, border district identifies borders across which there is a difference in treatment status in 2008. I then calculate the total distance of such borders for each district in the country.

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In order to estimate treatment heterogeneity, I estimate a series of regressions, restricting estimation based on distance to the nearest border. I begin by estimating regressions using all individuals. Then, I restrict estimation to only individuals living within a certain distance

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of the border (e.g. 50, 40, 30, etc.). I define this distance variable as follow: For all villages in treated border districts, I construct another variable equal to the distance from each

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village to the closest border with an untreated district. Similarly, for villages in untreated border districts, I construct this variable as the distance from each village to the closest border with a treated district. To analyze spatial heterogeneity in effects of the program, I will essentially be comparing differences-in-differences estimates of all villages compared to villages close to borders. Figure 2 presents a histogram of this variable across treated (NREGS) and untreated (non-NREGS) districts. 12

See http://mospi.nic.in/national-sample-survey-office-nsso.

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I define labor market exposure in a second way, as well. For each village in the data, I construct a circle with a radius of 20 kilometers whose center is the village. I then calculate

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the percentage of the area of the resulting circle that belongs to treated districts and the percentage of the area that belongs to untreated districts. For each village/individual, the resulting variable is the percent of the total area belonging to a district of the opposite treatment status. While we expect the wage increase to be smaller as the distance variable

be larger as the percentage of area decreases.

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gets smaller with the previous variable, with this variable, we expect the wage increase to

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I use two main variables to measure labor-market outcomes. The first is the wage. I construct this variable by including both casual agricultural and casual non-agricultural wages at the individual level. For individuals that worked more than one type of job, I sum hours worked and total remuneration (cash and in-kind) to create the wage variable. The other main labor-market outcome I use is private-sector employment. I construct this variable

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by including all days worked in casual labor, own-account agricultural labor, own-account non-farm labor, own-account livestock labor, construction/maintenance labor, household (non-leisure) labor, and other economic activities.

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Finally, I cluster standard errors at the district level in all regressions, despite the inclusion of household fixed effects. The program itself was implemented at the district level, so

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district-clustered standard errors provide a conservative estimate for the standard errors (Donald and Lang, 2007).

3.2

Summary Statistics

Summary statistics from 1999, prior to the program, are presented in Table 1. In Panel A, statistics are at the district level. There are 39 treated (phase one or two) districts and 33 untreated (phase three) districts in the ARIS/REDS data. Treated districts tend to be larger – 15

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geographically – and more rural than untreated districts. They also have a higher percentage of scheduled castes and scheduled tribes living in the district, suggesting treated districts

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may be worse off relative to untreated districts. This is confirmed by the literacy rate and wage rate, both of which are lower in treated districts. This is, of course, unsurprising, given that rollout was designed to give the poorest districts access to the program first.

Panel B presents summary statistics at the individual level for any individual with a valid

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wage observation in 1999. The first four variables are defined at the village level, but are presented at the individual level. Consistent with the rural nature of treated districts,

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individuals living in treated districts tend to be farther from the district headquarters, farther from the nearest road, and farther from the nearest town than individuals living in untreated districts. Treated individuals with a wage observation are slightly younger but are less likely to be male. Finally, again consistent with the district-level statistics, individual wages are

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Results

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lower in treated districts than in untreated districts.

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I begin by estimating a simple differences-in-differences of the district-level effect of the program on wages in Table 2. This specification is similar to previous estimates of the

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impact of NREGS on wages. The first three columns present estimates using household fixed effects, while the last three columns present estimates using district fixed effects. In the first and fourth columns, only age (and age squared) and gender are included in the regression. In the second and fifth columns, state by wave fixed effects are also included. Finally, in the third and sixth columns, an extended set of controls is added. These controls are detailed in the methods section above. The estimated effect of NREGS on wages is relatively similar, regardless of specifica-

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tion. Across all six columns, the estimated effect is between approximately 7.6 and 12.1 percent.13 This is slightly larger than previous estimates using the NSS (Imbert and Papp,

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2015) but slightly smaller than previous estimates using the same dataset as this paper (Liu and Deininger, 2010). Despite the fact that the estimated effect is smallest using the simplest specification, previous research has found that this specification may be biased due to violations of the parallel trends assumption. However, the inclusion of household

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fixed effects – instead of district fixed effects – should help alleviate some of these concerns. Moreover, the third column includes a number of controls that have been found

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to attenuate the pre-program trend (Imbert and Papp, 2015); since the estimated effect of NREGS does not change following the inclusion of these controls (in the household fixed effects specifications), this is suggestive evidence that pre-program trends may not be driving household-fixed-effect estimates of the effect of NREGS on wages.14 To explore whether the district-level estimate of the effect obscures spatial heterogeneity,

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I first present a graphical representation of wage changes from 1999 to 2008 in Figure 3. Only individuals located in border districts are included in the figure. The x-axis denotes the distance to the border between treated and untreated districts, with negative values indi-

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cating movements towards the interior of untreated districts and positive values indicating movements towards the interior of treated districts. A value of zero indicates the location

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of the border. The wage in 1999 is monotonically decreasing as we move from the interior of untreated districts – presumably the location of better-off households – towards the border and then towards the interior of of treated districts. It is well documented that wages 13

The Post dummies have been omitted for simplicity. In columns one and three, the post dummy is identified. However, in columns two and five, the post dummy takes on the value of one of the state/wave fixed effects, complicating its interpretation. Despite the inclusion of household fixed effects, the NREGS dummy is technically identified in all columns. However, this identification comes from just a handful of households that appear to have moved districts. Thus, the coefficient is imprecisely estimated and its interpretation is not clear. 14 If the estimate in the first column is indeed biased upwards and if we are able to control for the variables responsible for this bias, then the estimates in column two and three should actually be smaller, not larger.

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in treated districts were markedly higher before implementation of NREGS than wages in untreated districts. If the means are different, on average, across the treatment phases, then

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there is likely to be some type of gradient across districts, which is what we see in Figure 3. In 2008, we see a similar pattern in untreated districts; the wage is decreasing as we move towards the border. However, there is a clear difference in the pattern as we move towards the interior of treated districts; the wage seems to be increasing relative to 1999.

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Table 3 presents empirical estimates of this effect, using the same specification as column two of Table 2. The first column estimates the effect of NREGS when using all individuals

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with a wage observation. The estimate indicates that NREGS increased the wage in treated districts by around 9.5 percent relative to untreated districts. Each subsequent column restricts the sample to individuals located closer and closer to the border. The second column restricts estimation to only individuals located within 55 kilometers of the border, the third column to only individuals located with 45 kilometers of the board, and so on. The

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effect appears to attenuate as we restrict attention to households located closer and closer to the border. However, due to imprecision in the estimates and the fact that estimates jump around slightly as we restrict our sample, the actual empirical estimates are very sensitive

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to the exact cut-off used. While round numbers may be preferred for presentation, there is no empirical reason that 50 is a more appropriate choice than 49, for example.

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To help make the pattern clearer, Figure 4 presents the results graphically. The regressions in Table 3 were re-estimated at every cut-off between 15 and 50 kilometers. The estimated effect size at each cut-off is plotted against the distance. The first panel presents results using the simple specification (column one of Table 2); the second panel presents results using the state/wave fixed effects specification (column two of Table 2); and the third panel presents results using the extended controls specification (column three of Table 2). In all three cases, the spatial heterogeneity is clear: the estimated effect of the program at-

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tenuates as we restrict attention to individuals located closer to the border between treated and untreated districts.15 Moreover, consistent with the results in Table 2, the overall ef-

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fect appears to be smallest with the simple specification and the most imprecise (and also the largest) – as evidenced by substantial jumps in the estimated coefficients – with the extended controls specification. This motivates the use of the state by wave fixed effects specification for results in the remainder of this paper.

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The appendix presents three additional graphs to help contextualize these results. Figure A1 presents the effect when not restricting attention to only individuals living in border

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districts; the results are unchanged. Figure A2 shows the estimated effects of the program by phase, comparing phases one and three (first panel) and phases two and three (second panel). This substantially reduces power, but we see the same general spatial trend in both graphs. Finally, Figure A3 presents results within 15 kilometers to help clarify why the three graphs in Figure 4 stop at 15 kilometers. We start to see large jumps in the estimated

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effect based on sample restrictions. For example, restricting the sample from 13 to 12 kilometers causes the estimated effect to increase from just 0.03 to 0.2. Similarly, seven to six leads to a drop of more than 0.2 and going from six to five leads to an even larger drop. It

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appears that the ARIS/REDS does not have enough observations to reliably estimate effects within approximately 15 kilometers of the border.

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The previous results use the distance to border as a proxy for labor market exposure. Another possible proxy is the area around a village that is made up of a different district. In other words, if we construct a circle with a radius of 20 kilometers around each village, what percent of that circle belongs to a district of the opposite treatment status? In this case, a value of zero would indicate a village that is completely surrounded by districts of the same treatment status, while a value of one would indicate a village that is completely 15

In the first two panels, the effect is approximately zero within 15 kilometers. In the third panel, the coefficient is slightly larger than zero, but the standard error is larger than the coefficient, suggesting any differences from zero may be driven by imprecision.

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surrounded by districts of the opposite treatment status.16 Table 4 presents results based on restrictions using this radius variable. The first column again uses all observations. Each

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additional column restricts the sample to individuals with less and less of the surrounding area belonging to a district of the opposite treatment status. While we expected the effect to attenuate with the sample restriction in Table 3, we now expect the effect to increase as we restrict the sample. Indeed, this is exactly what we see. Similar to the previous

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results, however, the exact cut-off is important. Thus, Figure 5 again presents the results graphically. The first graph uses a radius of 20 kilometers while the second graph uses

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a radius of 30 kilometers. The pattern is again clear: more isolated villages (with values closer to zero) see larger estimated effects of NREGS on prevailing casual wages. To help quantify the effect of distance on the estimated impact of NREGS on wages, Table 5 presents results using two separate triple interactions. The first three columns include a triple interaction of Post×NREGS×Distance to other. The estimates in column

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one suggest that an increase of one kilometer is correlated with an increase in the estimated effect of NREGS on wages of approximately 0.3 percent. The mean distance is 26.2, which would suggest a wage increase approximately 7.9 percent higher at the mean distance than

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at the border. Importantly, the Post×NREGS dummy is the estimated effect of NREGS on individuals located at a distance of zero kilometers from the border. As we would expect,

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this coefficient is not significantly different from zero. The last three columns use a triple interaction of the Post×NREGS dummy with a new variable, which is the length of the district border shared with districts of the opposite treatment status. The intuition behind this variable is that treated districts surrounded by untreated districts should, ceteris paribus, see smaller wage increases than treated districts surrounded by other treated districts. This is meant to act as a third proxy of labor market exposure. Column four suggests that as the length of the border shared with dis16

The latter is of course not a realistic possibility, though the former is.

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tricts of the opposite treatment status increases – conditional on length of total border – the estimated effect of NREGS on casual wages decreases. The coefficient is marginally

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significant (p=0.113) with the conservative district-clustered standard errors. The mean length of the length variable is 1.86, which corresponds to 186 kilometers. For the mean treated district, the effect of NREGS on wages would be approximately 9.7 percent smaller (−0.052 × 1.86) than for a treated district without any exposure to untreated districts. This

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estimate is surprisingly close to the estimate using a completely different specification in column one. The Post×NREGS dummy is again the estimated effect of NREGS on wages

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for districts with a value of zero on the border shared variable. In contrast to column one, however, this is now the estimate of the effect of NREGS on wages for the most isolated districts. This is arguably the best estimate we have of the true effect of NREGS on wages, a point to which I return below.

Interestingly, columns two, three, five, and six suggest that the heterogeneity is driven

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completely by dynamics within treated districts. Column two shows the estimated wage change by distance to border for treated districts while column three shows the estimated change by distance to border for untreated districts only. The coefficient in column two

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is positive and significant, as expected, but the coefficient in column three is a preciselyestimated zero. The same dynamic is seen in columns five and six, though the coefficient in

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column six is at least in the predicted direction. It is not clear why this heterogeneity is only seen within treated districts and this finding deserves further analysis in future research. The results in columns two and three of Table 5 suggest that previous estimates might be underestimating the wage change due to the implementation of NREGS in treated districts. If true, then previous estimates of the impact of NREGS on wages are biased downwards. To quantify this bias, we need to isolate the effect of NREGS on wages in more “isolated” areas. It is not clear the best measure of isolation, but Table 6 presents two possibilities. The

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first column presents the overall, district-level effect of NREGS. As before, the estimated effect is around 9.5 percent. Column two estimates the effect only for individuals that

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are not located within 20 kilometers of a district of the opposite treatment status; in other words, a circle with a radius of 20 kilometers around that individuals does not contain a district of the opposite treatment status. The estimated effect is approximately twice as large in these areas as the district-level average suggests. The third-column estimates are

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identical to the triple interaction in column four of Table 5. The assumption here is that treated districts that do not share a border with untreated districts feel the full effect of

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NREGS on wages. As previously indicated, this effect is the Post×NREGS coefficient. Reassuringly, the estimated “true” effect is almost identical to the estimate in column two. To put bounds on the underestimate, the bottom row shows the difference in estimated effects along with a percentile 95-percent confidence interval constructed by bootstrapping the estimates 1,000 times. The bootstrap draws households within districts to be consis-

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tent with the inclusion of household fixed effects and the clustering of standard errors at the district level. In both columns two and three, the estimated “true” effect is larger – approximately twice as large – than the average effect in column one. In column two, the

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95-percent confidence interval suggests the underestimate could be as small as 0.018 but as large as 0.161. Given that the overall effects are slightly larger than previous estimates, the

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upper end of the confidence interval seems unlikely. Though the point estimate in column three is almost identical, the confidence interval is slightly larger due to larger standard errors (and almost includes zero at the 95-percent level).

4.1

Is This Finding Driven by Pre-Program Trends?

The fundamental issue in this paper is the inability to test for pre-program trends. Though the ARIS/REDS has another wave before 1999, it was collected in the early 80s and, as 22

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such, is unlikely to provide a valid estimate of any wage trends just before NREGS implementation. Therefore, in this section I present several pieces of circumstantial evidence

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that suggest pre-program trends are not responsible for the results. First, unlike previous studies, this paper uses household fixed effects in all specifications, which should help with identification. Second, Figure 4 shows similar heterogeneity, regardless of specification. In particular, the third column (“Extended Controls”) shows the

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results when a number of district- and household-level controls are included, including the variables that determined roll-out. Imbert and Papp (2015) show that these variables help

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mitigate differential pre-program trends. Using the National Sample Survey, I confirm this in Table A1. The first column shows the simple difference-in-differences estimator from the period 1999/2000 to 2004/05. As in Imbert and Papp (2015), the wage appears to be trending upwards in treated districts relative to untreated districts prior to the program. However, the inclusion of the district-level “Extended Controls” mitigates this problem, as

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show in column two. As such, the fact that the heterogeneity remains even conditional on these variables is suggestive evidence that trends are not responsible. Third, though there were differential pre-program trends in wages, that was not the case

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for days worked in casual employment. This is confirmed in columns three and four of Table A1 in the Appendix. Thus, if we see spatial heterogeneity in private-sector employ-

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ment, as well, we might attribute this to true effects instead of trends. Table 7 shows the effects of NREGS on private-sector employment at different distances to the border, similar to the estimated effects on wages in Table 2. Again, however, the exact choice of cut-off is important. Therefore, Figure 6 presents the effects graphically, at every possible cut-off. To facilitate comparison, Figure 6 also includes the effects on wages shown in Figure 4. The heterogeneity in private-sector employment is exactly as we would expect, with a more negative effect towards the interior of districts, where the wage increase was the largest.

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Moreover, just like wages, the estimated effect near the border is approximately zero. The effects on wages and days are also strongly correlated, with a correlation of −0.792. This

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is further evidence that the spatial heterogeneity is due to the program and not trends. Fourth, Table 6 presents two ways to quantify the bias in the district-level estimates of wage impacts. In particular, the third column reports estimates using the ARIS/REDS and the distance of shared borders between districts. Though I cannot test pre-program

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trends using distance to border with the NSS (since the dataset does not have geographic information available below the district level), I am able to estimate pre-program trends

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using the distance of shared border. I present these results in Appendix Table A2. Column one shows the triple interaction from 1999/2000 to 2004/05 using all districts available in the NSS. The second column restricts attention to just the districts also in the ARIS/REDS, while the third column restricts attention to just border districts in the ARIS/REDS. In all three cases, the triple interaction is positive and insignificant, the opposite of what we

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would expect if a violation of the parallel trends assumption were driving the results. This is again inconsistent with pre-program trends being responsible for the current results. Finally, another possibility is that the wage increase is largest on the interior of treated

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districts because NREGS may be better implemented there. In this case, the differences in wage effects would be true program effects, but they would not be due to spillovers of any

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kind. To test this possibility, Table 8 presents regressions of days in public works in 2008 on different distance variables. These regressions include district fixed effects instead of household fixed effects, since the variable is available only for 2008.17 The first column confirms that public works employment in 2008 was significantly higher in treated districts than in non-treated districts, as would be expected since NREGS was not yet implemented in the non-treated districts. 17

Recall that in a single wave, there is variation within the district in the distance variable but not within the household.

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The second and third columns present results using only NREGS districts. Interestingly, being located farther from an untreated district is negatively correlated with days in public

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works. If the spatial heterogeneity in wage changes were driven by differences in program implementation, we would likely see more days in public works, not less.18 Rather, this is more consistent with the wage increase itself. If NREGS wages are constant within a district, then, all else equal, we should see fewer days in public works where the prevailing

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private-sector wage is higher than where the prevailing wage is lower. The third column adds distance to the district headquarters. Though the coefficient is negative, it is small and

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insignificant. The mean distance to headquarters in treated districts is 53 kilometers, which is associated with a decrease in days of public works of just 2.2 percent. On the whole, these results are not consistent with differences in implementation being responsible for the observed spatial heterogeneity.

As expected, when we restrict estimation to untreated districts, the coefficients them-

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selves are very small in magnitude, though the coefficient on distance to headquarters is marginally significant in column three. Though there are other public works programs in India, none is as large as NREGS. As such, we would not expect to see any significant

Do We Observe Labor Movements?

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4.2

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correlations between distance variables and days in public works in untreated districts.

It appears that this spatial heterogeneity is driven at least partially by movements of labor. Figure 7 presents some individual characteristics (in 2008) and how they vary with distance to border in an attempt to identify some of these movements. The first three columns are personal characteristics that should be pre-determined – relative to the program, that is – for most adults. First, we see that the number of males (as a proportion of all adults) is 18

Note that workers do not need to work in the program for it to have a significant impact on wages (Basu et al., 2009). Rather, the program need only provide workers with a credible outside option.

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increasing as we move towards the interior of treated districts. One can construct a story in which this is consistent with a wage increase, but that story is not so clear for either

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age or primary education, neither of which shows a consistent spatial pattern. Age is first decreasing then increasing then decreasing, while primary education is increasing then decreasing. The last figure presents travel time to employment, which is available only for non-farm employment. Interestingly, travel time increases exactly where we see the

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gradient in the wage effect, around 30-40 kilometers from the border. Moreover, it then decreases towards the very interior of treated districts, which we might expect if the wage

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increase is largest there and residents do not need to travel to take advantage of the largest wage increases.

However, it is not necessarily the levels in 2008 that are of interest to the estimated wage effects, but rather the changes in these characteristics from 1999 to 2008. While this is not possible for non-farm travel time – which is only available in 2008 – Figure 8 presents

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difference-in-differences estimates of changes for the other three individual characteristics. There are clearer trends here than in the previous figure. In particular, it appears that the changes in male and primary education follow very similar patterns as the wage increase.

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Age also follows a similar pattern, though it is not as evident as for male or primary education. This is consistent with men and more educated individuals being more likely to

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remain behind to take advantage of the larger wage increase. It should be noted, however, that the patterns presented here are not consistent with the movement of labor causing the wage increase. Rather, we might expect an influx of men and/or educated workers, all else equal, to suppress prevailing wages rather than increase them. Though travel time to non-farm employment may be indicative of daily travel, demographic changes are not. Rather, demographic changes are presumably due to either changes in migration or changes in the types of people who are working for wages. The present

26

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results mirror recent research that finds NREGS reduces seasonal migration in three Indian states (Imbert and Papp, 2018).19 The authors, using a survey designed specifically

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to answer questions related to seasonal migration, find non-monetary costs of migration are especially important for individuals with more education and for older individuals. In other words, the authors argue NREGS may be especially likely to reduce migration of these individuals, which is exactly what I find. Despite historical low labor mobility in

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India (Munshi and Rosenzweig, 2009), these results nonetheless suggest wage increases may decrease out-migration. In addition, they further supports the contention that the wage

5

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heterogeneity documented in this paper is indeed caused by the program.

Conclusion

In this paper, I document the effects of the Mahatma Gandhi National Rural Employment

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Guarantee Scheme (NREGS) in India. In particular, I show that the effects of the program are spatially heterogeneous: treated areas located near untreated areas see smaller wages increases than treated areas located farther from untreated areas. In addition, this hetero-

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geneity does not appear to be driven by pre-program trends or program leakage. However, while the pattern is clear across all of the results presented, a small sample size and demanding empirical strategy suggest caution in interpreting the magnitude of the estimated

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effects.

These results suggest that previous studies of the effect of the program on wages underestimate the true effect of the program. This bias theoretically operates through two separate channels: an overestimate of the counterfactual wage in untreated districts and an underestimate of the counterfactual wage in treated districts, although the present results suggest the latter is more important. Quantifying the bias suggests that the true effect of NREGS 19

Those three states are Rajasthan, Gujarat, and Madhya Pradesh.

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on wages is approximately twice as large as previous estimates indicate. It appears that the

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effects of NREGS on wages may have been greater than previously believed.

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Tables

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Figure 1: NREGS Districts and ARIS/REDS Villages

Legend

ARIS/REDS Villages

NREGA Districts Phase

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N/A

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6

Phase 1 Phase 2 Phase 3

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Table 1: Summary Statistics (1999)

Panel A: District Level Total border Area

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Population (log)

Percent SC Percent ST Literacy rate Labor force participation rate Median wage (log rupees)

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Observations

Panel B: Individual Level Distance to district HQ (log km)

Distance to nearest road (log km)

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Distance to nearest town (log km) Village population density

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Male (yes = 1)

Wage (log rupees) Observations

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Percent rural

Age

5.42 (2.30) 8.88 (0.54) 14.67 (0.49) 0.80 (0.11) 0.18 (0.07) 0.10 (0.13) 0.54 (0.11) 0.41 (0.07) 4.17 (0.30) 39

(2) Non-NREGS Districts mean/sd

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(1) NREGS Districts mean/sd

3.72 (0.96) 0.52 (0.87) 2.44 (0.97) 0.94 (1.43) 33.72 (13.26) 0.61 (0.49) 4.09 (0.43) 2031

5.12 (2.06) 8.72 (0.72) 14.81 (0.48) 0.65 (0.17) 0.15 (0.06) 0.03 (0.06) 0.60 (0.10) 0.39 (0.06) 4.40 (0.33) 33

3.57 (0.93) 0.23 (0.62) 2.08 (1.06) 0.97 (1.28) 34.48 (13.15) 0.68 (0.47) 4.37 (0.40) 2043

All statistics are from prior to implementation of NREGS. Column one includes phase one and two districts while column two includes phase three districts. Panel A includes district-level variables: total border and area are constructed from GIS files, population through labor force participation are from the 2000 census, and median wage is constructed using the ARIS/REDS 1999 wave. Panel B includes individual-level variables in the 1999 ARIS/REDS.

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Figure 2: Histogram of Distance to Border

Distance to border is defined as the distance from the enumerated village to the closest border between a treated and untreated district.

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Table 2: Effect of NREGS on Wages

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Post×NREGS

(1) Model 1 0.076 (0.059) yes no no 9649

Age and Gender State/Wave FE Extended Controls Observations

Household FE (2) (3) Model 2 Model 3 0.095** 0.095* (0.045) (0.057) yes yes yes no no yes 9649 9649

(4) Model 4 0.075 (0.061) yes no no 9649

District FE (5) (6) Model 5 Model 6 0.121** 0.090 (0.052) (0.059) yes yes yes no no yes 9649 9649

Standard errors are in parentheses and are clustered at the district level in all columns. Post is defined as a dummy equal to one for the 2008 wave of the ARIS/REDS, between phases two and three of NREGS implementation. NREGS is defined as an individual that lives in a phase one or two district. Extended controls include both district-level variables and village-level variables. District-level variables are defined using either the 2000 census or the 1999 ARIS/REDS. These variables are constant across both waves and are thus interacted with the Post dummy to allow them to differentially affect trends. Village-level variables use the values from their respective waves and thus are not interacted with the Post dummy. * p<0.1 ** p<0.05 *** p<0.01

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Figure 3: Distance to Border and Wages - 1999 and 2008

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Distance to border is defined as the distance from the enumerated village to the closest border between a treated and untreated district. Negative values indicate untreated (phase three) districts and positive values indicate treated districts. In other words, more negative values indicate the interior of untreated districts, values close to zero indicate areas located near the border between a treated and untreated district, and more positive values indicate the interior of treated districts.

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Table 3: Effect of NREGS on Wages by Distance to Border

Post×NREGS

Age and Gender State/Wave FE Observations

(1) (2) All < 55 km 0.095** 0.058 (0.045) (0.042) yes yes yes yes 9649 7296

(3) < 45 km 0.056 (0.043) yes yes 6929

(4) < 35 km 0.037 (0.039) yes yes 6452

(5) < 25 km 0.017 (0.042) yes yes 5217

(6) < 15 km 0.001 (0.045) yes yes 3584

Standard errors are in parentheses and are clustered at the district level in all columns. Post is defined as a dummy equal to one for the 2008 wave of the ARIS/REDS, between phases two and three of NREGS implementation. NREGS is defined as an individual that lives in a phase one or two district. Distance to border is defined as the distance from the enumerated village to the nearest border between a treated and untreated district for border districts. * p<0.1 ** p<0.05 *** p<0.01

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Each point is the a difference-in-differences estimate of the effect of NREGS on wages for all households no farther than x kilometers from the border between a treated and untreated district. As an example, a point at 30 means that the regression was estimated for all households less than or equal to 30 kilometers from the border. The first figure reports results from column one in , the second figure reports results from column two in , and the third figure reports results from column three in .

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Figure 4: Effect of NREGS on Wages by Distance to Border

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Table 4: Effect of NREGS on Wages - Circles of Radius 20km

Post×NREGS Age and Gender State/Wave FE Observations

(3) < 0.2 pct 0.113* (0.061) yes yes 7336

(4) < 0.15 pct 0.143** (0.063) yes yes 6901

(5) < 0.1 pct 0.122* (0.061) yes yes 6604

(6) < 0.05 pct 0.132* (0.074) yes yes 6005

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(1) (2) All < 0.25 pct 0.095** 0.122** (0.045) (0.053) yes yes yes yes 9649 7633

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Figure 5: Effect of NREGS on Wages by Distance to Border - Circles

Each point is the a difference-in-differences estimate of the effect of NREGS on wages. The x variable is the percent of a circle of radius 20 kilometers (first figure) or 30 kilometers (second figure) – whose center is each household – that belongs to a district of the opposite treatment status. As an example, a point at 0.2 in the first figure means that the regression was estimated for all households with less than 20 percent of the area within 20 kilometers of the household belonging to a district of the opposite treatment status.

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Table 5: Effect of NREGS on Wages - Triple Interactions

Post×NREGS×Border with other

-0.052 (0.033)

0.001 (0.001)

0.005*** (0.001)

Post×Border with other Post×NREGS

0.024 (0.053) yes yes 8693

yes yes 4606

yes yes 4087

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Age and Gender State/Wave FE Observations

-0.000 (0.001)

0.006 (0.019) 0.185** (0.085) yes yes 9649

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Post×Distance to other

Border Shared w/ Other (km) (4) (5) (6) All NREGS Non-NREGS

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Post×NREGS×Distance to other

Distance to Other (km) (1) (2) (3) All NREGS Non-NREGS 0.003* (0.002)

-0.067* (0.037)

0.008 (0.016)

yes yes 5562

yes yes 4087

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Post×NREGS

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Table 6: Quantifying Bias in District-Level Wage Estimates (1) All 0.095** (0.045)

(2) Radius Area = 0 0.188** (0.082)

Post×NREGS×Border with other

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9649 Bias: Difference: 95-percent Bootstrap CI:

4605 Col(2) - Col(1) 0.093 (0.018, 0.161)

(3) Shared Border 0.185** (0.085) −0.052 (0.033) 0.006 (0.019) 9649 Col(3) - Col(1) 0.090 (0.001, 0.187)

Standard errors are in parentheses and are clustered at the district level in the top panel. In the bottom panel (Bias), confidence intervals are calculated by bootstrapping the estimator, with the bootstrap set up to draw households from within districts, consistent with household fixed effects and district-clustered standard errors. Column one is the simple difference-in-differences estimate (column two of Table 2), column two is the difference-in-differences estimate when restricting the sample to only households more than 20 kilometers from any border with a district of the opposite treatment status, and column three is column four of Table 5. * p<0.1 ** p<0.05 *** p<0.01

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Table 7: Effect of NREGS on Employment

Post×NREGS Age and Gender State/Wave FE Observations

(3) < 45 km −0.124 (0.092) yes yes 29279

(4) < 35 km −0.155 (0.095) yes yes 26828

(5) < 25 km −0.098 (0.115) yes yes 22010

(6) < 15 km 0.027 (0.122) yes yes 14941

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(1) (2) All < 55 km −0.066 −0.116 (0.096) (0.092) yes yes yes yes 38160 31026

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Standard errors are in parentheses and are clustered at the district level in all columns. The dependent variable is total days in private-sector employment. The specification is otherwise identical to column two of Table 2. * p<0.1 ** p<0.05 *** p<0.01

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Figure 6: Effect of NREGS on Wages and Employment

The figure presents the wage results from the middle figure in Figure 4 (dotted line) as well as results from identical specifications using (log of) days in private-sector employment as the dependent variable. The relevant sample includes all adults over 18 years of age. The restrictions in each column are based on the distance to border variable used in previous specifications.

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Table 8: Days in Public Works in 2008 and Distance to Border and HQ

Distance to other district (hundreds of km) Distance to district HQ (hundreds of km) Observations

Non-NREGS Districts (4) (5) Model 4 Model 5

-0.539** (0.249)

-0.021 (0.013)

17100

-0.513** (0.229) 0.137* (0.074) 17100

18212

-0.019 (0.012) -0.007* (0.004) 18212

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NREGS Districts (2) (3) Model 2 Model 3

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All (1) Model 1 0.071*** (0.015)

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Figure 7: Distance to Border and Individual Characteristics

Distance to border is defined as the distance from the enumerated village to the closest border between a treated and untreated district. Negative values indicate untreated (phase three) districts and positive values indicate treated districts. In other words, more negative values indicate the interior of untreated districts, values close to zero indicate areas located near the border between a treated and untreated district, and more positive values indicate the interior of treated districts.

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Figure 8: Distance to Border and Changes in Individual Characteristics

Each figure presents difference-in-differences estimates using the same methods as Figure 4 and Figure 6. The dependent variable (DV) in the top-left graph is whether the wage earner is male; the DV in the top-right graph is the age of the wage earner; and the DV in the bottom graph is whether the wage earner has a primary education or above.

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Appendix

State/Wave FE Extended Controls Observations

Days (log) (3) (4) Model 3 Model 4 0.011 -0.006 (0.016) (0.019) yes yes no yes 396604 336495

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Wage (log) (1) (2) Model 1 Model 2 0.032* -0.010 (0.019) (0.019) yes yes no yes 62269 57133

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Table A1: Simple Pre-Program Wage and Private Employment Trends (NSS)

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Table A2: Border Distance and Pre-Program Trends

Post×NREGS Post×Border with other

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Post×NREGS×Border with other

(1) All Districts

(2) ARIS Districts

0.011 (0.009) 0.007 (0.029) −0.009 (0.007) 62269

0.026 (0.018) −0.028 (0.053) −0.015 (0.014) 16155

(3) ARIS Border Districts 0.020 (0.021) −0.008 (0.067) −0.008 (0.018) 13682

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Standard errors are in parentheses and are clustered at the district level in all columns. All regressions include district fixed effects and use the National Sample Survey (NSS). The NSS waves used in this analysis come from 1999/2000 and 2004/05, prior to the implementation of the program. Border with Other is defined as the percentage of the district border shared with a district of the opposite treatment status, similar to the specification in column four of Table 5. Column one includes all NSS districts while column two restricts the sample to only districts also available in the ARIS/REDS and column three further restricts the sample to border districts. NSS sample weights are used in all regressions. * p<0.1 ** p<0.05 *** p<0.01

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Figure A1: Effect of NREGS on Wages by Distance to Border - All Districts

The figure is identical to the middle figure in Figure 4 but does not restrict the sample to only border districts.

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Figure A2: Heteogeneity by Phase

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The specifications are identical to the middle figure in Figure 4. However, the left figure restricts the sample to phase one (treated) and phase three (untreated) districts, while the right figure restricts the sample to phase two (treated) and phase three (untreated) districts.

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Figure A3: Effects inside 15 Kilometers

The figure is identical to the middle figure in Figure 4 presents results within 15 kilometers.

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Highlights

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Wage effects of Indian public works program are spatially heterogeneous Treated areas near untreated areas see smaller wage increases Treated areas far from untreated areas see larger wage increases Suggests previous estimates are underestimates of true effect Results indicate true effect may be twice as large as previously estimated

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