Reducing Delay in Payments in Welfare Programs: Experimental Evidence from an Information Dissemination Intervention

Abstract

This paper assesses the impact of an information dissemination intervention on the local-level implementation of the rural public works program in India. One key feature of the intervention is to provide information to workers once their wages get credited into their accounts. Using administrative and survey data, its impact on delays in wage payments and days of work along with the awareness levels of the entitlements is evaluated. The findings indicate a substantial reduction in payment delays and in trips made for wage withdrawal, in addition to improvements in awareness. The decrease in the payment delays in the treated villages persists even beyond the intervention period. While a limited impact on work days is observed during the intervention, a significant increase in the post-intervention period is found. The findings substantiated through qualitative evidence provide a platform for an innovative and cost-effective intervention to improve the implementation of social protection programs.

1. Introduction

The success of welfare interventions, including public works programs, depends on how they are implemented at the local level. Multiple market failures leading to implementation shortfalls, transaction costs, and elite capture are often cited as the reasons for their failure to produce desirable impacts (Bardhan and Mookherjee 2000; Skoufias 2005; Pritchett 2009; Narayanan et al. 2017). One key reason for such failures is incomplete information among the beneficiaries, which makes it difficult for them to hold functionaries to account (Drèze and Sen 2013). In other words, the local functionaries can utilize the information asymmetry for their benefit, resulting in significant welfare losses for the intended beneficiaries (Banerjee et al. 2018). Accordingly, the literature has emphasized the pivotal role of information in various contexts, which include functioning of the markets, community development, mobilization of natural resources, and provisioning of public goods and services (Stigler 1961; Jensen 2007; Buntaine, Daniels, and Devlin 2018; Protik et al. 2018; Camacho and Conover 2019; Armand et al. 2020; Dal Bó and Finan 2020). This paper evaluates an experimental intervention that provides information to workers on the rural public works program implemented in India, thus seeking to reduce the information gap between them and the implementers.

Theoretically, better access to information can mitigate the effects of government failure and improve rural governance (Kosec and Wantchekon 2020). With easier access to information for citizens, monitoring and accountability may improve, thereby reducing the incentive for service providers to shirk their responsibilities. However, it is also possible that citizens are unable to use the information to demand their entitlements. Even if they do, the implementing authorities may not respond to the demands unless there are proper incentive mechanism or sanctions. Hence, gauging whether the dissemination of information improves implementation depends on the context and how it is disseminated. Previous studies have found mixed evidence in this regard. For example, Banerjee et al. (2018) found that the dissemination of information increased the receipts of benefits in a subsidized rice program in Indonesia. However, Ravallion et al. (2015) saw no such gains in work days under the Indian rural public works program. While Grossman, Platas, and Rodden (2018) were able to observe short-term improvements in educational services in Uganda due to interventions associated with the Information and Communication Technology (ICT) platform, they did not find any discernible improvements in health and water services.

This paper evaluates a small-scale randomized intervention rolled out in parts of the southern state of Telangana in India. The intervention is based on accessing information from a public website and disseminating this information to the beneficiaries of the Mahatma Gandhi National Rural Employment Guarantee Act (MGNREGA), a public works program that has been implemented in India since 2005. The program guarantees each rural household a minimum of 100 days of manual and unskilled work for wages available on demand. Among other issues, one critical problem of the program is the prevalence of substantial “last-mile” delays in payments. This problem arises when workers often do not have precise information about when their wages are credited to their accounts. The official responsible for wage disbursal then takes advantage of this information gap to retain the money for some time instead of disbursing it, thus delaying payments to the workers. To prevent this delay, the intervention harnesses publicly available micro-level administrative records of the program to disseminate the information. The main component of the intervention is as follows: the information on workers’ payments is reflected on the public website once their wages are credited to their respective payment intermediary (banks or postal accounts). Using this information from the website, a list with names of the relevant beneficiaries (whose wages have been credited) is posted at the main junctions of the respective villages, along with a mobile phone call to let them know. In addition, awareness messages on various provisions of the program are disseminated through mobile phone calls and local meetings. With this information available, it is expected that the beneficiaries can hold the local authorities responsible if the relevant wages are not paid on time. Therefore, the expected cost of holding the wages by the officials would increase, thereby reducing the delay in payment at the local level.

In this paper, the impact of this intervention on three primary outcomes related to MGNREGA is examined: last-mile payment delays, the number of trips made to collect wages from banks/post offices, and the uptake defined as the number of days of work under the program, in addition to the associated intermediate outcomes that include indicators of awareness of the program provisions. To estimate the effect on awareness and the number of trips for wage withdrawal, longitudinal survey data from the baseline and end-line waves is used. Household administrative data are used to gauge the impact on local payment delays and work days.

A substantial reduction in local-level payment delays is found, which could be attributed to the wage credit list posting. The gains appear to persist for several months after the conclusion of the intervention. In addition, a significant reduction in the likelihood of making multiple trips to banks / post offices to withdraw wages is observed. While the average effect on participation in the program is found to be statistically insignificant during the intervention, an increase in work days after the intervention is observed. Further, a significant improvement in awareness of various program provisions is found among the respondents residing in the intervention villages. The results are robust even after accounting for the potential attrition bias. Based on the findings and approximate intervention cost, the intervention is found to be cost-effective. Conservative estimates indicate that the government can save about |${\$}$|31,000 (in US dollars) annually, if the program is implemented across the state. This is in addition to a range of other benefits that include a reduction in the number of trips for wage withdrawal and increased awareness of entitlements, among others.

This paper complements Ravallion et al. (2015), who use information campaigns to improve awareness of the program entitlements. The intervention provides similar information that explains the entitlements in addition to the posting of the wage credit list. Further, the paper complements Muralidharan et al. (2021), who use a phone-based monitoring system to find improvements in local-level implementation in the context of a cash-transfer program (the Rythu Bandhu Scheme) in India. In particular, they collected information from the beneficiaries about the payments and then provided it to the relevant agricultural officers responsible for timely payments. This intervention resulted in significant improvements in the implementation of the program. While the intervention described in this paper also aims to reduce delays in payment and improve local-level implementation, here information is provided directly to the beneficiaries, which arguably can auger demand for better public services from the relevant authorities. Evidence suggests that this is a cost-effective way of improving local-level program implementation.

The paper's main contribution lies in finding ways to increase accountability among the implementers. Here, a cost-effective intervention is evaluated to address the information gap between workers and local authorities, a gap that may incentivize rent-seeking behavior among the latter. Arguably, such information can also be disseminated through mobile phones. However, rural areas in developing countries, including India, have relatively lower mobile ownership and poor signals. Economic constraints may also push them not to use their phones regularly. Hence, dependence on mobile technology for information dissemination may not provide a complete solution. In this context, it can be argued that this paper's intervention is more inclusive and far-reaching. Therefore, through this paper, the intervention is proposed as a valuable alternative to the actions of Civil Society Organizations (CSO) and other program-implementing authorities for improving local-level implementation of social protection programs.

Additionally, the study contributes to three strands of the information dissemination and policy literature. First, it documents how technology-based interventions can improve the implementation of welfare programs. These interventions work directly through the dissemination of information to beneficiaries and indirectly by encouraging the beneficiaries to hold the implementing authorities to account (Björkman and Svensson 2009; Bhatti, Kusek, and Verheijen. 2014; Nagavarapu and Sekhri 2016; Grossman, Platas, and Rodden 2018; Muralidharan et al. 2021). Second, it contributes to the literature showing how information dissemination can address rural governance problems (Kosec and Wantchekon 2020). Finally, the paper contributes to the growing research on MGNREGA and related welfare programs that discuss the strategies for improving their implementation (Banerjee et al. 2020; Muralidharan et al. 2021).

The structure of the paper is as follows. Section 2 describes the MGNREGA program and the existing payment system. Section 3 lays out the problems in detail and gives a description of the intervention design and the mechanisms through which it can address the issues. Section 4 presents the study design, data description, variables, and randomization process. Section 5 discusses the estimation strategy, and section 6 presents the main findings from the regressions. Section 7 examines the intervention in terms of the heterogeneous effects, post-intervention work days, and cost-effectiveness, and section 8 concludes with a discussion of the potential takeaways and policy recommendations.

2. MGNREGA Payment System and the Problems

MGNREGA was introduced on August 23, 2005, and was initially implemented in 200 rural districts of India. In 2008, it was extended to all rural areas of the country. Under this program, any adult from a rural household willing to do unskilled manual labor at the statutory minimum wage is entitled to be employed for at least 100 days a year in public works. A job card is mandatory to work under the program. If a household wants work, an application must be submitted indicating the dates and duration of the work undertaken. An unemployment allowance is paid if no work is provided within 15 days of the application. If wages remain unpaid, even after 15 days of completion of the work, the workers are eligible for delay compensation. The democratically elected village head and their office are typically responsible for implementing the program at the Gram Panchayat (GP) level.¹ However, in Telangana, the responsibility lies with an employee of the state government called the field assistant (FA).

The system of payment under MGNREGA in Telangana is as follows. When the work is completed, the office of the block development officer (BDO) physically verifies it. A fund transfer order (FTO), which is analogous to a pay order, is then generated. Next, the FTO is submitted for approval from the central ministry. After the approval, the details are sent to the payment intermediaries responsible for the transfer of wages. Whether the payment intermediary is a bank or post office varies across the GPs but the same method is used within each GP.

The postal office comes under the Ministry of Communications, Government of India. Historically, due to a lack of adequate financial infrastructure, the postal department in India had been responsible for accepting deposits under different saving schemes or money transfers, among other financial operations. Because of the widespread outreach of post offices, the government often utilizes its network to disburse payments for many welfare programs. Administratively, a single local post office branch covers one to two GPs. All local post offices come under the jurisdiction of the main post office at the district level. The total amount of wages due at the district level is first transferred to the main post office at the district level. Since the district is a large geographical area, a branch postal master (BPM), a contractual employee, is entrusted with collecting wages from the main post office and disbursing them to all beneficiaries coming under her jurisdiction. Therefore, the wages credited to the postal accounts must be obtained through the BPM. However, the wages credited to the bank accounts must be directly collected through the banks. It should be noted that biometric authentication needs to be done to receive both types of payments.

The existing literature has observed a prevalence of substantial delays in payments because of delays in FTO generation or approval from the central ministry (Narayanan, Dhorajiwala, and Golani 2019; Ravallion 2019; Narayanan, Dhorajiwala, and Kambhatla 2020). Three other problems relevant to our study are discussed in detail:

Last-Mile Delay in Payments

Last-mile delay in payment occurs when the wages are credited to the bank/postal account, but the beneficiary is unable to collect them. This can happen for several reasons, which include local administrative constraints or corruption, among others. In the present context, the BPMs are responsible for wage disbursal when it gets credited to the postal accounts of the beneficiaries. Because the beneficiaries are often unaware of when wages get credited into their accounts, the BPMs use this information gap to their advantage. For example, the BPM may take this opportunity to collect the wages from the main post office. Instead of disbursing it to the beneficiaries, she may choose to keep the money for an extended period to meet her personal needs, thus delaying the payments.

In contrast, beneficiaries who have bank accounts do not depend on BPMs or similar officials to disburse wages. Instead, they have to collect wages themselves once the payment gets credited. However, a common complaint within the Indian rural banking system has been overcrowding. Because of this, bank officials often turn away the beneficiaries under the pretext that the wages have not yet been credited, even when they have (Narayanan, Dhorajiwala, and Kambhatla 2020). Therefore, for bank payments as well, last-mile delayed payments are common.

While the data on wage debit dates for bank payments are unavailable, wage credit and debit dates are both available for postal payments. This information makes it possible to gauge the extent of this problem of last-mile payment delay for postal accounts. Suppose this delay is defined as the number of days between the wage credit and debited date.² In that case, in the pre-intervention period, an average delay of about 37 days is observed for every wage payment transaction (January to October 2017). This last-mile delay is about 34 days in Maddur and more than 40 days in the Damaragidda block.³ Additionally, 10 percent of the beneficiaries faced an average delay of 148 days and 165 days in these two blocks, respectively. Notably, in the treatment GPs and control GPs (discussed in the “Study Design” portion of section 4), the corresponding maximum delay goes up to 695 days and 743 days, respectively. Other studies have also flagged this incidence of highly delayed payments across India (Narayanan et al. 2017; Narayanan, Dhorajiwala, and Golani 2019). Such payment delays can adversely affect the poor through two key channels: the imposition of an implicit consumption tax and a decline in the human as well as the net financial worth of the household (Basu, Natarajan, and Sen 2020). Significantly, this article's work area is based in the Mahbubnagar district, which is among the most economically backward regions in India.⁴

Multiple Trips for Wage Withdrawal

It is important to note that payment delays can also push beneficiaries to make multiple visits to banks or post offices to enquire about whether wages have been credited into their accounts. Narayanan, Dhorajiwala, and Golani. (2020), based on a survey conducted in 2018–2019 across three states (Andhra Pradesh, Rajasthan, and Jharkhand), found about 45 percent of the MGNREGA workers had to make multiple trips for wage withdrawal. In addition to the cost of travel, these problems also entail the direct substitution of labor time. This article's data suggest that 86 percent of the respondents in the pre-intervention period made multiple visits for their last wage withdrawal. An average worker has to make close to three trips before receiving the wages, with about 22 percent having made more than three visits. In this article's midline survey, several respondents reported that these multiple trips are costly because workers have to forgo a part of their daily wages. Notably, the problem of multiple trips exists for workers with bank accounts and also those depending on postal payments.

Awareness

In addition to the problems of delay in payments and multiple trips made for wage withdrawals, low levels of awareness among beneficiaries also pose a significant impediment to the successful implementation of the program. Studies conducted across states have documented the lack of awareness of the critical entitlements of the program, and this problem is widespread even after years since the program was put into effect (Bhatia and Dreze 2006; Das, Singh, and Mahanto 2012). From this article's pre-intervention survey data, only about 63 percent of the respondents were found to know about the entitlement of 100 days of work. Similarly, only 24 know the process requirement of getting the work, and only 5 percent about the provision of unemployment allowance.

3. The Intervention

The intervention, developed by LibTech, was rolled out in randomly selected GPs of the Damaragidda and Maddur blocks in the Mahbubnagar district in Telangana under the name of Upadhi Hami Phone Radio.⁵ It was implemented for 13 months from November 2017 to November 2018, and consisted of two main components:

Posting of Wage Credit Lists

The intervention team followed two-pronged strategies to expedite the disbursal of payment. First, they sourced data on wage payments from the MGNREGA administrative website after they get credited to the accounts. A wage credit list is then prepared and posted at multiple points, including the GP administrative office and other meeting points within the GP. The list included the following information: (1) The name of the beneficiary, (2) the job card number, (3) the duration of work for which the amount was credited, and (4) the amount credited into the beneficiary account.⁶ Second, a phone call is made to inform the beneficiaries about this wage list posting. The frequency of this intervention depended on the number of times the wages got credited in a month.

In the absence of the intervention, the workers are unaware even when the wages get credited to their accounts. The BPMs take advantage of the situation and hold the payment for their personal needs on the pretext that the money is yet credited into the workers’ accounts. Hence the wage payment may get delayed at the local level after it is credited into the postal accounts. It should be noted that the BPM faces an expected cost of holding the money in the form of fines or termination of the contract if she gets caught (Ravallion 2019). The intervention can reduce the information gap between the BPM and the workers, raising this cost and forcing the former to pay the wages timely. This is explained through a theoretical framework presented in section S1 and fig. S1.1 in the supplementary online appendix.

For beneficiaries with a bank account as well, the intervention is likely to reduce payment delays by providing timely information on wage credit. In this case, even when bank officials ask them to come sometime later for wage withdrawal, the workers, knowing that their wages have been credited, can pressure the banks to pay them.

Mobile Phone Broadcasting

Information about various rights and entitlements guaranteed under MGNREGA is disseminated to beneficiaries through periodic voice broadcasts, primarily using mobile phone calls. These mobile phone broadcasts included information on general processes that could help workers to access their entitlements. These include the procedures that must be followed for demanding work, getting job cards, unemployment benefits, delayed and rejected payments, and grievance redressal, among others. The messages are read from a script, which is recorded and then broadcast.⁷ The intervention team also arranged local-level meetings to discuss these provisions in detail, primarily for non–mobile phone owners. However, the ones with phones are also eligible to join.⁸

To sum up, the intervention consists of two components: (1) posting of the beneficiary list after the wages get credited to their account, and (2) broadcasting of the program entitlements.⁹ The first component can force BPMs (in the case of postal accounts) and bank officials (for bank accounts) to pay the wages after they get credited, thereby lowering last-mile delayed payments. Further, these measures can help reduce multiple visits to banks and post offices for wage withdrawal. This may encourage workers to demand more work under the program, potentially improving welfare. The second component can increase awareness levels of the program entitlements. Therefore, it can act as a catalyst to improve the process through higher accountability and transparency, encouraging beneficiaries to demand more MGNREGA work days. Notably, the interaction of the first and second components can also raise awareness levels and reduce last-mile payment delays. Figure S1.2 in the supplementary online appendix shows how these mechanisms interact.

4. Study design, Data, and Variables

Study Design

The intervention was rolled out randomly at the GP level in the Damaragidda and Maddur blocks of the Mahbubnagar district, where the randomization was stratified across the blocks. Accordingly, 12 GPs out of the 22 GPs of the Damaragidda block and 14 GPs out of 27 in the Maddur block are randomly selected for intervention. It should be noted that the Mogala Madaka GP of the Damaragidda block is dropped from evaluation as the local Member of Parliament adopted it. Hence, the 26 selected GPs form the intervention group, and the remaining 23 GPs in these two blocks constitute the control group. At the time of intervention, 19 treated GPs, and 19 control GPs had postal accounts as the payment intermediary, and in the rest of the GPs, the payment is made through the bank accounts. The administrative job card–level data from these two blocks are primarily used to evaluate the effect on delay and uptake. To estimate the impact on the trips made for wage withdrawal and the intermediate outcomes, which are indicators of awareness in this case, baseline and end-line survey data are used.

Two other blocks within the Mahbubnagar district and close to the Damaragidda and Maddur block, Hanwada and Koilkonda, are also considered broadly based on similar geographic and demographic characteristics to study spillover effects, if any. It can be argued that the control GPs located within the same intervening block are closer to the treated ones, and there is a possibility of flow or spillover of the intervention from the beneficiaries into these GPs. For example, the disseminated information in the intervention GPs may get shared with the villagers in the adjoining non-intervened GPs because of the proximity of the two sets of GPs. Hence gains from some of the interventions in the treatment GPs may flow to the adjacent control GPs within the same block. However, the chances of spillovers in GPs in the Hanwada and Koilkonda blocks are negligible because of potentially lesser interaction between individuals of two different blocks. Therefore, spillover can be assumed to flow across GPs within the same block and not across the blocks. Since these GPs in Hanwada and Koilkonda are not intervened, they are referred as “additional control blocks,” and Damaragidda and Maddur block together are referred to as “intervention blocks.” The basic characteristics of these four blocks taken from the 2011 Census conducted by the Government of India are presented in table S7.1 in the supplementary online appendix. The block map of the Mahbubnagar district with the study areas highlighted is shown in figure S4.1 in the supplementary online appendix. The treatment and control GPs within the two intervention blocks (Damaragidda and Maddur block) are shown in figure S4.2 in the supplementary online appendix. The primary analysis in the paper uses data from these GPs.

Data

The data primarily used in this study are from the administrative website of the program in Telangana to evaluate the impact on uptake and delay.¹⁰ In particular, to estimate the impact on last-mile delay, all the job cards, from whose account at least one payment was debited between January 2017 and May 2019 are considered. This period is studied because it covers 10 months of the pre-intervention period, with 11 months of the intervention period and 5 months of the post-intervention period. To estimate the impact on the uptake, those job cards that worked at least for one day from January 2017 to November 2018 are considered.

Two waves of a household survey among job card holders in 96 GPs within the four blocks are conducted to gauge the impact of the intervention on intermediate outcomes. The baseline survey was conducted in September and October 2017, before the start of the intervention. Additionally, a midline survey was conducted in July 2018 to get a stock of the nature and status of the intervention and obtain qualitative insights on the potential impact. The end-line survey was conducted from December 2018 to February 2019 after 13 months of exposure to the intervention. The same households and respondents that were surveyed in the baseline survey were also interviewed during the end-line survey.

Among the households working at least once in 2016–2017, approximately 15 from each GP were randomly chosen for the baseline survey. The total number of households surveyed was 1,444 in the baseline survey and 1,352 in the end-line survey (692 and 660, respectively, from intervention blocks).¹¹ From these households, the person who worked for the highest number of days in 2016–2017 is interviewed. Some households were left out in the second wave since the respondents were not found even after three visits. To ensure that the sample of non-resurveyed households is random, their characteristics are compared with those that were resurveyed. No systematic difference between the two is observed, ensuring the non-resurveyed sample is random (table S7.2 in the supplementary online appendix). One may argue that the sample size is low, which may not yield unbiased estimates. However, administrative data are utilized, which makes it possible to include all the eligible job card holders in determining the causal effects of the intervention on two of the primary outcome variables: last-mile payment delays and uptake. The survey data are used to estimate the impact on the trips made for wage withdrawal and intermediate outcomes on program entitlement awareness. Further, randomization inference technique is used to address any potential small sample bias.

The survey questionnaire asked for a wide range of household information, including demographic, socio-economic, and detailed information on MGNREGA. Apart from general queries about the program, specific questions were asked to get a clear picture of the awareness levels among beneficiaries of the scheme and their entitlements (including unemployment allowance, minimum days of work entitlement, and wage rates). In addition, information about the FAs and the salient characteristics of the GPs was collected. During the second wave, further information from the surveyed households in the treated GPs on their perception of the intervention and its effects on MGNREGA participation and payment delays was gathered.¹²

Variables

The two primary outcome variables are last-mile payment delays and uptake or number of days of work under the program. Last-mile payment delay is calculated as the difference in days between the wage credit and debit dates in the bank or post office account (see detailed discussion in the portion of section 6 on the “Impact on Delay and Trips Made for Wage Withdrawal”). The underlying assumption is that beneficiaries withdraw the money as soon as it gets credited into their account. This assumption is based on the context where the beneficiaries are poor with a high marginal utility of money, disproportionately higher disutility for payment delay, and a low propensity to save.¹³ Nevertheless, even if this bias is allowed for in the measurement of last-mile delay, the average causal estimates would remain unbiased due to the random assignment of the intervention. The uptake in terms of the number of days per month/year for every job card is calculated directly from the publicly available administrative data portal.

Using the survey data, two related outcome measures are examined: the average number of trips made and the probability of making multiple trips for wage withdrawal. A range of intermediate outcomes that include five indicators of awareness levels are assessed: whether the respondent knows (1) about the work entitlement of 100 days every year to each household, (2) about the work application process within MGNREGA, (3) that an unemployment allowance is made in the event of not receiving work, (4) that payment has to be made within 15 days of their completion of work, and (5) the correct wage rate (INR197 (∼US|${\$}$|2.8) at baseline and INR205(∼US|${\$}$|3) at end line).¹⁴

A set of control variables measured at baseline in these regressions are incorporated in the regressions. The associated covariates to capture the household economic conditions are land cultivated by the household in acres, the number of livestock (including oxen, bullocks, and cows), and whether the household has a toilet. Further, the main occupation of the household is controlled through a dummy variable that captures whether it is engaged in agriculture. Other control variables include whether the household members watch television, the number of adult members, and the highest educational level in the household in the regression. Since caste is one of the significant barriers to social inclusion, whether the household belongs to the Scheduled Caste or Scheduled Tribe (SC/ST) community is incorporated (Deshpande 2011). At the respondent level, gender, age of the respondent, and possession of a mobile phone, along with the household level variables mentioned above are controlled for. It should be noted that three respondents could not report the educational attainment of all the household members. Hence, the highest educational level within the household cannot be determined. Additionally, three other respondents did not report if their household members watch TV.

To ensure the success of the randomization procedure, the administrative job card level data are used along with the sample of 660 households surveyed across both waves to compare the baseline characteristics across the respondents from treated and control GPs.¹⁵Table 1 presents the results of the difference in the means test between the respondents from the two groups. The mean levels of none of the intermediate outcome variables derived from the survey are found to be statistically significant at a 5 percent level. This is also true regarding the proportion of respondents who reported making multiple trips to banks / post offices to withdraw wages and the average number of trips. Further, 13 control variables are further considered, which include the characteristics of the respondents and their households. Only the respondents’ mean age is found to be statistically significantly different in the two groups (at a 5 percent level).¹⁶ Nevertheless, the value of this difference is small; therefore, the imbalance is unlikely to confound the findings. Further, using the set of all job cards from administrative data, the differences in the primary outcome variables—average last-mile payment delay and uptake from January to October 2017 (the intervention started in November 2017)—are observed. The results ensured that the randomization is balanced. In addition, where survey data are used, the p-values generated using the randomization inference technique (explained in the subsequent section) that accounts for the potential small sample bias are presented. Importantly, no statistically significant difference is observed for any of the characteristics that are considered. Additional tests for the balance through kernel density plots (section S7 in the supplementary online appendix) also indicate the same.

Notably, in the regressions, these household and respondent characteristics are controlled for in addition to the block-level fixed effects. Further, the outcome variable measured at baseline is also incorporated to control for pre-program levels in the outcomes. This minimizes the bias in the treatment estimates.

5. Estimation Strategy

The randomized experimental design, as explained earlier, controls for potential selection or omitted variable bias and yields unbiased causal estimates. To gauge the impact of the intervention, the monthly average difference in last-mile delay and uptake between the job cards in treated GPs and the control GPs is mainly relied upon. The difference between the pre-intervention period with those during the intervention and post-intervention periods is compared. This is similar to a standard double difference (DD) comparison, which assumes that the indicators in the intervention GP would have shown similar levels to those in the control GPs without the treatment. Therefore, the observed difference between the two post-intervention can be causally linked to the intervention.

More formally, the following regression model is estimated:

Here |${Y}_{ijbt}$| denotes the outcome variable (average last-mile payment delay and uptake) for job card i belonging from GP j situated in administrative block b during the month |$t,$| which varies from 1 (January 2017) to |$k=23$| (November 2019).¹⁷|${T}_{jb}$| indicates whether GP j has been treated or not through a binary variable. |${M}_t$| represents the month-wise dummies, and |${\pi }_b$| is the vector of block fixed effects. |${\omega }_{ijbt}\ $|is the error term. |${\gamma }_t,$| which gives the coefficient of the interaction term of the treatment and month-wise fixed effects, is of interest. The standard errors from the regression are clustered at the GP level.

To estimate the impact on intermediate variables and visits made to banks / post offices for wage withdrawal, analysis of covariance (ANCOVA) is used. This makes it possible to estimate the treatment effects after controlling for the baseline value of the outcome variables. The literature indicates that this increases statistical power, especially when the autocorrelation of outcomes is low (McKenzie 2012; Hidrobo, Peterman, and Heise 2016; Haushofer et al. 2020). Since the autocorrelation of the outcome variables is low, and most of the variables of interest are binary in nature, the following probit model is estimated:

In the first model, |${\tilde{Y}}_{ijbt=1}$| is whether respondent|$\ i$| from GP j situated in administrative block b has to travel more than once to banks or post offices to collect the wages during the end-line |$t=1$|⁠. |${\tilde{Y}}_{ijbt=0}$| is the same binary variable at baseline. In another model, |${\tilde{Y}}_{ijbt=1}$| and |${\tilde{Y}}_{ijbt=0}\ $|are taken as the reported number of trips made on average by the respondent during end-line and baseline surveys, respectively. |${T}_{jb}$| is the treatment dummy variable, which equals 1 if the GP j is in the treatment arm; 0 otherwise. |${\pi }_b$| is the vector of block-level fixed effects, and |${u}_{ijbt}$| is the error term. |$\beta ,$| gives the treatment effects by controlling for the lagged value of the outcome variable along with a set of potential controls. The same method is used to estimate the impact on the indicators denoting awareness (intermediate outcomes). Here as well, the standard errors are clustered at the GP level.

Importantly, the randomization inference technique—which provides critical values from a two-sided randomization inference test of zero treatment effects to address the potential small-sample bias—is used here. More precisely, using the existing sampling design, the technique reassigns the treatment and control units in the sample and then re-estimates the coefficients using the placebo assignment. Under the null hypothesis of zero treatment effects, the test computes the p-values by calculating the proportion of re-estimated coefficients that are larger (in absolute value) than the actual ones. This technique is useful in this context as it provides inference with the correct size regardless of the current sample size (Fujiwara and Wantchekon 2013; Athey and Imbens 2017; Young 2019). Accordingly, the randomization inference p-values obtained after 1000 replications are reported wherever the survey data are used. The user-written ritest command in STATA 14 is used for this exercise (Heß 2017).

6. Results

Impact on Delay and Trips Made for Wage Withdrawal

To examine the impact of wage payment delay, information on the credited and debited dates for all job cards from the GPs that depend on postal accounts for the disbursement of MGNREGA wages and also received their wages in the analyzed time period is used.¹⁸ These data are specifically used to calculate the outcome variable, which is the month-wise mean last-mile delay defined by the difference in the credited and debited dates for each job card. The monthly estimates of the treatment effects are obtained through the regression outlined in equation (1). Figure 1 presents the plots of the marginal effects separately for the treated and control GPs over the months starting from January 2017.

The findings reveal a significant positive impact, as the difference in last-mile delays between treatment and the control GPs shows a considerable fall in the latter part of the intervention period. Before the start of the intervention, as one can observe, the difference in last-mile delay across the treatment and control GPs remained insignificant at a 90 percent level. Even after November 2017 (month number 11), when the intervention started, this difference remained statistically indistinguishable from zero for most of the months. However, during the latter part of the intervention, a significant reduction in last-mile delay is found. For example, in August 2018, an average decrease in last-mile delay in the treated GPs by about six days in September 2018 is found, which went up to more than 12 days in October and about 29 days in November. Notably, instead of the monthly average, two-month and three-month average delays from January 2017 to May 2019 are also considered. The findings from the regression given in figs. S7.2 and S7.3 in the supplementary online appendix indicate a statistically robust impact of the intervention on last-mile payment delays, respectively. Interestingly, a significantly lower last-mile delay even during the post-intervention period (December 2018 to May 2019) is observed, possibly indicating that the effects persist and there might be long-term benefits associated with the intervention.

The qualitative investigation reveals that the beneficiaries were initially unable to leverage this information, as the intervention was new to them, and many were unaware of the right avenues to hold the BPM accountable. A part of this explanation also relates to the power asymmetry between her and the beneficiaries. A significant proportion of the beneficiaries in the study are illiterate. Hence, many could not comprehend the wage list posting and the advantages one can derive from it.¹⁹ The study's subsequent discussion with the intervention team indicates that many beneficiaries utilize the knowledge of credited wages through the wage list posting to demand their payments from the BPM. Also, when the lists are posted, a beneficiary can know about others whose wages are credited to their accounts. Hence, together they can hold the BPMs accountable and push them to deliver the payments on time, thus underscoring the potential importance of collective action in raising accountability.

As specified earlier, the average last-mile delay in the intervention and control GPs is about 37 days. The fact that observed last-mile delay reduction of about 11 days in the last five months of the intervention and about 21 days in the last two months is noteworthy, and it is here that the intervention assumes importance. Note that a reduction of about 29 days is registered in the last month of the intervention. One may argue that the intervention may not be policy relevant, as it can only influence the last-mile local-level delays. However, this study's observations indicate that last-mile payment delays are significant, especially considering that the program was designed to target the poorest population during the lean agricultural season.

The baseline and end-line survey make it possible to determine if the intervention led to fewer visits to banks or post offices to withdraw MGNREGA wages. For this, the effects on the probability of making multiple trips to banks or post offices and the number of trips for wage withdrawal are examined. Two outcome variables—whether the respondent made more than one trip (binary variable) and the number of trips (continuous variable)—are considered, and then probit and OLS regressions are applied, respectively, as outlined in equation (2). The estimates are presented in table 2. Two different specifications are used to ensure that they are robust to the addition of covariates. The first specification is the unadjusted one, where no control variables are included. In the second, all the mentioned controls, including the block dummies, are incorporated. The findings remain consistent across specifications and indicate about a 10–11 percentage point reduction in the probability of travelling more than once to banks / post offices to collect wages on average. Furthermore, respondents from intervention GPs are likely to travel 0.3 days less on average than those from the control GPs. This directly complements this study's findings on the reduction in last-mile payment delays because of the intervention. Regression estimates without controlling for the baseline outcome variable yield similar results. The distribution of the number of trips made in the treated and control GPs suggests that they do not cross each other at the higher levels.²⁰ For example, 31 percent in the treated GPs reported they had to make just one trip as against only 19 percent in the control ones; 83 percent in the control GPs reported they got the payment within three visits, while in the intervened GPs, this is close to 88 percent. Five percent in the control GPs say they need more than five trips on average for wage withdrawal, which comes down to less than 1 percent in the treated GPs. This study's back-of-the-envelope calculations, presented in the portion on “Cost Effectiveness” in section 7, indicate that the gains in the reduction of the trips can be equated to an additional three days of work under MGNREGA for an average household.

One can argue that the intervention could have nudged the individuals into withdrawing their wages, even if they did not need them. However, the intervention only provided information on the wages being credited to the bank account and did not mention anything about withdrawal. Further, the study area is among the poorest in India and comes under the Backward Regions Grant Fund (BRGF) program.²¹ Therefore, most of the workers are less likely to have surplus money. In the control GPs unaffected by the intervention, the end-line survey data indicate that 81 percent of the respondents make multiple trips for wage withdrawal, implying their need for money. In the regressions, the economic condition of the respondents, which would be potentially correlated with whether the respondent needs immediate cash, is controlled for. Further, the estimates remain statistically similar for respondents staying in cement houses compared to those without such dwellings. Therefore, it is less likely that the workers would have been nudged to withdraw wages early. However, this possibility cannot be ruled out, so the results follow this caveat.

Notably, similar insights are obtained from the qualitative work during the midline survey, indicating that the wage list posting helped them reduce the trips to the payment intermediaries for wage withdrawal.²² From the end-line survey data, 68 percent of respondents reported that their bank / post office transactions became easier than in the previous year. About 63 percent of them believe that delay in payment has reduced compared to the previous year.

Impact on Work Days

To examine the impact on the uptake, all active job cards—defined as the ones who have worked at least for a day between April 2015 and October 2017—are used. As in the earlier case, the month-wise average work days in the intervention and control GPs are used as the outcome variables and estimated as outlined in equation (1). The month-wise treatment effects from January 2017 to December 2018 (fig. 2) are plotted. The plots for the treatment and control GPs in the pre-intervention period are primarily found to move together. After the intervention was initiated, no discernible difference between the treatment and control GPs is observed, indicating limited impact of the intervention on the uptake.

These findings are checked using the survey data, which makes it possible to control for a host of household-level covariates that can confound the treatment effect estimates. For this, a simple DD regression is used to estimate the difference in uptake between the baseline and endline for jobcards from the treated GPs and compare it with those from the control GPs.²³ The regression is given as follows:

Here t takes the value of 1 for end-line and 0 for baseline. |${Y}_{ijbt}$| is the outcome variable of interest and denotes the logarithmic value of the number of days of work by the household at time t.²⁴|${T}_{jb}\ $|is the treatment dummy variable, and |${\pi }_b$| represents block-level fixed effects. |${X}_i$| denotes the respondents’ individual as well as household characteristics and |${u}_{ijbt}$| is the error term. |$\gamma ,$| which gives the treatment effects of the intervention, is of interest to this study. Table 3 presents the results from ordinary least squares (OLS) regressions using two different specifications. The first specification does not include any additional covariates in the regression model. The household covariates and the block dummies are incorporated in the second specification. The findings across these specifications and models indicate no significant difference in uptake because of the intervention; therefore, they remain in line with those that have been observed in fig. 2. Because the variable is observable only for those households that worked before or after the intervention period, the outcome variable is left-censored. Accordingly, a tobit regression with the same specification is estimated to obtain the effects on the intensive margin, but the results remain unchanged.²⁵

Despite no considerable impact in terms of uptake of the program, and hence no increase in the intensive margin, it is possible that the intervention led to a significant expansion on the extensive margin by including more households in the program and hence a higher probability of getting work. To check this, the same DD technique is used to estimate if there is an associated increase in its likelihood of getting work due to the intervention. Accordingly, the outcome variable takes the value of 1 if the household got work in period, |${\rm{t}}$| (baseline or end-line), and 0 otherwise. The marginal effects from probit regression calculated at the mean value of the independent variables are presented in table 3. The findings indicate no significant impact on the extensive margin, implying that the treatment did not have any discernible effect on the chances of getting work under MGNREGA.

Impact on Intermediate Outcomes

As discussed, the effect of the intervention on intermediate outcomes (indicators of awareness) is assessed using ANCOVA regressions given in equation (2). Since multiple indicators are considered, principal component analysis (PCA) is also used to create an awareness index, which is then used directly in the regressions. Broadly, this technique extracts orthogonal linear combinations of the variables from a more extensive set of variables that capture the maximum common information (Filmer and Pritchett 2001). The estimation results are presented in table 4. The findings indicate a statistically significant improvement in awareness after accounting for the possible controls with an observed increase of about 10 to 25 percentage points in the probability of being aware of different entitlements. This improvement remains robust even in the unadjusted model that does not control for the other covariates.²⁶ The family-wise error rate adjusted p-values based on Westfall and Young (1993) that account for multiple hypothesis testing of the five indicators of awareness (table S7.8 in the supplementary online appendix) are also reported. The results are found to be consistent.

The qualitative discussions during the midline survey substantiate this finding. In three of the four treated GPs that were visited, villagers appeared to be aware of the current MGNREGA wage rate and work application procedure. Many specifically attributed this awareness to the mobile phone calls from the intervention team.²⁷

To summarize, the intervention is found to be instrumental in increasing awareness of the basic provisions of the program. But this increase did not lead to higher uptake through increased work days under the program. This indicates the limited impact of awareness campaigns on participation in the program, a finding substantiating those by Ravallion et al. (2015), albeit their information campaign was different. Nevertheless, what sets this article's information dissemination campaign apart is its effectiveness in the reduction of last-mile delays in wage payments and trips made to banks and post offices for the withdrawal of wages. This is substantially important, especially when taking the disadvantaged population into consideration.

As discussed, the intervention had two components: phone calls and wage list posting. Therefore, in theory, our design does not allow us to associate these effects with one of these components. Hence, it is possible that the interaction of these two components leads to the observed effects on awareness, trips, and payment delay. During our midline survey, it was observed that the respondents attributed these effects to particular components of the intervention. While the reduction in delayed payments and bank/post office trips is attributed to wage list posting, the increase in awareness is linked with the broadcasts for informing about the entitlements.

Nevertheless, this evidence is suggestive; to precisely estimate the effect of each of these components, two further intervention groups apart from the control and the treatment are needed: one group with only the entitlement broadcasting component and the other with only the one associated with wage list posting. If randomly assigned, comparing the outcome indicators across these four groups is likely to generate the average treatment effects of each of these components. This is offered as a suggestion for further research.

Robustness and Falsification Checks

A series of robustness checks is conducted. Firstly, the inferences drawn from the pooled regressions rest on the assumption that there have not been systematic changes in the villages between the baseline and end-line that can influence the outcome variables. To ensure this, data on these changes (if any) from the GP officials and the FA are gathered. The officials and FA reported that there had not been any new NGOs working on MGNREGA or related programs that started their operations during the intervention period. No systematic changes in how MGNREGA functioned in the one year of running the intervention are observed. A number of additional checks that include falsification tests, re-estimation with double difference regression, placebo treatment of the control GPs, re-estimation with inverse probability weighting regression adjustments (IPWRA) and Lee Bounds (Lee 2009; Wooldridge 2010) have been done. The findings presented in section S6 in the supplementary online appendix ensure that the causal estimates are consistent.

Since the intervention pertains to information dissemination, there might be spillover from the intervened GPs to the adjoining control GPs within the same block. However, because the GPs situated in the non-intervention blocks of Hanwada and Koilkonda are distant from the intervention blocks, it can be assumed that the spatial spillover, which depends on the distance from the intervention GPs, should be minimal (Merfeld 2019).²⁸

With respect to the two components of the intervention, spillover from the treated GPs to the adjoining control GPs associated with wage list posting is likely to be negligible. This is because the list of beneficiaries whose wages have been credited would concern only a particular intervened GP and not an adjoining control GP. However, the likelihood of spillover from the information broadcasting component is higher because the information might flow from one individual to another.

Therefore, one would expect the effects of the spillover on payment delay and uptake would be limited while those on awareness indicators might not be. To gauge this, all the surveyed non-intervention GPs are categorized into two groups: (1) the control GPs within the intervening blocks of Damaragidda and Maddur and (2) the GPs from additional control blocks. If the group of control GPs from the additional control blocks is taken in the reference group, the marginal effect associated with the control GP dummy gives the estimate of the spillover effect. In other words, the same regression as specified in equations (1) and (2) is estimated for respondents only from the control and additional control GPs. The control GPs from the intervention blocks are now the treated GPs through spillover, and the control GPs are all those from the additional control blocks. With this setup, the associated regression coefficient for this dummy variable is assessed.²⁹

Findings from the regressions of last-mile payment delay and work days are presented in figs. S7.9 and S7.10, respectively, in the supplementary online appendix. As one would expect, no spillover effect is found for payment delay. Significantly higher work days are observed in the additional control GPs before and during the intervention when compared to the control GPs in the intervention blocks. Notably, this gap is not found to reduce after the initiation of the intervention. The regression results on trips made to the bank and awareness indicators are given in Table S7.13 in the supplementary online appendix. The findings indicate a statistically significant spillover effect on indicators related to unemployment allowance (at the 1 percent level) and work application (at the 10 percent level). For other indicators, no statistically distinguishable effect is observed. Therefore, limited spillover effects of the intervention on the outcome variables of interest are observed, which also acts as an additional robust check for the inference.³⁰

7. Further Analysis

Heterogeneous Impact

Are the treatment gains disproportionately higher for marginalized households? To test this, the effect of the intervention on last-mile payment delay and work days separately for the SC/ST households only is observed. Figures S7.11 and S7.12, in the supplementary online appendix, which present the relevant figures with the marginal effects, respectively, do not provide any evidence of higher effects for these socially marginalized groups.

The survey data are used to assess whether respondents belonging to the SC/ST community had to make a disproportionately lower number of trips for wage withdrawal because of the intervention. Further, these heterogeneous effects are explored among mobile phone owners or educated respondents (secondary or above). Table S7.14 in the supplementary online appendix, which presents the estimations, indicates no heterogeneous effects. Similar estimates for awareness indicators also show no such impact (table S7.14 in the supplementary online appendix).

Effect on Work days in the Post-Intervention Period

Literature has indicated that because of the uncertainty of securing jobs from the local authorities and associated delay in payments, workers are often “discouraged” from demanding work under MGNREGA (Himanshu et al. 2015; Narayanan et al. 2017). If this holds, a reduction in payment delay may encourage workers to demand more work under the program. In other words, a significant decrease in last-mile delay in payments, observed during the intervention, can potentially lead to a higher uptake of jobs in the next period. Given that a considerable reduction in last-mile delay in the treated GPs is found, this section tests if that is followed by an increase in uptake.

For this, the post-intervention period from January to December 2019 is considered, and equation (1) is used to run the same regression to estimate the changes in work days in the intervened GPs. The monthly estimates from the regression are presented in fig. 3. The findings indicate that households in the treated GPs worked for 10 days more under the program in 2 months (May and June 2019) than those in the control GPs (the difference is significant at the 10 percent level).³¹ It is important to note that these two months constitute the peak working months for the MGNREGA beneficiaries, which also get reflected in fig. 2. No significant increase for the other months in the non-peak working periods is observed. It should be noted that this marginal increase in work days may also be influenced by the authorities in the treated GPs being more proactive in giving MGNREGA work during the lean agricultural season because of the intervention.

Cost Effectiveness

The evidence from this paper indicates a substantial impact through a reduction in last-mile payment delays. For policy recommendations, however, one may argue that the intervention is costly and hence not cost-effective. To examine this in detail, the difference between the delay compensation amount the government has to pay to beneficiaries in the absence of the intervention and the total cost incurred to implement the intervention at the local level need to be calculated. As estimated, an average drop of around 25 days in last-mile delay per job card in the treated GPs compared to the control GPs, is assumed though this reduction was over 29 days in the last month of the intervention. With an average of 200 active job cards in every GP in Telangana, the total drop in last-mile delay is close to 5000 days. Guidelines on compensation for delayed wage payments state that the compensation amount that needs to be paid is calculated at a “rate of 0.05 percent of the unpaid wages per day for the duration of the delay.”³² Given that the minimum wage under MGNREGA in the state during the period of the intervention was around INR200 (∼|${\$}$|3), the compensation for each delayed day is INR 0.1 (∼US|${\$}$|0.0014).³³ This amounts to a cost of INR 500 (∼|${\$}$|7.15) that the government incurs each month in every GP for at least three peak months of work if it has to pay compensation for the last-mile delays. So, for an average of 25 GPs in each block, the monthly cost per block amounts to |${\$}$|178.75.

To calculate the total cost of the intervention, both the fixed and the variable costs need to be gauged. The fixed costs include a one-time lump sum payment of INR 5,000 (∼|${\$}$|70) to set the initial computer program to generate the list of beneficiaries whose wages got credited. This covers the entire duration of the intervention over all the 26 treated GPs (approximately the size of a block). Once this program is set, the existing block officials can generate the list using online administrative data and disseminate them through posters to the designated GP locations. The field assistants from the GPs can be used to post these posters, and their travel charge, based on the local rates, would be at most INR 100, which amounts to INR 2500 (∼|${\$}$|36) for all the 25 GPs within a block. Posters should be put up as many times as wages are disbursed from the central office, and the intervention team reported that for each GP, a maximum of five posters were needed to cover all the prime locations. Given the average printing cost per poster of around INR5, the total monthly cost per GP is around INR 25, which equates to INR 625 (∼|${\$}$|9) for all 25 GPs per block. The total cost of implementing the intervention per peak month per block is |${\$}$|115. With other miscellaneous expenses of US|${\$}$|20 every month, this amounts to |${\$}$|135 per block. Hence, the intervention can be estimated to save around |${\$}$|43 every month for each block. Considering about 240 administrative blocks in Telangana and three peak months of MGNREGA, the government could save about |${\$}$|30,960 annually. Notably, this estimate does not include the sunk costs of time the research team spent designing the intervention and learning how to use the phone-calling application. Further, it only includes the component of wage-list posting.

Nevertheless, this indicates that the government could enjoy a monetary gain of roughly |${\$}$|31,000 annually on average if it implements the intervention to reduce last-mile delays. This is significant: the marginal gain for every dollar spent in the existing system is close to |${\$}$|0.32.³⁴ It should be noted that from the second month onwards, because the fixed cost for the server need not be paid, this gain would be more than |${\$}$|18. Therefore, this is likely to be an underestimate of the actual gains.

There are multiple additional benefits for the beneficiaries, which are not considered in the above discussion. First, the findings discussed in the portion on “Impact on Delay and Trips Made for Wage Withdrawal” in section 6 indicate that they can save about 0.3 days by reducing the number of visits made to withdraw wages. This amounts to a saving of INR 75 for every payment if the daily average non-MGNREGA wage rate is assumed to be INR 250 (∼|${\$}$|3.6).³⁵ Generally, payments are made after six days of work. Therefore, for an average of about 48 work days yearly, a casual laborer household can save about INR 600 (∼|${\$}$|8.6) for the eight payment withdrawals. If a household works for 100 days, which is what it is entitled to, it may save about |${\$}$|18 yearly, equivalent to an additional six days of employment under MGNREGA every year. Second, the MGNREGA uptake in the subsequent period increases by about 10 days during May and June 2019. With the wage rate of INR 200 per day, the total earnings from the program would then be INR 2000 higher for the beneficiaries from the intervened GPs. Therefore, to sum up, this intervention can be regarded as highly cost-effective.

8. Discussions and Conclusion

This paper evaluates a novel randomized intervention that accesses information from a public website and disseminates the same to the beneficiaries of the MGNREGA. A substantial drop in last-mile delays in payments and multiple visits to banks or post offices for wage withdrawal is observed. Interestingly, even after the conclusion of the intervention, a significant reduction in last-mile delay is found, indicating a possible positive and sustainable change in these terms through the intervention. In addition, the intervention is found to improve awareness of the MGNREGA entitlements. However, no effect on days of work under MGNREGA during the intervention is observed, though, post-intervention, an increase in uptake in May and June is found when the demand for public works is high.

One of the limitations of the study is the inability to estimate the marginal effects of the two components of the intervention separately on the reduction in last-mile payment delay and improvements in awareness of basic entitlements. Theoretically, the reduction in payment delay is potentially the consequence of wage-list posting and the observed gains in awareness of basic provisions resulting from the broadcasts, which is validated by the qualitative interviews. Yet, quantitative estimation of these components' independent effects can further help refine the intervention and customize it when used as a policy tool, depending on the context. Therefore, this is flagged as a subject for future research.

Despite this limitation, arguably one of the novelties of the intervention is the usage of wage credit-list postings as a potential information dissemination channel. As hypothesized, the reduced information gap about wage credit enables the beneficiaries to make BPM accountable and enhance transparency, which can reduce last-mile delays in payments. This study lends credence to this argument empirically. Information campaigns on social protection programs often consist of generalized interventions that explain the provisions and entitlements of the program. While some of those campaigns have been successful in increasing the program uptake, they have not been beneficial in reducing local-level corruption, which systematically affects the stakeholders from developing countries (World Bank 2003). In fact, grievance-redressal mechanisms often fail due to a dearth of complete information among the beneficiaries, thus incentivizing rent-seeking behavior among the concerned authorities (Muralidharan et al. 2021). The intervention provides personalized information at a community level to all beneficiaries, once their wages get credited to their account, thereby reducing last-mile corruption in terms of payment delays. Here, the collective action from the group of beneficiaries is utilized, which can potentially make the authorities accountable. While individualized wage-credit information through mobile phones can also bridge the information gap, it is less likely to take gains from collective action. In addition, this article's intervention is cost-effective and does not depend on mobile phone signal or recharging. Further, in areas where officials have incentives to siphon off workers' wages, this intervention can effectively alleviate this leakage because the wage list also provides information on the due amount. The calculations indicate that the government can save about |${\$}$|31,000 annually if the intervention is implemented across the state. In addition, the workers can enjoy benefits that include a reduction in the number of trips for wage withdrawal and increased awareness of entitlements, among others.

Despite documenting a considerable reduction in payment delays, the intervention may not necessarily enjoy equal success elsewhere, as much depends on the context. Accountability, as one may identify, is often associated with power relations and political connections that can interact in ways that can potentially limit the effectiveness of the interventions that focus on transparency. As argued by Khan and Roy (2019), it becomes necessary to analyze asymmetric power together with this information gap, which varies across contexts. Along similar lines, implementing authorities may resist initiatives to increase transparency and accountability if they disrupt established patterns of rent-seeking (Bussell 2010). On these grounds, replicating the present intervention in other contexts may require contextual alterations to enhance its impact and establish external validity.

Nevertheless, the intervention gives a platform to initiate similar interventions to improve their local-level implementation. Importantly, its simplicity and cost-effectiveness give an opportunity to replicate in the context of other welfare programs that provide publicly available micro-level data. Accordingly, CSOs can engage with local stakeholders and use such interventions to disseminate information. The gains from such interventions can be expected to be substantially higher, given the already established organizational structures at the local level of the CSOs.

Conflict of interest

We would like to confirm that there are no known conflicts of interest associated with this work and there has been no financial and personal relationships with other people or organizations that could inappropriately influence (bias) the outcome.

Data availability

Anonymised, unit-level data along with the do files that are required for replication of the findings presented in this paper can be provided on request.

Footnotes

Notes

Upasak Das (corresponding author) is a presidential fellow in the Economics of Poverty Reduction, Global Development Institute, University of Manchester, and an affiliate at the Centre for Social Norms and Behavioral Dynamics, University of Pennsylvania, Philadelphia, PA, United States; his email address is [email protected]. Amartya Paul is an assistant professor of economics at the XIM University, Bhubaneswar, India; his email address is [email protected]. Mohit Sharma is a doctoral scholar at the Madras School of Economics, Chennai, India; his email address is [email protected]. The authors benefited from the comments from three anonymous referees and the editor. The authors thank David Fielding, Kunal Sen, Anirban Mitra, Sattwik Santra, Srikanta Kundu, Thiagu Ranganathan, Chakradhar Buddha, Anuradha De, and numerous seminar participants at UNU-WIDER; University of Manchester; University of Calcutta; Centre for Development Studies, Jadavpur University; Indian Statistical Institute, Kolkata, XIM University; Bhubaneswar and Indian Institute of Management, Ahmedabad; for their comments. The authors also thank the Libtech team, along with Aastha Ahuja, Diwakar Mantri, and Sushmita Chakraborty, for their help with the preparation of data and maps, and express special gratitude to the interviewers, supervisors, and respondents for their cooperation with data collection. An earlier version of this study was published as UNU-WIDER Working Paper 21/2021. A supplementary online appendix is available with this article at The World Bank Economic Review website. This work is financially supported by the Tata Trust (grant number RLC-PPP-CORD India 20160922).

References