What Are the Headwaters of Formal Savings?
Experimental Evidence from Sri Lanka
Michael Callen
University of California San Diego
Suresh de Mel
University of Peradeniya
Craig McIntosh
University of California San Diego
Christopher Woodruff
Oxford University
June 2018

JEL Codes: O16, D14, G21
Abstract.
The world’s poor are seeing a rapid expansion in access to formal savings accounts. What is thesource of savings when households are connected to a formal account? We combine a highfrequency panel survey spanning two and a half years with an experiment in which a Sri Lankanbank used mobile Point-of-Service (POS) terminals to collect deposits directly from households
each week. We find that the headwaters of formal savings lie in sacrificed leisure time: households
work more, and improved savings options generate an increase in labor effort in both selfemployment and in the wage market. The results suggest that the labor allocation channel is an
important mechanism linking savings opportunities to income.
Keywords: savings, intertemporal labor supply, household decision-making, high-frequency surveys.

1. INTRODUCTION.
There is currently a strong push - in developed and developing countries alike - to provide
financial services that bring the savings of the unbanked into formal institutions. The surge ininterest stems from a recognition of the potential of formal savings to improve the efficiency of theoverall economy by increasing the depth of financial markets, and from increased understanding of
the potential of formal savings to improve the lives of people, most of them poor, who do not use
banks. Half of adults worldwide remain unbanked, but 35 percent of the unbanked report obstacles
to saving that can be overcome by improvements to products and regulation (Demirguc-Kunt andKlapper, 2012). Several recent studies suggest that overcoming the obstacles to savings can lead tovery large positive effects on household expenditures (Kast et al., 2012; Dupas and Robinson 2013;
Brune et al., 2016; Prina 2015; Schaner 2017).
The reasons behind these substantial impacts of formal savings on the well-being of thepoor have been the subject of a great deal of theoretical and empirical work. Much attention has
been focused on understanding why individuals fail to achieve their own savings goals, and how
well-designed financial services help overcome these obstacles. Potential impediments to savings
include problems with self-control arising from time-inconsistent preferences (Laibson, 1997) andother-control issues arising from pressure to make transfers to spouses or peers (Anderson andBaland, 2002). Commitment products (Benartzi and Thaler, 2003; Ashraf, Karlan, and Yin, 2005)
and savings accounts that provide women greater autonomy over savings (Ashraf, 2009; Schaner2017) may overcome these obstacles. Even those models that use a neo-classical framework to
explain the large effects of recent savings experiments (such as Dupas and Robinson, 2013) typically
invoke production function non-convexities that prevent individuals from making high-returninvestments in productive inputs without savings instruments that allow them to accumulate enoughcapital. Under this framework, tools that help entrepreneurs save can have transformative effects by
allowing people to make lumpy investments that provide higher steady-state returns and, thereby,
enable them to escape low-investment poverty traps (Banerjee and Newman, 1993).
Studies of savings products targeting the poor have paid less attention to an older neoclassical explanation for the impact of new savings technologies: even with time-consistentpreferences and a concave production function, savings interventions that generate an increase in
the effective real interest rate will encourage intertemporal substitution, increasing the incentive toearn today so as to enjoy interest-driven consumption in the future. This logic is characteristic ofworkhorse macroeconomic models such as Lucas and Rapping (1969) and Blanchard and Fischer
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(1989), and places emphasis on labor rather than investment as the pathway that connects improved
savings options with increased incomes.
In this paper, we present an experiment providing a powerful inducement to save. We
combine the experiment with detailed, high-frequency surveys to capture the time path of changes incash flows within households as money begins to flow into formal savings. Our experimental sample
comprises 389 treatment and 406 control households who we survey periodically over two and ahalf years. We attempt to answer a simple question: what are the headwaters of formal savings?
Different potential explanations imply distinct signatures in terms of the timing and nature of intrahousehold cash flows, allowing our high-frequency data to provide an informative account of thecausal pathways behind savings impacts. If overcoming self-control problems related tocontemporary consumption is key, we should find the headwaters of formal savings in decreased
consumption. If other-control is central, then formal savings will flow from decreased net intrahousehold transfers and potentially from decreased use of collective informal savings products that
increase savers’ autonomy. If non-convexities in production are the driver, we will observe an initialtransition period during which consumption, net transfers, or other investments decrease so as togenerate savings balances, followed by lumpy investments in productive assets and then an increase
in income resulting from improved marginal returns on capital. If the intertemporal substitution
story is operative, we should instead see an immediate increase in labor as households respond tothe higher interest rate. Of course, more than one of these mechanisms may be relevant.
We collaborated with a Sri Lankan bank to send staff door to door to offer households aweekly savings deposit collection service using a mobile Point-of-Service (POS) handset that prints
out deposit receipts on the spot. The service was provided to randomly selected unbanked
individuals living at least 5 kilometers from their nearest bank branch.1 Starting five months before
the collections began and continuing monthly for 13 months afterward, and again 19 and 25 months
afterward, we collected detailed survey data, including income, expenditures, transfers, and labormarket activity data. We use the detailed survey data to analyze changes in households’ cash flows
and labor allocations resulting from the savings treatment. The methodology we use is along thelines of the analysis in Samphantharak and Townsend (2009).
1

The intervention is designed to open new savings opportunity for unbanked individuals. We screened ourexperimental sample such that participants satisfied three criteria: (i) they received income at least weekly, e.g.,
were self-employed or daily wage workers; (ii) they were accessible by a motorcycle and; (iii) they were unbanked,
i.e., they had no formal bank account or had not used a bank account in the previous month.

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The weekly POS deposit collection service led to large increases in formal savings. The
number of transactions with formal financial institutions per month quadrupled as a result of thetreatment; the flow of savings into bank accounts almost doubled; and overall savings increased bymore than 15 percent, or about US$7 per month. The treatment generates an immediate increase intotal household income, and in earned income, in particular. The increased income is used to fundthe increased savings and to pay off loans. We see no change in transfers to or from otherhouseholds, and no decrease in consumption.
The suggestion that increases in income are a source of savings rather than a result ofsavings leads us to examine labor market activity in more detail. The survey data for the main
respondents show that labor hours, and, particularly, hours worked on the wage market jump withina month of the offering of the treatment.2 Moreover, an immediate shift out of self-employment andinto wage work occurs, with the occupational shift persisting over time. In aggregate, we find anincrease in earnings from wage work, and no increase in self-employment income. The lack of any
lag in the savings and income effects implies that the saving-invest-earn channel highlighted in theexisting literature cannot be the only pathway through which savings accounts affect income.
Instead, our data are consistent with the neoclassical model in which new savings options represent
a change in intertemporal prices which affect the intertemporal allocation of consumption and,correspondingly, of labor (Blanchard and Fischer, 1989).3 Indeed, a calibration exercise suggeststhat the labor response we observe in the data is in line with what should be expected from the 5
percentage-point increase in real interest rates that is part of the account offered in our treatment.
This shift from self-employment to wage work, which ran counter to our initial expectations,is, again, consistent with the neoclassical model if households wishing to expand labor hours
confront constant marginal returns on the wage market and diminishing marginal returns in selfemployed microenterprises. To examine this possibility further, we split the sample into threesubsamples based on activities reported during the baseline period: 1) individuals who are selfemployed in the retail and service sectors, where we posit the ability to expand is limited given the2

Nearly all wage jobs in this setting are day labor jobs, typically agricultural work that is paid daily in cash. Having a bankaccount does not directly increase access to these jobs. It is therefore unlikely that the increase in wage market hours is amechanical consequence of having an account.
3 Banerjee et al. (2015) develop a model to structure an analysis of the effects of an expansion of a microcredit programin India. They also show that the increase in credit can lead to an increase in labor. Intuitively, their effect comes fromthe fact that credit makes the purchase of durable goods possible, and hence raises the marginal benefit of consumption.
In the Blanchard and Fischer framework, savings accounts increase the labor effort immediately because the higher
interest rate increases the benefit of future consumption.

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very local markets typical in our rural setting; 2) those active in the manufacturing sector, where sales
are more easily made outside the local area; and 3) those not involved in any self-employment. We
find that those who were self-employed in retail and services are the source of all movement out ofself-employment into wage work, and those who were self-employed in the manufacturing sector are
the source of all increases in income and savings. The initial increase in income comes from anincrease in hours worked, but also, apparently, from an increase in intensity of work per hour. The
data provide evidence that the labor / leisure channel is an important piece of the answer to boththe question of the headwaters of savings and the question of the channel through which theavailability of savings services affects expenditures. Note that we are not the first to explore thelabor channel. Dupas and Robinson (2013a) examine the impact of providing a non-interest-bearing
account to self-employed workers in Kenya. The market vendors in their study make substantial useof the savings product, and Dupas and Robinson show that their working hours increase by justover five percent of the control group mean (p. 178, Table 3), an effect that is highly insignificant
given their standard errors. Additionally, Schaner (2017) examines the effects of providing a highpowered savings subsidy on labor effort three to four years after the incentive expires. She finds a
positive though insignificant increase of about 15 percent above the control group mean in hours
worked in the business (Table 4). Bruhn and Love (2014) find that the opening of 800 Banco Azteca
branches in rural Mexican communities ̶ which substantially increased both formal borrowing andsavings opportunities ̶ increased employment by 1.4 percent over the pre-opening level (Table 4).
Labor hours may have increased for reasons other than the increase in interest rates. We
examine the importance of several other channels. In a second experiment, we transitioned some of
the control zones to collection through local lockboxes rather than door-to-door collection. We use
this experiment to test whether the peer pressure and reminders that accompany door-to-doorcollection play a role in increasing income and savings. The data show that the lockbox treatment
also led to increased labor market participation. These efforts, however, do not result in moresavings for this group. This suggests some potential role for either peer pressure or limited attention.
The literature also points to savings accounts allowing participants to deal with other-control
or self-control issues. Our data show no significant role for other-control, but we do find someevidence that the collection services disproportionately benefitted those most subject to self-control
issues. To explore self-control, we use individual information on the time consistency of preferences
at baseline, along with a list of experimental questions on the consumption of “sin goods.”
Regarding other-control, the product allows the saver to interact privately with a bank staffer to4make a deposit into the account solely in his or her own name, and thus may improve the ability of
the account holder to deny the demands of others for transfers. Baseline survey questions onwhether the participant has control over savings decisions in the household show that the treatment
effect is not significantly larger for those initially lacking control over savings decisions.
Finally, we worried that the availability of formal savings mechanisms might crowd out
informal savings. Rotating savings and credit associations, referred to locally as seetus, are a common
means of informal savings in our sample. We exploit an experiment in which we randomized theintensity of treatment (Crépon et al., 2013; Baird et al., 2017) within the seetus used by study
households at baseline to examine the interaction between formal and informal savings. We findthat, if anything, our collection services and seetus prove to be complements in this setting. Overall,our results highlight the ability of savings to have a transformative effect on income even in anenvironment in which non-convexities in production do not appear to play a dominant role.
The remainder of the paper is structured as follows: Section 2 presents the background anddesign of the experiment, and Section 3 develops a simple framework to organize the analysis.
Section 4 presents the impact of the program on savings, the “headwaters” of personal liquidity, andon entrepreneurial activity. Section 5 investigates the extent to which increases in peer pressure or
improvements in self- and other-control may also be responsible for generating our results, andSection 6 concludes.
2. SURVEY AND EXPERIMENTAL DESIGN.
This section describes the procedure used to create an experimental sample and the protocol used toassign households to treatment. Our objective in sampling was to identify unbanked individuals who
lived in remote households (accessible by motorcycle), and who received income at frequentintervals (and, as a result, were likely to benefit from weekly deposits). Figure 2 provides a complete
overview of our study design.
2.1. Sampling.
In 2008, Sri Lanka’s National Savings Bank (NSB) began a program of remote deposit
collection targeted at business owners within 1 kilometer of NSB branches. The collections are madeusing a wireless Point-of-Service (POS) terminal carried by a bank agent traveling by motorcycle.
The POS terminal allows deposits to be recorded in the bank’s accounts immediately; at the same5

time, the depositor receives a deposit confirmation showing the new account balance. Agentstypically visit a given merchant once per week.
For this project, NSB agreed to provide branches in the towns of Bandarawela andMahiyangana with an additional POS terminal and agent to make collections from more remotely
located rural areas. While NSB’s goal for the initial POS program was to reach highly liquidmerchants, the goal of this project was reaching lower-income, under-banked households.
2.1.1. Sampling Criteria. We agreed on selecting areas by first going 5 kilometers to 15
kilometers from the branch along the main roads leading away from each of the two towns, andthen taking households within 1 kilometer of the main road. Figure 1 maps the study households
around Bandarawela and Mahiyangana and shows their proximity to the road network and theirdistance to NSB branches; this confirms that nearly all households selected for the study lived
between 5 kilometers and 15 kilometers from the nearest NSB branch.4 We began by conducting alisting exercise, visiting every household in the sampling area, and listing all economically active
adults aged 18 to 65 in the households. The screening survey collected information on: thefrequency of pay from employment; whether the individual had a bank account, and, in the case ofindividuals who did have a bank account, whether the individual had made any banking transaction
within the past month; and whether the individual participated in one or more seetus, the rotating
savings and credit associations that are common in Sri Lanka. A total of 5,081 individuals in 3,657
households were listed during this exercise.
Before drawing the sample, we eliminated individuals whose profile made the weekly POS
collection either infeasible or inappropriate. The first group included those living in houses that
could not be reached by motorcycle. By this criterion, the house had to be within 500 feet of a point
accessible to the agent via motorcycle. We also eliminated those who received income payments lessfrequently than once per week. The weekly collection is of most value where income streams areeither daily or weekly. In practice, this means the sample is largely made up of individuals who areeither self-employed or daily wage workers. This is important to keep in mind because the daily paid
workers may have more ability to change hours worked than, for example, monthly salary workers.
Finally, we eliminated those who had made a deposit in a bank account within the past month, since
we expected the behavior of those using the bank regularly would not be affected as much by the

4 Appendix Figure A1 depicts the distribution of distances between study participants and the nearest bank branch

traveling along the nearest road.

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deposit collection services. Note that the last two criteria were applied at the individual level, so that
if any listed member of the household received income payments at least weekly and had not used abank account in the previous month, that individual remained eligible even if the criteria eliminatedother household members. We also only sampled prime-age working individuals, defined as being
between 18 and 65.
2.1.2. Creating Zones. NSB quite reasonably felt that their agents could not refuse adeposit from anyone approaching them while making their rounds. In the region of our experiment,
the households are scattered into small clusters rather than distinct villages. Therefore, we conducted
the randomization at the level of clusters of houses. We identified 156 distinct clusters ofhouseholds (hereafter referred to as “zones”), separated by at least a stretch of road long enough tomake spillovers between treatment and control zones unlikely. In addition, in this area, agriculture is
the primary activity in the sampled areas around both towns. Near Bandarawela, the main crops aretea and vegetables; near Mahiyangana, the main crops are rice and vegetables.
2.1.3 Sampling Within Zones. With these zones in mind, we selected the experimental
sample in several stages. Because we were particularly interested in the interaction between formal
and informal savings – specifically whether the introduction of deposit collection changes seetu
participation – we began by selecting a sample of individuals who participate in a seetu in which all of
the members reside within 1 kilometer of the initial respondent. We refer to these seetus as “close
seetus.” The first step was to select an individual in each cluster who is a member of a close seetu.5
There were 93 zones with at least one member of a close seetu. We randomly selected one memberof a close seetu in each of these 93 zones, and then re-surveyed these 93 individuals to collect the listof names of other participants in their seetu. We selected only one individual per zone to ensure that
seeds did not come from overlapping seetus. This list of names permitted us to “snowball” sample
other members of their seetu. If individuals brought in via the snowball did not meet the othersampling requirements, we sampled them nonetheless.
The second step of the sampling was aimed at achieving gender balance. The listing yielded amuch smaller number of women than men meeting the employment / earnings frequency criteria
explained in 2.1.1 above. We also required that women eligible for sampling at this stage were not amember of a close seetu. We selected up to five women in each of the zones. There were more than
five women in only two of the 156 zones, implying that we had selected essentially all the women in
5 These individuals also satisfied the sampling requirements of being unbanked and being accessible by motorcycle.

7the comprehensive listing who qualified according to the earning frequency and bank transaction
criteria. We then extended the sample by selecting an additional one or two men randomly fromeach zone.6 Finally, for each close seetu we then randomly selected 20 percent of its membership toparticipate in the survey. The resulting intake sample of 829 has 432 women and 397 men.
We sampled only one individual per household. Between August 2010, when the baseline
was conducted, and November 2010, when the randomization was carried out, 34 respondents
attrited from the survey, leading to an experimental sample of 795 who were included in the
randomization. Twelve households did not answer at least two post-treatment survey waves, ourcriterion for inclusion in the panel analysis, leaving us with a final sample of 783 for analysis. In all,44 percent of the sample (344) are members of close seetus, with the remainder (439) coming fromthe broader random selection.
2.2. Treatment Assignment.
The randomization of collection services was carried out at the zone level, stratifying andbalancing on data from the baseline survey. We stratified on quartiles of total savings balances,
above/below median of household expenditures and whether the zone included a close seetu. We
then re-randomized to achieve balance on a set of variables related to savings behavior and income
generation.7 The study sample thus consists of 78 zones with 389 individuals for treatment and 78
zones with 406 individuals for control.8
In December 2010, we offered to open accounts at the local NSB branch for those selected
into treatment.9 The account opening required that the individual come to the bank branch. During
the first two weeks of the month, project research assistants were at the bank branches to help
participants with the required paperwork. The minimum balance required to open an account is 500
6Because some zones have no males, we select up to two additional males per zone and use those to fill the remaining
sample.
7 Specifically, to achieve balance we randomize using the “big stick” approach, whereby randomizations are redrawn
until the minimum p-value among a pre-specified set of balance variables is greater than some threshold (see Bruhn and
McKenzie (2009) for a discussion of the advantages and disadvantages of this approach. In our case we select a
threshold of 0.21. The variables on which we balanced were: agricultural employment, education, gender, present bias,
monthly income, whether the individual had a formal bank account, balances of formal and informal savings, total andinformal monthly savings amounts, and whether anyone in the household was either a grantor or recipient of an
outstanding informal loan. We also examine whether our core results are robust to using randomization inference, where
potential treatment assignments satisfy these conditions.
8
Seetu members who were brought into the study through the listing of all seetu members received treatment based on
their zone of residence, not on the status of their respective seetu seed.
9 If individuals in treatment zones either had an existing account (and so were excluded during screening), or opened one
during the study, they were eligible to use the deposit collection service.

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LKR (~ US$4.50); we paid this for all treated individuals who opened an account.10 Of the 389
individuals selected for treatment, 347 (89 percent) opened an account. POS collection services
began December 13th, 2010, in both branches. One main road from town was serviced each day of
the week.
2.2.1 Unbundling Experiment. Six months into the main experiment, we began a series of
unbundling experiments. In a randomly selected and well-balanced subset of the control and weekly
home visit treatment arms, we worked with participating households to establish locked collection
boxes in each selected cluster of houses. The lockboxes were visited by the NSB agent on a weekly
or bi-weekly basis. Participants were given envelopes and stickers with which to seal the envelopes.
On the stickers, they wrote their account name, account number and the amount of the deposit.
Initially the participants were given several stickers with their name and account number filled in byproject staff; all they had to do was fill in the amount. Participants placed deposits in envelopes anddropped the envelope into the box. The NSB agent came, together with project staff, on a scheduled
day and time with a key to open the box to collect the deposits made by participants. The agent
carried his POS terminal with him, made the deposits on the spot, and then left the receipt for thedeposit in a sealed envelope in a compartment built onto the side of the box. Participants thenreturned to collect the receipt. Thus, the deposits were made into the NSB exactly as in the door-todoor collection, but in a manner that was more efficient for the agent. In practice, since the agent
arrived around the same time on the announced day, participants often came to the box at that timeand made the deposit in person. De Mel et al. (2013) describe the impact on savings of thecollection boxes by using the experiment to parse out the role of habit formation and salience insavings. Here, we use the additional experiment introducing weekly box collection to the control to
try to adjudicate between mechanisms linking deposit collections to changes in labor supply, in amanner we discuss in Section 5 below.
2.2.2 Saturation Experiment. Finally, we exploited the additional listing of seetu members
described in Section 2.1.3. to introduce a randomized saturation experiment to investigate whether
the introduction of a formal savings account affected how individuals interacted with their informal
savings organizations. We began from the group of 39 close seetus that had been selected into thetreatment; in each of these seetus, 20 percent of the membership participated in the household

10 The opening deposit is trivial relative to median income of the participants (22,000 LKR).

the course of the study was approximately 111 LKR per U.S. dollar.

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The exchange rate during

survey. We then offered treatment to (but did not survey) an additional 20 percent of the members
in one-third of these groups, and to an additional 40 percent of members in another one-third of thegroups. With respect to treatment, 45 of the close seetus are untreated, 13 are treated at 20 percent,
13 are treated at 40 percent, and 13 at 60 percent saturation. The comparison of the fortunes of theconstant 20 percent of members studied across the randomized variation in the treatment saturation
allows us to isolate externality effects of formal financial services on the welfare of the membershipof informal savings networks.
2.3. Surveys and administrative data
We conducted a baseline and three additional pre-treatment surveys for the full sample atmonthly frequency between August and November 2010. We randomly allocated 498 households toa sample in which we continued to conduct monthly surveys, and 297 households to a sample inwhich we conducted quarterly surveys. This both reduced survey costs and allowed us at least a
partial test of whether survey frequency affects deposit or aggregate savings behavior. For bothmonthly and quarterly survey groups, we conducted surveys at the defined frequencies throughNovember 2011. We then conducted monthly surveys of everyone in December 2011 and January
2012, and longer-term follow-up surveys in July 2012 and January 2013. Thus, for the monthly
survey sample, we have five pre-treatment surveys and 15 post-treatment (13 monthly and two semiannual) surveys; for the quarterly survey sample, we have four pre-treatment and eight posttreatment (four at quarterly intervals, two monthly, and two semi-annual) surveys. To avoid
confounding the primary results, in the initial analysis we drop the 192 treatment and 150 control
individuals involved in the unbundling exercise described above as soon as their treatment statuschanges. That is, we retain them in the sample until the point when they change from their firsttreatment designation (either control or in-person deposit collection) to lock box deposit collection.
Appendix Table A1 details the timing of the surveys, and shows which surveys are includedin the sample we use here. The result is a full 30 months of data for the core sample (92 zones; 18
months at high frequency) and, for a subsample of 64 zones, data from the 12 months prior to thebeginning of the unbundling experiment. Results are very similar if we use only the sample of 92
zones, but the precision of the short-term estimates improves with the inclusion of the additionalgroup that receives the core treatment for six months. Our analyses use individual-level fixed
effects, and we cluster standard errors at both the zone and survey round using the method
developed by Cameron, Gelbach and Miller (2008) as a way of accounting for both the substantial
10autocorrelation present in high-frequency household data and the effect of local and period-specificshocks. For balance tests using pre-treatment data, however, we cluster only at the zone level.
We undertook this project with the aim of answering the simple but vexing question: what is
the root source of money that is newly brought into the formal financial sector? When people begin
to use formal savings, what other behaviors in the household change to allow this liquidity to bedeposited in a bank? Candidate explanations are: (i) that saved capital is substituted from cash in themattress; (ii) that greater discipline from formal savings causes expenditures to decrease; (iii) thatformal savings come at the cost of informal mutual insurance networks; or (iv) that individuals work
more in order to save. The survey was designed with these sources in mind. The heart of the survey
instrument is a cash flow analysis (see Appendix B for the relevant survey questions) for both thesampled household and the sampled individual, who was always the respondent. To unpack the
headwaters of formal finance, we need to be able to construct balances of financial flows at thehousehold level. Thus, our survey was designed to capture monthly inflows (earned income,transfers from individuals and other transfers) and outflows (expenditures, transfers to otherindividuals, savings and loan payments). While these modules are meant to comprehensively coversources and uses, this module does not capture expenditures related to business and agriculturalinvestment, which have their own detailed modules elsewhere in the survey.11
Because we expect individual members of a household to have better information about
their own earnings and transfers than those of other members of the household, we also ask about
the respondent’s individual cash flow. Questions asked of the individual respondent net out her/his
transfers to and from other members of the household to calculate personal income, and thenallocate this personal income to individual consumption items. Significantly, we ask the directquestions on the amount saved through various means (in the NSB account, in other formal
accounts, in cash, in seetus, etc.) with regard to the individual respondent. Since savings decisions arelikely made at the household level in many households, we make use of the aggregate householdincome and expenditure data. But we also use the more detailed individual data to focus on theoutcomes of the individual respondent. The enumerators were trained to check that the sources of

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Both the monthly and quarterly surveys asked respondents about income and expenditure flows during the previous
month. We asked about the previous month even in the quarterly survey to minimize recall issues. For investments,
including business investments and financial investments in jewelry, loans, etc., the questions were asked with reference
to the time since “the previous survey” (i.e., the previous month for the monthly sample and previous three months forthe quarterly sample).

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cash matched the uses of cash for the individual. Where the initial responses yielded differences, theenumerators pointed out the inconsistency and re-asked the income and expenditure questions.12
The decision to focus the detailed earnings questions on the activities of the participant
him/herself represents a tradeoff. On the one hand, we focus on data the participant knows best.
On the other hand, we will be somewhat limited in answering the “headwaters” question if thechanges in income, expenditure, or savings come from changes in the behavior of other members of
the household. That is, if we identify that increases in savings in banks are associated with increases
in transfers from the spouse, we know only indirectly whether the spouse increased his income (andif so, we do not know how) or decreased his formal or informal savings. But the aggregate
household data allow us to identify the sources of changes in savings arising from income andexpenditure patterns of other household members up to a point.
In addition to the detailed survey data, we have administrative data from NSB for theaccounts directly linked to the project. These detail each deposit and withdrawal, as well as othertransactions (e.g., interest payments). We use the institutional data in this paper to study thedeterminants of uptake and account usage (Table A4) and institutional balances (Table 2); allremaining impact tables rely exclusively on information from the household surveys.13
2.3 Balance and attrition
Table 1 examines the balance of the experiment. Treatment was assigned at the zone leveland stratified on whether a zone contained a close seetu (meaning that all the members of the seetu
were resident in that zone), as well as on average household expenditures and baseline averagesavings in each zone. Stratification was done using baseline (round 1) data, and we test for balanceusing the remaining pre-treatment rounds (2-5). Table 1 shows balance on a range of variables
measuring savings, income and expenditure. Only one of the 35 difference-in-means tests, formonthly savings in cash, shows a statistically significant difference. However, while not significant atconventional levels, some baseline differences are fairly large. For example, earned income over theprevious month is about 1787 LKR lower in the treatment group compared to the control, which is
12 Samphantharak and Townsend (2009) assign mismatches in monthly income and expenditure to changes in cash
holding. We measure cash holdings along with other financial assets. To the extent that individuals do not want to reportincreases in cash holdings, they might be tempted to increase reported expenditures instead. However, over years of
conducting surveys in Sri Lanka, we have found respondents to be generally very willing to discuss financial matters
openly, and we do not detect any patterns in the data which suggest significantly misreported cash balances.
13 Our analysis of a subsequent unbundling experiment takes place within the treatment group, and hence makes
extensive use of the institutional data; see de Mel et al. (2013).

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similar in absolute value to the earned income effect (after winsorizing) that we estimate below. We
use individual fixed effects throughout our analysis to help address potential imbalances.
Appendix Table A2 examines correlates of survey attrition. Overall, the resurvey rates were
high. Ignoring attrition from the sample that occurred prior to the assignment of treatment, only 12of 795 individuals were not surveyed at least twice pre-treatment and twice post-treatment (ourcriteria for inclusion in the panel sample). We also examine the 20 individuals who did not complete
the last high-frequency survey (wave 18 in January of 2012). Most importantly, attrition does notdiffer in the treatment and control groups whether we examine simple differences between the twogroups or whether we control for other covariates.
Despite the overall balance of the experiment, the number of zones to which treatment was
assigned was relatively small (156), and, due to sampling rules intended to locate as many selfemployed females as possible, there is substantial cross-zone variation within the sample in variables
such as gender and seetu participation. For example, 28 zones contain all-male and 10 zones allfemale core respondents. Potentially, due to this clustering of gender by zone, the experiment is
imbalanced when we look among men only or among women only.14 Appendix Figure A2 shows thedensities of one of the most severely imbalanced variables, the log of personal income. While theimbalances are not visually severe, the figure illustrates how the problems within exclusively maleand exclusively female subsamples counteract each other to lead to a full treatment/control
comparison that is well balanced.15
Given this issue, we pursue several other approaches to test whether our experiment
provides clean identification. First, we test for subgroup balance using the three self-employment
classifications that are explored later in the analysis (self-employed in manufacturing, self-employedin trade and services, and not self-employed). Appendix Table A3 demonstrates that the study iswell-balanced within subgroups. Second, we exploit our multiple pre-treatment survey waves tosubject the experiment to a test of parallel trends. Appendix Table A4 estimates intercept and time14

To perform randomization inference, we re-ran our treatment assignment protocol 1,000 times to obtain acorresponding number of artificial draws. This allows us to examine how the actual subgroup balance of our experimentcompares to the distribution of subgroup treatment/control differentials that could have been obtained given our
sample and randomization routine. This illustrates that we were simply unlucky in realizing a group of treatment females(males) that are substantially richer (poorer) than the control (p-value < .01 for highly imbalanced variables such as
household income among males).
15
Interestingly, if we use only the data from the round 1 survey (on which the stratification was conducted), no
significant signs of subgroup imbalance are observable. The imbalances result from a gap that opens between treatment
and control within men and within women in rounds 2-5, and hence is only observable because we collected multiple
high-frequency pre-treatment surveys as suggested by McKenzie (2012).

13

trend slope differentials between the treatment and the control prior to treatment. This table
presents the results of 68 tests; none of the intercept terms are significant, one slope term issignificant at 90 percent and one (total consumption) at 95 percent. This suggests that the pretreatment rates of change in the treatment and control were broadly comparable. Nonetheless,because of the imbalance within gender, we avoid analysis by gender and discuss imbalance issues
carefully when we move to the analysis of the seetu experiment in Section 5.
3. THE INTERTEMPORAL SUPPLY OF LABORA substantial literature in macroeconomics examines the role of interest rates in governing
the intertemporal allocation of labor (Lucas and Rapping, 1969). Central to these models is the ideathat increasing the real interest rate raises the relative return to working in the present relative toworking in the future. In this section, we provide a standard model to develop this point.
Consider an agent who consumes !! and works ℎ! in period ! with utility
(1)

!

!

! !! , !! = (!!!)! u !! − ℎ! .

In period ! the agent has wealth !! , which is a function of the prior period’s assets and wage
income.
(2)!! = 1 + !! !!!! + !! ℎ! − !! .

Several simplifying assumptions are worth noting. First, we ignore the issue of risk in the income
stream. Increasing risk would lead to precautionary savings, but, because our experiment changes theinterest on savings in isolation, any effect of treatment on the level of precautionary savings is likely
to be second order. Second, we assume that utility from consumption and disutility of effort are
additively separable, implying that the marginal utility of consumption is independent of the disutilityof effort. We make the standard assumption of positive and concave consumption in utility. Finally,
we assume that wage rates are not affected by the experiment. Because the treatment group is asmall part of the regional population, we take the increase in the interest rate as isolated from any
effect on wages or prices. The Euler equation governing the intertemporal allocation of labor is:
(3)

16

!!
!!!!

=

!!

1 + !!!! !

!

!!! (!!!)!
!!! 16.

The corresponding Euler equation for the intertemporal allocation of consumption is14!!(!")!!(!!!! )=!!!!!!
(!!!).

If the POS savings treatment provides an improved savings option, 17 then for theexperimental treatment group, the increase in r, holding other parameters fixed, represents anincrease in lifetime wealth for those in the treatment group with positive savings balances. The
treatment thus implies an income effect in addition to the substitution effect. In this formulation,!

the elasticity of the labor ratio with respect to the gross interest rate 1 + !!!! is !!! and so is afunction of the curvature of the disutility of effort function. The Euler equation communicates astandard feature of these models: if the cost of effort function is convex (! > 1), then thesubstitution effect will dominate the income effect such that an increase in the future interest rateshould lead to more work in the current period relative to the future period.18 That is, holding theperiod-specific wage rates constant, the increase in r will lead to an increase in hours in period t
relative to period t+1.
4. RESULTS.
The changes in labor supply and intertemporal consumption that come from the model are
driven by an increase in the interest rate on savings. If the collection services did increase theeffective interest rate realized by program participants, then we should observe both a robust takeup of the product, and an increase in total savings. These outcomes are the analogous to the firststage in the experiment. We begin, then, by looking at these preliminary outcomes.
4.1. Uptake and Usage.
Appendix Table A5 uses pre-treatment averages (data from rounds 1-5) to predict
subsequent uptake and usage of the accounts among the 389 individuals offered the treatment.
Account usage appears progressive in that those most likely to make any deposit are low-income
females who score poorly on the digitspan test. At the same time, a strong predictor of use of our
accounts is a history of formal savings prior to the initiation of the experiment. Low-expenditure
households use the accounts most frequently for both deposits and withdrawals, but none of ourdeterminants are significant in explaining the total number of transactions in program accounts.
17

The NSB accounts paid an interest rate of 5 percent per year. Plausibly, the effective interest rate on cash held athome (a common situation in our sample) is negative because money might be stolen or used by someone other than
the respondent.
18
There are, similarly, income and substitution effects in consumption. The increase in r favors consuming
tomorrow over today, but the increase in wealth increases aggregate lifetime consumption.

15

Among those who make deposits, the two significant determinants of the log of deposits are having
more education and having higher formal savings at baseline. Those with high baseline savings also
make significantly more withdrawals from program accounts, however, leading to final savingsbalances that are not significantly higher than those who had no formal savings at baseline. Finalsavings balances are strongly progressive in expenditures (meaning that poor households savesignificantly more through the program than wealthier households even in absolute terms), andbaseline seetu participation is also predictive of lower final savings balances. The progressivity of final
savings balances is encouraging, indicating that weekly home visits with the POS terminals are
particularly effective at generating deposits from low-income households.
4.2. Savings Impacts.
The primary objective of the deposit collections is to increase bank savings. We estimate theimpact of deposit collections on banking activity running regressions of the form:(4)!!"# = ! ∙ !"#$%#&!" + !! + !! + !!"# .

!!"# is the individual savings outcome, where ! refers to individual, ! to the zone, and ! tothe month of the study; !"#$%#&!" is a dummy variable equal to one for individuals in treatment
zones after month six of the study (January 2011), !! are individual fixed effects and !! are month
fixed effects.19 We note that all results presented in this paper, other than the results in Table 1, arefrom regressions that include individual and month fixed effects. Table 2 provides estimatescorresponding to this specification. Panel A columns (1) – (3) uses administrative savings data as
outcomes and columns (4) – (7) uses survey data as outcomes. We note that, throughout the paper,
wherever we report control means, we do so for the untreated group pooling across all waves ofdata collection. Estimates in column (1) indicate that monthly bank transactions increase by 1.73
from a base of 0.01 and, correspondingly, in column (2) we see that monthly deposits increase froma base of 1.68 LKR by 1,143 LKR; column (3) shows that monthly deposits minus withdrawals
increase by 425 LKR from a base of 0.85 LKR. The administrative data, therefore, indicate asubstantial increase in program savings as a result of treatment. Turning to estimates based on

19 The specification therefore provides difference-in-difference estimates of the effect of treatment. Correspondingly weomit a dummy variable equal to one for all subjects in the treatment group and a dummy variable equal to one for the
post-treatment period, as those are full accounted for by the individual and time fixed effects. Standard errors in all
regressions are clustered at the zone level (to account for the design effect) and at the survey wave level (to account forcontemporaneous shocks in outcomes) using the technique of Cameron, Gelbach, and Miller (2011).

16

survey outcomes, column (4) indicates that treatment quadruples reported transactions from acontrol average of 0.5 transactions per month to a treatment average of over two per month in thetreatment group. Column (5) indicates a near doubling of bank savings. Column (6) suggests nocorresponding reduction in informal and cash savings, and column (7) suggests indicates a 16.9
percent increase in total savings. The degree of the effect of deposit collections on monthly banktransactions is also depicted in Figure 3. Despite a large increase over the control group, the data
show that treatment households only make deposits through the collectors during half of the weeks
in which visits occur. Comparing columns (3) and column (5) suggests that treatment might also leadto an increase in deposits in other formal accounts. While we would be cautious about that
conclusion – both because the difference of 265 LKR per month is not significantly different fromzero and because the survey data may be noisier – the data suggest that the NSB savings are notcoming directly from other formal savings accounts.
We re-randomized in this experiment to achieve balance. To address potential concerns for
inference, Appendix Table A6 repeats the estimates from Table 2, including p-values obtained using
randomization inference.20 This approach tests a null of no treatment effect for any participant in the
study. Under this null, we can generate a sampling distribution for ! simply by estimating
specification (4) on any treatment assignment that satisfies our assignment protocol.21 This approachyields similar conclusions. In particular, we reject the null of no effect on total savings for any
participant at the 5 percent level.
This preliminary look at savings therefore indicates that treatment leads to a statisticallysignificant and economically meaningful increase in total savings. There is no evidence that thesavings deposited in the NSB account are crowding out either other formal savings or informal
savings. The increase in savings suggests that participants viewed the collection services as a
substantial change in their portfolio of financial services, opening the possibility that the treatment
led to more fundamental changes in their behavior.
4.2.1 Savings Impacts by Time Period. After the introduction of treatment, we followed thesubjects for two years, allowing for an examination of whether participation fluctuated over time.
We estimate these effects using regressions of the form:
20 We point the interested reader to Gerber and Green (2011) for a full description of this approach to inference.
21 In practice, we obtain 1,000 potential treatment assignments.

17

!!"# = !! ∙ !"#$%#&!,!!! + ϕ! ∙ !"#$%#&!,!!! + ϕ! ∙ !"#$%#&!,!!!" + ϕ! ∙(5)!"#$_!"#$!#%!,!" + !! ∙ !"#$_!"#$!#%!,!" + !! + !! + !!"# .
Where variables and subscripts are defined similar to specification (4), except !"#$%#&!,!!! is adummy variable equal to one for zones in the treatment group for months 1-4 of the post-treatment
period (January 2011 – April 2011), !"#$%#&!,!!! is a dummy variable equal to one for zones in thetreatment group for months 5-8 of the post-treatment period (May 2011 – August 2011), and so on.
!"#$_!"#$!#%!,!" and !"#$_!"#$!#%!,!" are dummies for the treated group six and 12 months
after the door-to-door treatment ended, and weekly home visits were replaced with weekly box
pickup at the zone center. These post-treatment coefficients measure the impact of weekly box
pickup when individuals have first been habituated to save by a year of weekly home collections.
Examining the period-by-period impacts in Panel B of Table 2, we see that once the weekly
home visits end and the zone switches to weekly box pickup we continue to observe significantly
elevated financial transactions and NSB deposits relative to the control. The net flow of funds into
NSB accounts reverses, however, and the treatment group eventually withdraws money fromaccounts at a higher rate than the control. Total savings flows drop back to the control level within
12 months, consistent either with households approaching a new steady state given a continued
decrease in effective savings interest rates or with boxes having a more modest impact on totalsavings than deposit collection at the home.22
4.3. Headwaters
Having verified that the experiment had the intended effect of increasing the aggregate
savings of the participants, we can now ask the central question for which the experiment was
designed: where does the increase in savings come from? The three immediate possibilities are: 1) a
reduction in expenditures; 2) an increase in earned income; 3) and increase in net transfers fromothers inside or outside the household. Previous research gives some support for at least the firsttwo possibilities. Banerjee et al. (2015) find that microfinance clients investing in microenterprises
reduce expenditures on “temptation goods” and increase the purchase of durable goods. And both
Dupas and Robinson (2013a) and Prina (2015) find that expenditures increase with the introduction

22

Section 5.1 provides additional evidence as to the impact of the collection boxes on household behavior.

18

of savings products that are similar to the one we examine. Both of these studies find incomesincreased by an economically meaningful but statistically insignificant amount among those offered
the savings accounts.23 Our high-frequency data provide us with the statistical power to present a
detailed answer to the “headwaters” question. We take a “sources and uses” accounting approach toanalyzing the effect of the POS treatment on outcomes, beginning by examining the sources anduses of funds at an aggregate household level. We estimate these impacts using a specification similar
to equation (1) above, except with the cross-sectional unit, indexed by the subscript !, being thehousehold rather than the individual. The first column of Table 3 shows the treatment effect on
total household income from all sources, including earnings, remittances from domestic and foreignsources, and other flows (including loans, government program payments, and the like). Panel A
shows the effect of treatment using the raw data, and Panel B shows the treatment effects using data
winsorized at the 99th percentile. Treatment has a substantial positive effect, increasing total
household income by roughly 10 percent of the mean in the control group; the measured effect is ofsimilar magnitude using either the unwinsorized or winsorized data, though it is statisticallysignificant only with the winsorized data.
Columns 2, 5, and 6 disaggregate the household income into three sources, which comedirectly from survey responses: earned income (Column 2), remittances from domestic and foreignsources (Column 5), and other household inflows, including loan receipts, seetu payments,
government program payments, and the like (Column 6). In the unwinsorized data, just over 90
percent of the increase in household income comes from earned sources. Winsorizing the data
reduces the effect of earned income somewhat. Combined with a larger estimated treatment effecton total household income, this implies a larger role for other household inflows. However, eventhough the measured flow from other sources is higher in the winsorized data (Column 6, Panel B),
the treatment effect on these flows remains insignificant.
Columns 3 and 4 split the increase in household earnings into changes in income reported by
the respondent, and a residual, which we label changes in earnings from other household members.24
Using either the unwinsorized or winsorized data, the change in the respondent’s income is about
twice that of other household members. We return to a further analysis of the respondent’s income
below. Understanding the source of these new (and fairly immediate) earnings is of key interest.
23

Dupas and Robinson show results on enterprise revenue rather than on profits.
The baseline survey included a household roster for which the respondent reported the occupation, hours worked,
and income for other household members.
24

19Columns 7-10 of Table 3 report the estimated treatment effect on uses of funds in thehousehold. Reasonably, inflows could be consumed, saved, or transferred outside the household,and so we measure these dimensions of potential use. There are non-trivial measured effects on
savings in both the unwinsorized and winsorized data, but the estimated savings effect is statisticallysignificant only in the winsorized data. The unwinsorized data also show some evidence of anincrease in loan repayments. In aggregate, the treatment effects on the sources and uses of funds
balance reasonably well, with the changes in uses reflecting 70 percent of the increase in sources offunds in both the winsorized and unwinsorized data. One possible explanation for this “leakage” isthat there are uses that are not categorized by respondents in any of these bins, as would be the case,for example, with investment in livestock or business inventories.
To present visual evidence of the distributional impact of the savings product, Figure 4
shows the un-winsorized cumulative density functions of the raw data for three of the main
outcomes in Table 3, namely monthly bank savings, monthly total savings, and household income.
The impacts on bank savings are clear throughout the distribution. For total savings, we see that the
impacts are only visually positive above the median. For household income the impacts are lessstark, and again the treatment effects are positive only above the median.
Panel C of Table 3 allows the treatment effect to vary across time by estimating thehousehold-level analogue of specification (5) above. The save-invest-earn channel implies that
income should increase little if at all initially, with larger increases occurring later after treatment.
The labor reallocation effect should have the opposite pattern, with income rising immediately ashouseholds increase effort today. The data show a pattern more consistent with the laboradjustment story, with very large immediate increases that do not grow over time, and may diminish
by the last survey round. Figure 5 shows that (along with a large shock caused by widespreadflooding), a treatment effect on business income is visible from the very first month of treatment.
While impacts largely attenuate once weekly home visits stop, this pattern of treatment effects acrosstime is the first piece of evidence in favor of labor reallocation as a mechanism linking new savings
opportunities to increases in income.
Given that the savings increases we observe appear to be primarily driven by new income,we turn in Table 4 to examining the individual-level income data in more detail. We perform thisanalysis estimating regressions similar to specification (4) above, replacing the dependent variables
with measures of the sources of individual-level income. We shift our focus to the respondent’s

20

behavior because that is where we have the most detailed income data. In addition, the estimates inTable 3 indicate that the majority of the increase in earned income is due to the respondent.
Panel A of Table 4 shows the disaggregation of income for the full sample, with all income
data winsorized at the 99th percentile. We begin by examining the effect of treatment on
occupational choice. We find no evidence that the savings accounts operate by relaxing credit
constraints, and, thereby, increasing entry into self-employment. On the contrary, we find that selfemployment falls by 3.4 percentage points in the treatment group, relative to the control group.
Engagement in wage work increases by two percentage points, though the effect is not statisticallysignificant (p-value = 0.16). However, earnings from wage work (Column 4) and average hours inwage work (Column 7) both increase with the increase in wage hours being statistically significant.
Note that all measures capture both intensive and extensive effects. Self-employment status, income,and hours are coded as zeros for those not self-employed, and hence the treatment effects are
impacted by the entry into wage work and exit from self-employment reflected in Columns 1 and 3.
Appendix Table A7 uses Randomization Inference to calculate standard errors for Panel A of Table
4 and concurs with the two-way clustering in terms of the levels of significance of impacts on selfemployment and wage hours.
We can also calculate an hourly treatment effect by comparing the increase in hours with theincrease in earnings. Hours worked is reported on a weekly basis, and the income on a monthly
basis. Thus, the increase of 1.5 hours per week in wage work is thus approximately 6.4 hours permonth. This implies a wage at the margin of 49.4 LKR per hour (315 LKR / 6.4 hours), an amountvery similar to the average hourly wage of 50.5 LKR per hour in the control group. This isreassuring with regard to the consistency of the data.
In sum, we find that earned income increases immediately after treatment, and themagnitude of the treatment effect is either steady or decreasing across time. Treatment also leads toa shift out of self-employment and into wage work. These results are not consistent with the saveinvest-earn channel of savings. They are consistent with an increase in labor effort when the deposit
collections are introduced. To explore this channel a bit further, we step outside the experiment, andexamine effects dividing the full sample into three subgroups.25 We first split the sample into those25

The project started before the RCT registry was established. Hence, we have no public randomization plan.
However, the stratification indicates that our initial analysis was built around the informal-formal savings channel.
The data show little evidence for this channel in aggregate, though we return to this issue below. Though webalanced on expenditures, indicating that we saw this as a key outcome, we did not expect to find an immediate21

who are self-employed and those who are not. We do this using the activities reported in the fourbaseline rounds, which took place before treatment status was known to the participants. This initial
split is justified by the fact that the save-invest-earn channel can work through either the intensive or
extensive (e.g., lower exit rates) channel among those self-employed at baseline, but only through theextensive margin among those not self-employed. There are 419 respondents active in selfemployment in at least one baseline round, and 360 not active in self-employment. We then split the
self-employment sample further into those active in manufacturing during baseline, and those active
only in trade and services. Given the very rural nature of our sample, we expect those in trade andservices may have less opportunity to increase demand, while those in manufacturing likely facefewer constraints because they can sell output in nearby towns.26
Panels B, C, and D of Table 4 report the treatment effects on activities of participants in the
self-employed manufacturing, self-employed non-manufacturing, and not-self-employed samples.
Among those active in self-employed manufacturing in baseline (Panel B), we see no shift toward
wage work, but instead a very large increase in reported business earnings. This is accompanied by amodest (and statistically insignificant) increase in hours worked. Together, these imply marginal
earnings of 219 LKR per additional hour, about three times the sample mean of 72 LKR per houramong all self-employed. These data are thus consistent with an increase in both work intensity andwork hours, as should be expected if the effective returns to labor increase.27 Researchers havestruggled to find direct measures of effort in self-employment activities, and we lack good measures,
as well. So, we can only say that the reported increase in earnings is high relative to the reported
increase in hours worked, and we speculate that this may reflect an increase in the intensity of effort.
In contrast, among those who are self-employed in trade and services (Panel C), we see a
sharp exit effect (column 3), accompanied by an increase in wage work (column 1), in wage earnings(column 4) and in the hours worked in wage work (column 7). Again, the incremental earnings inwage work per incremental hour worked – 54.9 LKR – is close to the sample average. Now,
however, the same calculation on self-employment – measured as a decrease in earnings perincrease in income and a shift out of self-employment. The three subsamples we construct are, hence, nonexperimental, and the analysis should be interpreted with this in mind.
26
As it turns out, those active in manufacturing are also much more likely to report income from more than one
activity during the baseline period. Two-thirds of those in manufacturing are also active either in wage labor or
agriculture; this compares to less than 5 percent of those in trade and services. The differences in the subsamples
may be due to these multiple activities or some other characteristic correlated with involvement in manufacturing.
27
See, for example, the estimated intensity effects found by Lazear (2000) when workers switched from hourly
wages to piece rates.

22

decreased hour worked – is also much closer to the sample mean among the self-employed, at 88.2
LKR per hour. Note that this decrease is a LATE of those remaining in self-employment in thecontrol group who would have exited with treatment. Thus, we should not expect to find any effectof effort, since the self-employed over whom this effect is measured are in the control group. While
the trade and services self-employed are induced to make large movements to wage work, these
movements are ultimately ineffective in increasing income: wage earnings rise, but business earnings
fall by an almost identical amount. Finally, we see no effects on either activities or income earned
among those not self-employed at baseline (Panel D).
We now move to a period-by-period analysis of subgroup impacts. Just as Table 3 showed
immediate impacts of the treatment on income, Table 5 demonstrates that an exit from selfemployment and an increase in wage hours take place even in the first few months of treatment.
Panels B and C show the time-varying effects for the two self-employment subsamples. Among theself-employed in manufacturing (Panel B), we see the immediate jump in business earnings, whichfades very slightly over time until the last survey round, when it falls markedly and becomes
statistically insignificant. In Panel C, we find that the exit from self-employment among thoseinitially in trade and services increases throughout the post-treatment period. The treatment effecton reporting self-employment activity is -5.4 percent and significant in the initial post-treatment
period. But this grows so that by the final two survey rounds, fully one in six of those in thetreatment group who were initially self-employed has exited self-employment. Both reporting any
wage earnings (Column 1) and the level of wage earnings (Column 4) increase steadily across time,
but business earnings decrease by a comparable amount in the first 13 months, and by substantiallymore than the wage increase in the last two surveys.
It is reasonable to ask whether the differences in the earnings response across these threesubsamples are mirrored in differences in savings behavior. We examine this question in Table 6,
where we return to the sources-and-uses analysis, this time by subsample. Panel A repeats the results
for the full sample (with outcomes winsorized) in Table 3, again using data from survey round 2(September 2010) to survey round 18 (January 2012). Panels B, C, and D then show the selfemployed manufacturing, self-employed trade and services, and not-self-employed subsamples. We
see that there is a significant increase in savings (column 8) and loan repayments (column 10) only
among the self-employed in manufacturing, where individuals were successful in increasing earnings.
In this subsample, there is a small and insignificant change in consumption (column 7). Among theself-employed in trade and services, the only category showing a significant treatment effect is23

transfers outside the household; this category shows a decrease that, while significant at the .10 level,is relatively small in magnitude. Among those not self-employed, there is a marginally significant
increase in other household inflows (column 6) and non-trivial, though highly insignificant, increases
in savings and consumption. Thus, we find a significant increase in savings only where there is asignificant increase in income, that is, among those who were self-employed in manufacturing atbaseline. We see strong labor market effects among those self-employed in non-manufacturing
activities, but these shifts generate neither increases in income nor increases in savings.
Survey-based data on financial behavior are always reported with some noise.28 To assess therobustness of our results, we repeat all of the core results without winsorizing, with winsorizing at
the 95th percentile of the distribution, and using inverse hyperbolic sine transformations. These areshown in Appendix Tables B1-B10.
5. WHY DO DEPOSIT COLLECTIONS INCREASE SAVINGS AND LABOR EFFORT?
This section discusses and tests empirically, to the extent our data allow, several mechanismsthat might link deposit collections to increased labor effort. Empirically, in response to deposit
collection, weekly labor hours in wage work and self-employment increase by 1.29 hours or 4.2
percent of the control-group mean of 30.84 hours (Table 4, Panel A, columns 7 and 8). In the nonmanufacturing self-employed subsample, wage work and self-employment hours worked weekly
increase by 1.33 hours, a 2.5 percent increase over the control group mean of 53.25 hours.
Are the increases we observe in labor hours reasonable given the interest paid on theaccount? One approach to answering this question is to recall that, in the simple model presented in!

Section 3 above, the elasticity of the labor ratio ! ! with respect gross interest rate 1 + !!!! is just
!!!

!
!!!

. Using a 5 percentage point increase in the real gross interest rate – that is, assuming that thepre-intervention nominal interest rate was zero – and the sample-average increase in labor hours of
4.2 percent in the full sample, we find a value of γ equal to about 2.16. Using the 2.5 percent
increase in the manufacturing subsample yields a γ of 2.95. Both of these are close to the quadratic
disutility commonly assumed (often for convenience) in standard models and within the range of28

For example, we have one respondent who indicates receiving 1.65m LKR as his monthly household income. At 16
times the 99th percentile, this very likely reflects measurement error, and is extreme enough that, even after taking theinverse hyperbolic sine transformation of this variable, it remains an outlier. Rather than selectively removing
observations like this one, which very plausibly reflect recording error, we prefer winsorization.

24

estimates for γ found in the literature (Beaudry and Van Wincoop, 1996, find an IES of 1, equivalentto γ = 2, and Augenblick, Niederle, and Sprenger, 2015, estimate γ = 1.6 in an experiment over real
effort tasks) suggesting that the increase in labor hours is reasonable given a 5 percentage point
increase in real interest rates.
We can also address the importance of the income channel using a direct survey question we
asked in the final monthly wave. In that survey, we asked participants in the treatment group several
questions about how the savings treatment had affected their behavior. Their responses are generally
consistent with the outcomes and channels we identify in the data. Of those opening accounts, 78
percent reported that the intervention helped them to increase savings, and only 5 percent said theyfelt pressured to save by the door-to-door collection. Among those who said they had saved more,
38 percent said this was achieved primarily through increased income, 34 percent said this wasachieved through decreased consumption, and 22 percent said this was achieved through changes inintra-household transfers. By far the most common source of increased income was said to be“more effort to increase sales” in self-employment or agriculture. This was reported by 50 percent of
those saying that income had increased, with 13 percent reporting doing more work at a previously
engaged wage-paying job, 5 percent reporting doing new wage work, and 18 percent reporting
increased income from re-investing in self-employment or agriculture. Although we find someevidence of increased investment in enterprises in the final survey rounds, these self-reported
narratives reinforce the idea that our intervention increased savings by raising incomes, principally
through more labor effort.
While both the calibration and the survey evidence suggest that our results are broadly
sensible relative to the neoclassical literature on intertemporal labor substitution, it is of course
possible that labor effort and income increase for other reasons, or that other mechanisms amplify
the effect of interest rates. We explore some of the other channels in this section.
In addition to the 5 percent interest rate, the deposit collection process has several featuresthat could induce an increase in savings. First, in-person visits by bank staff might remind
participants to save or exert peer pressure on participants. A growing literature suggests that people
may fail to save because doing so is not salient (Taubinsky 2014; Karlan, McConnell, Mullainathan,Zinman, 2016); and, correspondingly, they might be induced to do save by reminders. In-person
visits may also generate peer pressure (Kast, Meier, and Pomeranz, 2012; Chandrasekhar and Breza,2015). Second, the collection service has a commitment feature: we reduce the cost of making
deposits, but not withdrawals. This feature constrains the ability of individuals to use their funds in25

the future since they must travel to make a withdrawal.29 If participants are present-biased andsophisticated, they could use the account to constrain future behavior. Finally, the product may
reduce loss of savings either from theft or from others in the household demanding transfers. Thisis because once a deposit is made it is difficult to withdraw. Capture by others or loss through theft
would imply that the effective pre-intervention interest rates (e.g., saving in cash) may have been
negative, in turn implying that the increase in real interest rates was more than 5 percent.
Exploring these additional explanations can shed light on how expanding savings
opportunities might increase labor effort and income. In addition, identifying the operative featuresof the treatment is useful for policy design.
Several elements of our design allow us to adjudicate between these potential explanations.
First, after six months, we introduced lockboxes in a subset of our control zones. This intervention
still reduces travel costs and protects against potential self-control and other-control impediments tosaving. At the same time, by contrast, it has much more limited elements of peer pressure andprovides much less of a reminder. Second, we elicit structural estimates of time preference using ahypothetical time-dated monetary payment protocol. This permits an examination of whether
individuals who are more present-biased in a task designed to measure preferences exhibit larger
savings, income, and labor responses to treatment.30 We also have geolocations for the center of
each of the 156 zones in our sample, allowing us to measure the travel distance and travel time alongroads from the zone to the bank (see Figure 1). Our sample was selected deliberately to lie between
5 kilometers and 15 kilometers from the bank. Conceivably, deposit collection reduces travel costs
more substantially for participants who live farther from the bank. We therefore check forheterogeneous effects by travel distance.

Finally, we examine the role of other-control using

responses from baseline survey questions indicating whether the respondent had control over formal
and informal savings decisions.
29

A substantial literature in developing countries studies products that provide commitment against withdrawal(Ashraf, Karlan, and Yin 2006; Brune et al., 2016; Kast, Meier, Pomeranz, 2012; Dupas and Robinson 2013b; Bryan
et al., 2010; and Blumenstock, Callen, and Ghani, Forthcoming). Indeed, one recent large experiment finds little
effect of savings accounts without commitment features (Dupas et al. ,2016), and another with Malawian farmers
suggests the potential benefits of commitment may outweigh the cost of reduced flexibility (Gine, Goldberg,
Silverman, and Yang, 2016).
30
The elicitation of preferences using time-dated monetary payments is more likely to accurately reveal present bias
when conducted with credit-constrained individuals because the intertemporal fungibility of money may pose less ofa confound (Cubitt and Read, 2017); Chabris, Laibson, and Schuldt, 2008; Andreoni and Sprenger, 2012; Carvalho,
Meier, and Wang, 2014; and Augenblick, Sprenger, and Niederle, 2015). Our sample, during the exercise, wasselected specifically for lack of access to formal finance, and so it is plausible that the exercise in this environment
could reflect present bias.

26

5.1. Limited Attention and Peer Pressure
In July of 2011, six months after deposit collections began in the treated sample, we
introduced a lockbox treatment in 26 of our 78 control zones. As we discussed in Section 2.21 above,
this treatment was integrated with the mobile POS technology. Deposit collectors visited the box
periodically, added all deposits to user accounts, and left behind deposit receipts. Centralizingcollection greatly decreased costs to the bank. We consulted households in the 26 zones todetermine a secure location within their cluster of houses for the lockbox to be installed. Deposits inthe boxes were collected by a bank agent weekly in 13 of the zones, and biweekly in the other 13
zones. Participants collected receipts for the deposits from envelopes in a compartment on theoutside of the box. This introduction of a less personal collection service allows some scope to test
for the importance of reminders and peer pressure. Importantly, the introduction of savings
treatment to a new group of participants also provides a replication of the initial experiment in adifferent sample at a different time. We examine the effects of this intervention comparing the 13
zones given weekly box collection to the control, running regressions of the form:(6)!!"# = ! ∙ !"#$%"&!" + !! + !! + !!"# .

!!"# are the individual savings, income, or labor-related outcomes. The treatment effect is measured
relative to respondents in the 52 control clusters that remained as undisturbed controls following thestart of the lockbox experiment. Table 7 reports the corresponding estimates. Panel A reports
effects on savings outcomes while Panel B reports effects on labor-related outcomes. In columns 13 of Panel A, we see that this treatment increased both the number and value of deposits, though byonly about one-third as much as the deposit collection response reported in Table 2. In Columns 47, we see no clear impact on total savings, except perhaps that deposits crowded out informal
savings. Therefore, the lockbox appears to have a less substantial effect on financial behavior, andwe find no clear evidence that the increase in NSB institutional deposits leads to an increase in
overall savings. (Indeed, it appears to lead to some reduction in informal savings.)
However, the deposit collection boxes do appear to create a labor market response that isvery similar to what we see in the initial treatment group. These results are reported in Panel B.
Wage employment increases (column 1), self-employment decreases (column 3), wage income rises(column 4), and business income falls (column 5). Correspondingly, wage hours increase (column 6),27and hours in self-employment decrease (column 7). These responses are similar to those seen in
Panel C of Tables 4 and 6 (the non-manufacturing self-employed): a shift of labor toward wage
work that is fully counterbalanced by a decline in business income. We interpret these results asshowing that the lockbox savings products lead participants to make attempts to increase income,but these efforts are ultimately not successful, and, hence, lead to no additional income to channel
into savings. Given sample sizes, we can only speculate why the lockbox treatment does not lead toan increase in income even among the self-employed in manufacturing. Perhaps these results suggest
a link between salience provided by door-to-door collection and the production of overall income.
Households may need the pressure of the weekly home visits to be successful in translating an
increase in labor effort into an increase in total income. Overall, however, the effect of the lockbox
treatment broadly confirms the link between improved savings options and labor decisions.
5.2. Self-Control
Much of the recent interest in the theory underlying the use of savings products is due tobehavioral economics’ focus on the difficulty that people have putting aside money from daily cash
flows to meet savings goals. The literature provides several distinct reasons that individuals may failto save, and many of these explanations suggest that a high-frequency deposit collection service canalter behavior in important ways. Individuals with self-control problems will achieve a higher savings
trajectory if the long-term self can lock the short-term self into a commitment (Laibson 1997).
Frequent deposit collecting allows people to get loose cash away from themselves, and may permit
them to control their own consumption of “temptation goods” (Banerjee and Mullainathan 2010).
Our savings product provides an interesting window on these behavioral dimensions: it features
convenient deposit and inconvenient withdrawal, and therefore has a commitment dimension.
The fact that we find no evidence that treatment decreases expenditures suggests thatstandard arguments about controlling consumption cannot be playing a driving role in the overall
effects of the program. The commitment feature of the product might allow present-biased
individuals to select new consumption streams more aligned with long-run preferences. Throughthis channel, we would expect to see that income increases more, relative to controls while there
would be ambiguous effects on aggregate consumption, with savings balances building up faster forthe time inconsistent.
To test this, we measured present bias using a standard hypothetical multiple price list; ourbaseline survey asked the respondent “Suppose someone was going to pay you Rs. 1500 1 month28

from now. He/she offers to pay you a lower amount today. What amount today would make you
just as happy as receiving Rs. 1500 in 1 month?” The answer to this question gives the total current
discount factor, or the product of ! and ! if intertemporal preferences take the quasi-hyperbolic
form ! = !! ! !! + !

!
!
!!! ! !(!! ) . We then ask the same question with the time scale moved

out by one year (12 months from now versus 13 months), and the ! parameter can be calculated by
the ratio of the former to the latter answer.
In addition, because of the potential for deposit collection to control the consumption of“sin” or “temptation” goods, we conducted a survey experiment to induce truthful revelation of
goods whose use may be stigmatized. The survey experiment asked respondents to pick (and notreveal to the enumerator), prior to each question about consumption of different sin goods, a card
numbered from 1 to 10. If the number was between 4 and 10 the respondent was to answer “blue”
if they consumed that sin good in the past month, and “red” if not, but if the number was between 1
and 3 they were to answer “blue”’ regardless of the correct response. In this way enumerators cannever infer the consumption status of a specific individual, but the sample prevalence of sin good
consumption can be readily calculated. The same property of aggregation holds across sin goods for
an individual; consequently the panel dependent variable used in the analysis is!! !"#$!
! !.!(!!!.!) , where!! !"#$! is an indicator for a response of “blue” for each of the J sin goods in the survey
experiment. We asked about purchase of alcohol, purchase of tobacco, and about gambling on
horse races and on cards. These questions were asked in pre-treatment wave 3 and in posttreatment waves 10 and 18, and are included in Appendix B.
Table 8 examines the heterogeneity of treatment effects by the extent of present bias. We
estimate these effects using regressions of the form:(7)!!"# = !! ∙ !"#$%#&!" + !! ∙ !"#$%#&!" ∙ !""#$%&'#_!"! + !! + !! + !!"# .

!""#$%&'#_!"! is our experimental measure of subjects’ present bias corresponding to ! in thequasi-hyperbolic utility function and the remaining variables are defined identically to specification(4) above. To improve the precision of the estimates, we winsorize !""#$%&'#_!" at the 10th and90th percentiles. Given the values on the price list used to measure preferences, subjects at the 10th
percentile have a !""#$%&'#_!" of 0.862 and subjects at the 90th percentile have a29

!""#$%&'#_!" of 1.071.31 We have demeaned !""#$%&'#_!"! so that our estimate of !! reflects
the treatment effect at the mean !""#$%&'#_!"! (which is !""#$%&'#_!"! = 0.98 in both thewinsorized and un-winsorized samples).

From this average effect, !! then provides theheterogeneity in impacts corresponding to a decrease in present bias (lower values of!""#$%&'#_!" imply more present bias).
The point estimates suggest that the positive effect of deposit collection on income (column1), wage employment (column 2), business income (column 4), bank savings (column 8), non-banksavings (column 9) and total savings (column 10) are larger for present-biased individuals. For all
three of the savings effects, the heterogeneity is significant at the 95% level implying that those with
self-control problems find the home visits more useful in effectively increasing savings. To provide
a sense of the difference, the estimated effect of deposit collection on total savings is 936 LKR at
the mean of !""#$%&'#_!"! while it is 1422.04 LKR at the 10th percentile of the winsorized
distribution (!""#$%&'#_!" = 0.923). Likewise, the estimated effect on total income is 3235.2
LKR at mean !""#$%&'#_!"! and 3,692.41 LKR at !""#$%&'#_!" = 0.923, though in this casethe interaction is imprecisely measured. We present Fan regressions in Figure 6 that illustrate thissame heterogeneity, showing that significant effects of the treatment on wage hours and overallsavings are restricted to individuals who have measured immediate discount factor of less than about.925. The estimated effects on both our direct survey measure of `sin good’ consumption, as wellas the measure obtained using a randomized response technique, are small and imprecise.
These results suggest that the commitment features of deposit collection play some role inincreasing savings by offsetting a reduction in savings due to present bias. Combining this with theintuition from standard models of intertemporal labor allocation ̶ that increases in the value of
one’s labor provide an additional inducement to work in the current period ̶ suggest that thecommitment features of both the deposit collection and deposit boxes are a reason subjects areworking harder. However, as Figure 6 shows, the data are consistent with an increase in savings forevery level of beta. We additionally check for heterogeneity in treatment effects by distance to thebank along the most direct road (Appendix Table A9), by numeracy (Appendix Table A10), years ofeducation (Appendix Table A11), household size (Appendix Table A12), the number of household
members of working age (Appendix Table A13), and the share of members of working age
31

It is plausible that these respondents may have misunderstood the experimental task. Unwinsorized results are
qualitatively similar, though less precisely estimated (results available on request).

30

(Appendix Table A14). There is limited apparent heterogeneity in deposit-collection impact along
these dimensions (though the estimates are in cases imprecise) in linking deposit collection toincreases in savings and in labor effort. Taken together with the results from the prior section, thesetables suggest that behavioral explanations do play some role in moderating the effect of an interest
rate shock on labor, income, and savings.
5.3. Other-Control
When members of a household disagree on the optimal savings trajectory, privatecommercial savings may allow the pro-savings individual in the household to control the householdsavings rate (Ashraf et al., 2006; Schaner, 2017). We examine the extent to which interpersonal
conflict drives savings by testing for impact heterogeneity over the degree of financial control
respondents had at baseline. In the second of our five baseline rounds, we asked the question, “Do
you have control over the use of money needed . . . for savings (such as in financial institutions, e.g.,banks) for yourself/your children?” We code a dummy for “savings no control” equal to one if the
respondent reports no control over either formal or informal savings vehicles.32 This direct survey
question provides a straightforward way of examining whether treatment had a stronger impact on
individuals who lacked control over savings decisions at the time the intervention began.
The interaction analysis presented in Table 9 indicates that the impact of the treatment was
not concentrated among those who lacked financial control. These regressions include individual
and round fixed effects, the panel dummy for treatment, and the interaction between treatment andan indicator for “had no savings control at baseline.” Importantly, it does not appear that the effectof deposit collection on bank savings (column 8), non-bank savings (column 9) or total savings(column 10) is localized to this group. Correspondingly, there is no clear differential impact for thisgroup for wage hours (column 2), self-employment (column 3), or business income (column 4).
Effects on total income (column 1) and consumption (column 5) do appear to be larger for thisgroup, though the interaction terms are not statistically significant. Curiously, there is some evidence
that deposit collection increased consumption of sin goods in this group (columns 6 and 7).
Collectively, this does not suggest a major role for other control. We emphasize that this context is
atypical for a developing country in that financial control is not highly gendered. In our sample, 63%32

This approach is intended to identify respondents with low degrees of spousal control. 456 of the 788 respondents
in our sample (58%) report having no control.. Results are similar if the analysis is conducted using only control overformal savings.

31

of men, and 54% of women, indicate having no control of either formal or informal savings
decisions.
An alternate approach to this problem is presented in Appendix Table A15, which draws on
an idea from Anderson & Baland (2002) in which the share of household income earned by the
respondent is taken as a measure of control over finances. Following their methodology, we analyze
heterogeneity by terciles of the share of income earned by the respondent and find results opposite
to those found in their paper: total savings impacts are slightly larger for the top and bottom terciles
than the middle tercile. While earnings impacts are larger for those with less income to begin with,there is no evidence of significant differential impacts on consumption, transfers, or savings byincome tercile. Thus, taking this approach, we again conclude that the impact of our mobile deposit
collection does not arise as a result of improved ability to control the behavior of other household
members.
5.4. The Impact of Formal Accounts on Informal Savings Institutions
At the time of designing the study we were concerned with the possibility that formal
savings accounts, by creating a private and concealable way of storing wealth, might undermine thesocial insurance provided by informal savings institutions such as ROSCAs (Besley et al., 1993).
Such institutions are fragile in that they rely on social coercion to enforce contributions (Anderson
et al., 2009). By opening up new exit options, particularly for those with substantial savings liquidity,
private accounts could spell trouble for the effectiveness of both informal saving and risk-poolingmechanisms. To address, this, we randomized the intensity of the weekly home treatment among
other members (besides the survey respondent) for a set of seetus as described in Section 2.2.2. As an
increasing share of these other members have access to private personal savings accounts, they may
become more likely to renege on ROSCA contributions, and less likely to exert effort monitoring
the behavior of group members. Thus, if formal savings are a substitute for informal savings
groups, we expect to see the attractiveness of ROSCA savings fall as an increasing share of the
ROSCA members renege on their savings commitments and on their attempts to control the
behavior of fellow group members. At the extreme this could lead to group collapse, and on theintensive margin it could lead to a decline in the number of ROSCAs an individual chooses toparticipate in and the quantity of savings achieved through ROSCAs.
To understand the impact of seetu saturations on informal insurance, we use the monthly
flows of transfers into the household and out of the household (we screened out cases in which a32second household member was in the same seetu as the respondent, and so the interpersonal flows of
informal insurance should be primarily inter-household). We also examine the effect of the seetu
saturation experiment on overall savings. The sample for this analysis consists of the sampled 20
percent of the membership of each of the 84 close seetus drawn into the survey at baseline, and theexperimental variation arises from whether an additional random 0 percent, 20 percent, or 40
percent of their ROSCA was offered the POS weekly home savings product.
We use two empirical specifications for each outcome. The first examines the overall
intention-to-treat effect within the close seetu membership. The second includes a dummy fortreatment and further includes the randomly chosen saturation within treatment seetus. In thisspecification the dummy for treatment gives the impact in the 20 percent treatment saturation seetus,
and the slope term on the saturation gives the marginal effect on outcomes of treating (but notstudying) an additional fraction of the membership beyond this. Because we have no individuals
who are studied but not treated in treatment seetus, we are only able to estimate the Spillover on theTreated, and not the Spillover on the Not Treated (Baird et al., 2017). The effects of the saturation
should therefore be interpreted as the impact of increasing the fraction of the seetu given the deposit
collection treatment, conditional upon the fact that the studied individual is treated.
Appendix Table A16 shows the balance of the seetu saturation experiment.

Thisrandomization was conducted in a very small number of units; the saturation experiment isparticularly subject to potential imbalance as each saturation cell contains only 13 seetus. We showbalance over 15 tests, and find only one of them to be significant at the 10 percent level.
Nonetheless there are some quantitatively large differences, particularly across the saturation
amounts within the treatment.

Overall savings is imbalanced across the distribution of thesaturation. We therefore proceed to the analysis of the saturation experiment with some caution as
the number of assignment units is small, and the balance not perfect.
The results of this analysis are given in Table 10. Contrary to the hypothesis that private
individualized savings poses a threat to seetu participation, the treatment and the treatment saturation
appear to lead to superior outcomes for the seetus. Treatment on average increases the number of
seetus in which a respondent participates by 0.27 over a base of 1.8, an increase of more than 10
percent. Allowing for heterogeneity across the saturation rate indicates that where more individuals
are treated, membership in seetus increases more rapidly. The coefficient of 1.42, significant at the 1
percent level, indicates that each 20 percent increase in the fraction of the seetu treated increases thenumber of seetus participated in by its members by a further 0.3. The monthly amount saved
33through seetus is higher in treatment than in control zones, and the saturation effect is again positiveand large in absolute magnitude, although not significant. The total amount saved through the seetu
is 238 LKR per month higher in treatment than control seetus, and the saturation of treatment in theinformal savings groups is also positive (though insignificantly) correlated with total savings. Hence,
the result of the randomized saturation experiment indicates that, far from posing a threat to seetus,
the bank-driven deposit collecting appears to be fortifying informal savings groups.
6. CONCLUSION.
We conducted an experiment with a powerful inducement to save: weekly visits by a deposit
collector equipped with a wireless POS device capable of printing out account balance receipts on
the spot. The experiment was implemented in Sri Lanka, a country with strong informal savings
institutions and a tradition of using formal banks for “children’s accounts” into which parents often
begin to put savings at the birth of a child. Despite this, we find strong effects of the treatment notjust on savings into program accounts, but into bank savings and overall savings as a whole. The
data therefore suggest that, even though the sample had access to a wide range of formal andinformal savings mechanisms, the simple low-transactions-cost account represented a significantly
better option. We tracked the sample with monthly surveys including five pre-treatment waves, anda careful cash-flow accounting instrument designed to answer two questions: First, what are theheadwaters of formal savings? Second, what are the channels through which formal savings affects
income and expenditures?
Our results confirm recent experimental findings that access to formal savings products can
produce surprisingly large benefits for unbanked households, even when these accounts bear low
real interest rates. Our detailed high-frequency surveys help to shed light on the mechanisms behindthese savings increases. We find a large and immediate increase in income following treatment,
allowing savings to increase without any accompanying decrease in consumption. The surveys
reveal that this newfound income is not generated by increased investment in entrepreneurial
activities; indeed, the savings product triggers an exit from self-employment.

In aggregate,households work more hours in wage work. An increase in earned income explains a substantial
majority of the increase in income.
The novelty of our results, then, is that we show substantial increases in savings and income
without any foregone consumption, and without the save-invest-earn channel that is suggested by
the literature on non-convexities in production. Earnings increase as soon as participants gain access34

to the deposit collection service, and they increase in the face of exit from self-employment. These
overall sample impacts are made up of a number of distinct sub-group effects. When self-employedhouseholds with manufacturing businesses were offered weekly home deposits, they successfully
expanded earnings by working harder in their own business; the higher income resulted in higher
total savings. Among those with non-manufacturing businesses, households exited self-employment
and increased labor in the wage market. The treatment effect on labor allocation is large in thisgroup – one in six individuals have exited self-employment by the end of the study – but ultimately
ineffective. The increase in wages is counterbalanced by a fall in business income; neither total
income nor total savings improves. The impact of the weekly home box treatment largely mirrors
this result. The effort to raise income by working harder in the wage market is unsuccessful.
Thus, only the subgroup successful in raising aggregate income was ultimately able toincrease total savings: we find no headwaters for savings other than income. The implication is thatnew institutional savings options will be most effective in raising total savings when they are offered
to households with potential to increase income, for example, by profitably expanding effort in selfemployment. A high-salience inducement to save regularly may be important to induce participants
to exert the continuous effort required to increase income through labor effort. We note that while
we believe our subsample analysis illuminates the mechanisms, our main conclusions derive fromthe full sample analysis on which the experiment is based.
The centrality of income generation underlines the challenge in detecting impacts when they
move through an outcome as difficult to detect as labor inputs. For example, Dupas and Robinson(2013) find a positive treatment effect of their savings product of between .15 and .31 hours worked
per day in their samples. The effect we find is of similar magnitude – 1.29 hours per week, or ~.25
hours per day – but this effect is more precisely measured and is statistically significant. A substantial
reason our study has the ability to detect this channel is the long, high-frequency panel we collected,
providing us statistical power for highly stochastic outcomes (McKenzie 2012).
In one sense it is surprising that a financial service offering nothing more than a low-costmeans to save in a bank could increase household income. However, as in classical macroeconomic
models of intertemporal labor allocation, the responses we observe in the data are consistent withthose we would expect from individuals who experience a large increase in the interest they receiveon savings. These effects appear to be larger for present-biased individuals, suggesting that thecommitment dimension of the product may reinforce the interest rate effect. These features of the
product drive up the benefit of working today to save for tomorrow, leading individuals to increase35

labor effort in the initial period to build up savings. We read the full-sample results, supported by
the subsample analysis, as suggesting that the labor channel, rather than the investment channel,
deserves some attention when studying the benefits of saving.
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Samphantharak and Townsend (2009). Households as Corporate Firms, Cambridge: Cambridge
University
Press.
Schaner, S. (2016) “The Cost of Convenience? Transaction Costs, Bargaining Power, and Savings
Account Use in Kenya”, Journal of Human Resources, forthcoming.
Schaner, S. (2017). The Persistent Power of Behavioral Change: Long-Run Impacts of Temporary
Savings Subsidies for the Poor. Working paper
Small, Dylan, T. Ten Have, and P. Rosenbaum. (2008). “Randomization Inference in a GroupRandomized Trial of Treatments for Deptression: Covariate Adjustment, Noncompliance,
and Quantile Effects.” Journal of the American Statistical Association, 103(481).
Taubinsky, Dmitry (2014). From Intentions to Actions: A Model of Experimental Evidence of
Inattentive Choice. Working Paper.
Thaler, Richard, and Shlomo Benartzi. 2004. “Save More Tomorrow (TM): Using Behavioral
Economics to Increase Employee Saving.” Journal of Political Economy 112(S1): S164-S187.

39

TABLES.
Table 1: Randomization Verification

Baseline Outcome:Number of transactions with a formal financial institution during previous month
FemaleDiscount Factor (delta)
Time Consistency Factor (beta)
Total number of seetus in which respondent participated in previous month
Total payouts from seetus in previous month
Number of transactions with a financial institution other than NSB over previous month
Total amount saved through ROSCAs over previous month
Total amount withdrawn from ROSCAs over previous month
Total amount put into informal savings over previous month
Total amount withdrawn from informal savings over previous month
Total change in household cash balance over previous month
Total amount received in loans over previous month
Aggregate income over previous month
Aggregate consumption over previous month
Earned household income over previous month
Total household income over previous month
Personal income taken from informal savings over previous month
Transfer from spouse over previous month
Transfer from outside the household over previous month
Total personal income over previous month
Transfers to spouse over previous month
Transfers to children over previous month
Transfers to anyone over previous month
Monthly savings into banks
Monthly savings in cash
Monthly savings through ROSCAs
Monthly savings through other means
Total Monthly savings over previous month
Respondent reports being self-employed in non-ag enterprise during previous month
Wage hours worked
SE hours worked
Total asset purchases over previous month
Total value of business inventory
Total business expenses over previous month
Total business sales over previous month
Total business income over previous month

Number of Baseline
Surveys

Pre-Treatment Mean

Control
(1)
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
1,445
733
733
733
733
733

Control
(3)
0.41
0.52
0.92
0.97
1.23
948
0.41
1,470
1,126
2,765
1,940
585
2,916
22,792
18,672
22,19529,754
13,2293,713
3,589
21,0981,945
260.66
3,093
780
2,413
1,481
416.96
5,587
0.51
5.95
24.26
561
35,491
20,34431,561
10,500Treatment
(2)
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
1,373
723
723
723
723
723

Treatment
(4)
0.40
0.54
0.93
0.99
1.16
817
0.39
1,367
1,011
2,480
1,738
-125
2,803
22,144
17,907
21,117
28,111
11,767
4,043
3,437
19,8192,113
253.92
3,076
635
2,157
1,407
388.43
4,932
0.53
5.65
25.48
490
41,79622,86033,561
10,734Treatmentcontrol
differential

SE of
Difference(5)-0.0130.016
0.00900.020*-0.069-127.4-0.018-104.0-115.1-289.5-206.7-712.7*-110.7-657.7-769.4-1081.7-1630.3-1451.7
323.9-150.0-1267.7
167.4
-8.08
-19.8
-141.8-246.2-75.5-30.6-646.6
0.019
-0.30
1.23
-74.4
6203.82484.92013.0233.7(6)(0.046)(0.038)(0.0095)(0.011)(0.11)(176.0)(0.044)(190.7)(181.1)(316.8)(267.9)(397.1)(396.7)(969.2)(952.8)(1007.1)(1413.6)(991.2)(401.8)(445.7)(1163.2)(242.9)(36.5)(267.6)(137.4)(236.4)(198.9)(60.1)(467.1)(0.043)(0.96)(2.74)(153.7)(8115.8)(3287.9)(4117.1)(1099.2)

Notes: This table reports on the pre-treatment balance of the main outcomes of the study as well as a broad set of covariates. Variables are Winsorized at the 99% level. Data include four monthsof pre-treatment surveys. The treatment-control differential is estimated using a regression including fixed effects for survey wave, and clustering standard errors at the zone level (treatment unit).
The unit of observation is the individual/month. Regressions pool samples surveyed monthly and samples surveyed quarterly.
* significant at 10%; ** significant at 5%; *** significant at 1%

Table 2: Estimated Impacts of Deposit Collections on Savings Outcomes
NSB Institutional Data

Survey Data

# of Program
Transactions

Program
Deposits

Program
Deposits Withdrawals(1)
1.73***(2)
1143.5***(3)424.9***(4)
1.57***(5)
689.6***

(6)
42.2

(7)
883.0**(0.13)(158.9)(95.1)(0.15)(198.6)(322.0)(376.7)

9172
0.68
783

9172
0.28
783

9172
0.090
783

9172
0.58
783

9172
0.25
783

9172
0.32
783

9172
0.33
783

1.74***

1112.3***660.2***

1.52***

660.6***

217.1

964.3**(0.22)(187.1)(178.6)(0.17)(220.1)(345.9)(428.1)Treated: months 5-8

1.74***

1060.8***269.6**

1.65***

616.4***-184.2634.8(0.17)(190.7)(112.3)(0.16)(229.5)(471.6)(489.9)Treated: months 9-13

1.69***

1283.2***279.2*

1.55***

818.5***

35.9

1036.8**(0.23)(230.1)(159.8)(0.29)(271.0)(409.7)(469.5)6 months post-treatment

0.42***

247.8**-527.8***0.32***

436.0

80.5

926.2*(0.052)(125.3)(164.8)(0.11)(295.5)(495.9)(538.5)

12 months post-treatment

0.36***

806.7***-386.3*0.19**

10.9-204.0-220.4(0.034)(194.5)(207.7)(0.099)(222.6)(412.7)(480.3)0.01
10,055
0.53
783

1.68
10,055
0.28
783

0.85
10,055
0.11
783

0.51
10,0550.57
783

756.81
10,0550.24
783

4,307.43
10,0550.30
783

5,213.32
10,0550.31
783

Panel A: Pooled
TreatedObservations
R-squared
Number of HHs

Total # of
Transactions

Bank
Savings

Informaland Cash
Savings

Total Savings

Panel B: By Period
Treated: months 1-4

Control Group Mean
Observations
R-squared
Number of HHs

Notes: This table reports on the effect of treatment on savings outcomes. Panel A reports results pooling across survey rounds 2 - 18. Panel B reports effects
separately for the five indicated sets of survey rounds separately. Each column within a panel reports results of separate regressions using individual- andmonth-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey wave level using the method of Cameron, Gelbach, and Miller(2011) are reported in parentheses. The unit of observation is the individual/month and the reported coefficients correspond to dummy variables equal to one
for individuals offered weekly home visits from National Savings Bank deposit collectors in the months indicated. Columns (1)-(3) use institutional data from
NSB to calculate cumulative monthly totals, including zeros for individuals without bank accounts. Columns (4)-(7) use survey data; (4) gives the cumulative
number of financial transactions with any institution over the course of the month, while (5)-(7) give the total amount saved by the individual survey
respondent over the previous month in each type of savings. Outcomes are Winsorized at the 99% level. Data include four months of pre-treatment data, 13
treated months, and two waves conducted 6 and 12 months after monthly home visits ended; the treatment changed at this point from door-to-door collection
to collection from a lock box placed in the cluster of houses (see section 2.2.1 for details). Panel A includes data through the end of weekly home visits (17waves). Panel B includes the two post-treatment surveys (19 waves). Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant
at 10%; ** significant at 5%; *** significant at 1%.

1

Table 3: Examining the Headwaters of Formal Savings
Panel A: Full Sample, Non-winsorized Data ( N=783)
(1)

(2)

Sources of income
(3)
(4)

(5)

Earned Income

Transfers and loans

HouseholdIncomeEarned byhousehold

Earned byrespondent

Earned byotherhouseholdmembers

Treated months 1-13

2634.9(1842.6)

2372.0*(1270.0)

1646.9*(977.3)725.1(894.2)103.0(396.1)

Observations
R-squared

9,172
0.241

9,172
0.271

9,172
0.302

9,172
0.295

VARIABLES(6)

Transfers fromOther
outsidehouseholdhouseholdinflows (e.g.,(remittance)
loan receipts)(7)

Uses of income(8)(9)

Consumption and savings(10)

Transfers and loans

Householdconsumption

Total savings

Transfers to
outsidehousehold

Loan payments

158.7(1315.7)279.2(1484.7)865.3(650.1)-92.5(129.7)804.7*(425.5)

9,172
0.180

9,172
0.157

9,172
0.167

9,172
0.223

9,172
0.072

9,172
0.142

Panel B: Full Sample, Data Winsorized at the 99th percentile (N=783)
Treated months 1-13

3185.3**(1240.6)

1853.5**(768.3)989.0(637.6)392.3(578.9)68.6(147.4)858.2(914.4)899.6(950.4)883.0**(376.7)

3.31(51.6)

362.5(232.7)

Observations
R-squared

9,172
0.360

9,172
0.425

9,172
0.378

9,172
0.518

9,172
0.243

9,172
0.202

9,172
0.290

9,172
0.325

9172
0.255

9,172
0.198

Panel C: Time-varying effects, Data Winsorized at the 99th Percentile (N=783)
Treated months 1-4
3465.8*2018.8**1436.7*49.3(1810.9)(948.4)(753.1)(611.4)Treated months 5-8
3270.6**
1823.4**
541.9
800.6
(1291.2)(912.3)(868.7)(798.9)Treated months 9-13
2495.11493.8862.6
279.3(1700.3)(1175.1)(821.4)(850.1)
6 months post-treatment
3038.2*1854.91190.0743.4(1657.2)(1413.5)(1273.1)(975.8)12 months post-treatment
82.5-1654.3-659.1-808.6(1661.8)(1139.0)(1392.4)(1151.7)

93.4(159.3)72.2(212.1)11.9(234.7)57.2(253.7)-96.9(230.6)1025.9(1101.2)
930.2(1089.6)553.6(1168.0)
606.4(989.1)1242.4(1102.6)

1005.0(1177.7)802.7(1049.5)
811.3(1182.7)
1583.0(1151.1)
629.8(1043.0)

964.3**(428.1)634.8(489.9)1036.8**(469.5)926.2*(538.5)-220.4(480.3)-16.5(49.8)
11.2(75.4)
22.8(71.0)-131.9*(72.0)-43.1(50.6)

558.1*(308.1)277.8(343.2)188.5(229.3)735.8**(313.3)
86.5(282.1)

Control Group mean
Observations
R-squared

611.1010,0960.221

5,979.01
10,0960.196

16,316.90
10,0550.284

5,213.32
10,0550.312

353.37
10,0550.243

1,559.02
10,0550.191

29,393.04
10,0550.355

22,022.68
10,0550.415

9,879.11
10,0550.365

11,786.89
10,055
0.513

Notes: This table reports on the effect of treatment on financial outcomes. Panel A reports results pooling across survey rounds 2 - 18, with no Winsorizing of the outcome variables. Panel B
reports effects for survey rounds 2-18, with the outcomes Winsorized at the 99th percentile. Panel C uses data Winsorized at 99% and presents estimates separately for the five indicated sets ofsurvey rounds. Each column within a panel reports results of separate regressions using individual- and month-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey
wave level using the method of Cameron, Gelbach, and Miller (2011) are reported in parentheses. The unit of observation is the individual/month and the reported coefficients correspond todummy variables equal to one for individuals offered weekly home visits from National Savings Bank deposit collectors in the months indicated. All columns in the table use survey data, andoutcomes are monthly flows for the variables indicated. Data include four months of pre-treatment data, 13 treated months, and two waves conducted 6 and 12 months after monthly home visits
ended; the treatment changed at this point from door-to-door collection to collection from a lock box placed in the cluster of houses (see section 2.2.1 for details). Panels A and B include data
through the end of weekly home visits (17 waves). Panel C includes the two post-treatment surveys (19 waves). Regressions pool samples surveyed monthly and samples surveyed quarterly.
* significant at 10%; ** significant at 5%; *** significant at 1%.

2

Table 4: Estimated Impacts of Deposit Collection on Earnings Outcomes
Panel A

Full Sample ( N=783)

Dependent Variable:
Treated months 1-13

(1)
Y/N: Wage
Employment?
0.020(0.016)(2)
Y/N: Ag
employment?
-0.0000048(0.014)(3)
Y/N: Selfemployment?
-0.034*(0.017)

Control group mean
Observations
R-squared

0.16
9172
0.86

0.59
9172
0.92

0.53
9172
0.92

(6)
Business
income573.5(469.0)(7)(8)

Wages earned
314.9(212.7)(5)
Ag incomeearned-15.4(503.2)

Wage hours
1.52**(0.71)

SE hours-0.23(1.00)

1,263.899172
0.76

2,566.01
9172
0.21

5,834.98
9172
0.68

6.00
9172
0.83

24.84
9172
0.85

Panel B: Some Self-Employment and Some Manufacturing During Pre-Treatment Period (N=259)
Treated months 1-13
-0.019-0.016-0.0092-204.1-210.6(0.033)(0.026)(0.027)(352.1)(759.4)2808.5***(1075.7)-0.037(1.38)

3.02(1.97)

Control group mean
Observations
R-squared

1,611.973085
0.13

9,561.80
3085
0.56

3.88
3085
0.78

42.10
3085
0.68

Panel C: Some Self-Employment but no Manufacturing During Pre-Treatment Period (N=160)
Treated months 1-13
0.10***
0.030-0.078**1014.6**293.9(0.032)(0.030)(0.037)(420.8)(192.8)-1141.3(1164.9)

4.40***(1.54)-3.07(2.73)

Control group mean
Observations
R-squared-56.391821
0.11

12,535.26
1821
0.61

1.38
1821
0.71

51.87
1821
0.63

Panel D: No Self-employment and no Manufacturing During Pre-Treatment Period (N=364)
Treated months 1-13
0.012
-0.0077-0.026339.7-257.0(0.020)(0.021)(0.022)(241.4)(762.2)-228.2(342.6)1.30(0.80)-0.77(0.79)

Control group mean
Observations
R-squared

535.13
4266
0.53

9.30
4266
0.87

1.74
4266
0.49

0.09
3085
0.80

0.04
1821
0.74

0.25
4266
0.89

0.67
3085
0.89

0.02
1821
0.63

0.72
4266
0.90

0.94
3085
0.65

(4)

796.01
3085
0.62

0.99
1821
0.51

258.47
1821
0.66

0.05
4266
0.59

1,988.71
4266
0.81

4,251.10
4266
0.24

Notes: This table reports on the effect of treatment on employment outcomes; columns 4-9 are Winsorized at the 99th percentile. All regressions use data acrosssurvey rounds 2 - 18. Panel A uses the full sample of respondents in the study, Panel B uses all respondents who ever reported being self-employed in a
manufacturing business in the five baseline rounds, Panel C uses all respondents who ever reported being self-employed in the five baseline rounds but not in a
manufacturing business, and Panel D uses all respondents who never reported being self-employed in the five baseline rounds. Each column within a panel
reports results of separate regressions using individual- and month-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey wave level
using the method of Cameron, Gelbach, and Miller (2011) are reported in parentheses. The unit of observation is the individual/month and the reported
coefficients correspond to dummy variables equal to one for individuals offered weekly home visits from National Savings Bank deposit collectors in the months
indicated. All regressions use survey data; colums (1) - (3) report whether an individual reported being employed in the described activities at any point during amonth, and Columns (4) - (8) report monthly totals. Data include four months of pre-treatment data and 13 treated months, through the end of weekly home
visits (17 waves). Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; *** significant at 1%.

3

Table 5: Estimated Impacts of Deposit Collection on Earnings Outcomes by Time Period
Panel A

Full Sample ( N=783)

VARIABLES
Treated months 1-4
Treated months 5-8
Treated months 9-13
6 months post-treatment
12 months post-treatment
Control group mean
Observations
R-squared(1)
Y/N: Wage
Employment?
0.013(0.013)0.024(0.019)0.027(0.025)0.031(0.027)0.055*(0.028)(2)
Y/N: Ag
employment?
-0.011(0.012)0.013(0.018)-0.0016(0.021)-0.012(0.023)-0.0081(0.024)(3)
Y/N: Selfemployment?
-0.034**(0.014)-0.028(0.020)-0.040(0.026)-0.045(0.032)-0.028(0.033)0.16
10,0550.852

0.59
10,0550.909

0.53
10,055
0.914

(4)

(6)
Business
income825.7*(457.9)578.8(524.7)210.3(630.7)-473.4(761.1)-1692.9***(627.8)(7)(8)

Wages earned
19.9(194.0)446.1*(246.8)583.8*(300.6)884.0**(381.5)1165.9**(506.8)(5)
Ag incomeearned449.9(660.3)-528.6(573.2)-101.5(582.5)465.7(925.8)-283.3(1272.7)

Wage hours
1.14**(0.54)
1.44*(0.85)
2.21**(1.10)
1.72(1.11)
2.95**(1.38)

SE hours-0.13(0.91)-0.058(1.08)-0.63(1.65)-4.05**(1.90)-1.17(1.78)

1,263.89
10,0550.743

2,566.01
10,0550.203

5,834.98
10,0550.667

6.00
10,0550.817

24.84
10,0550.839

Ag incomeearnedBusiness
incomePanel B: Some self-employment and some manufacturing during baseline (N=259)
Y/N: Wage
Y/N: Ag
Y/N: SelfVARIABLES
Employment? employment?
employment? Wages earned
Treated months 1-4
Treated months 5-8
Treated months 9-13
6 months post-treatment
12 months post-treatment
Control group mean
Observations
R-squared

Wage hours

SE hours

0.0096(0.030)-0.035(0.037)-0.041(0.038)-0.047(0.044)-0.050(0.043)-0.042*(0.024)0.0053(0.026)-0.0087(0.037)0.0066(0.044)0.019(0.045)-0.034(0.022)0.010(0.028)-0.00052(0.039)-0.050(0.048)-0.012(0.049)-298.6(371.5)-185.7(390.5)-79.9(449.1)309.8(663.1)
56.3(664.9)-241.4(1096.8)-266.7(732.7)-154.8(1339.0)-1368.8(1735.4)
1291.0(3207.2)

3106.1***(902.0)2348.4**(1029.4)
2867.6*(1679.3)
2747.3**(1252.5)-1572.3(1194.6)

0.69(1.35)-1.03(1.51)
0.15(1.73)-0.71(2.07)-1.21(1.99)

1.41(1.96)
4.37**(1.76)
3.46(2.95)-1.01(2.68)
0.49(2.52)

0.09
3,388
0.790

0.67
3,388
0.881

0.94
3,388
0.634

796.013,388
0.587

1,611.97
3,388
0.130

9,561.80
3,388
0.542

3.88
3,388
0.755

42.10
3,388
0.664

Ag incomeearnedBusiness
incomePanel C: Some self-employment but no manufacturing during baseline (N=160)
Y/N: Wage
Y/N: Ag
Y/N: SelfVARIABLES
Employment? employment?
employment? Wages earned
Treated months 1-4
Treated months 5-8
Treated months 9-13
6 months post-treatment
12 months post-treatment
Control group mean
Observations
R-squared

Wage hours

SE hours

0.063**(0.025)0.12***(0.032)0.14***(0.042)0.15***(0.044)0.17***(0.047)0.015(0.020)0.045(0.037)0.032(0.042)-0.016(0.031)-0.042(0.034)-0.054*(0.029)-0.079**(0.038)-0.11*(0.060)-0.16**(0.065)-0.16**(0.067)596.7*(327.7)1274.1***(483.6)1382.3**(570.4)1785.6***(623.1)2903.1***(834.6)495.7(398.2)129.7(198.5)
193.3(180.0)-7.78(135.0)720.4(449.9)-660.9(1427.5)-899.8(1289.2)-2130.3(1457.4)-6772.4***(1832.0)-6098.3**(2444.7)

2.66**(1.25)
5.29***(1.55)
6.08***(2.08)
6.11***(2.11)
8.35***(2.31)-0.89(3.13)-3.52(3.15)-5.83(4.12)-17.2***(4.14)-9.75**(4.75)

0.04
1,979
0.756

0.02
1,979
0.637

0.99
1,979
0.529

258.471,979
0.672-56.391,979
0.106

12,535.26
1,979
0.616

1.38
1,979
0.718

51.87
1,979
0.623

Wages earned

Ag incomeearnedBusiness
incomePanel D: No self-employment and no manufacturing during baseline (N=364)
Y/N: Wage
Y/N: Ag
Y/N: SelfVARIABLES
Employment? employment?
employment?
Treated months 1-4
Treated months 5-8
Treated months 9-13
6 months post-treatment
12 months post-treatment
Control group mean
Observations
R-squared

Wage hours

SE hours-0.0089(0.015)0.022(0.024)0.028(0.035)0.038(0.033)0.079**(0.036)-0.0015(0.012)-0.0035(0.030)-0.022(0.030)-0.036(0.035)-0.027(0.032)-0.020(0.019)-0.027(0.027)-0.033(0.036)0.0071(0.039)0.016(0.037)-37.7(235.4)491.8*(297.0)665.7*(390.6)958.1**(409.1)1236.1**(601.9)562.1(939.8)-1152.6(1113.8)-367.9(847.2)1692.0(1216.7)-2523.4**(1214.1)-156.4(180.7)-131.9(515.5)-442.8(428.5)-392.5(949.6)-328.5(558.9)0.70(0.50)
1.42(1.14)
1.99(1.46)
1.76*(1.05)
3.53**(1.67)-0.53*(0.28)-1.01(0.97)-0.86(1.62)-0.96(2.19)
1.02(1.60)

0.25
4688
0.88

0.72
4688
0.89

0.05
4688
0.60

1,988.714688
0.80

4,251.104688
0.24

535.13
4688
0.50

9.30
4688
0.85

1.74
4688
0.49

Notes: This table reports on the effect of treatment on employment outcomes; columns 4-9 are Winsorized at the 99th percentile. All regressions use data acrosssurvey rounds 2 - 20, which include four pre-treatment rounds, 13 treated months, and post-treatment rounds conducted 6 months and 12 months after the weekly
home visits ended. Panel A uses the full sample of respondents in the study, Panel B uses all respondents who ever reported being self-employed in a manufacturingbusiness in the five baseline rounds, Panel C uses all respondents who ever reported being self-employed in the five baseline rounds but not in a manufacturingbusiness, and Panel D uses all respondents who never reported being self-employed in the five baseline rounds. Each column within a panel reports results ofseparate regressions using individual- and month-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey wave level using the method of
Cameron, Gelbach, and Miller (2011) are reported in parentheses. The unit of observation is the individual/month and the reported coefficients correspond todummy variables equal to one for individuals offered weekly home visits from National Savings Bank deposit collectors in the months indicated. All regressions use
survey data; colums (1) - (3) report whether an individual reported being employed in the described activities at any point during a month, and Columns (4) - (8) reportmonthly totals. Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; *** significant at 1%.

4

Table 6: Estimated Impacts of Deposit Collection on Earnings Outcomes by Employment Subgroup
Panel A

Full Sample (N=783)(1)

Sources of income(3)(4)
Earnedincome: otherHouseholdRespondent
householdearned income earned income
members1853.5**
989.0
392.3
(768.3)(637.6)(578.9)(2)(5)
Transfers
from outside
household(remittance)
68.6(147.4)(6)
Other
householdinflows (e.g.,loan receipts)
858.2(914.4)(7)
Householdconsumption
899.6(950.4)611.109172
0.24

5,979.01
9172
0.20

Panel B: Some self-employment and some manufacturing during baseline (N=259)
Treated months 1-13
5711.3***4316.0***2329.7**1765.0*84.4(1925.6)(1286.2)(1131.6)(1049.2)(291.0)Control mean
Observations
R-squared

Uses of income
(8)
(9)

(10)

Total savings
883.0**(376.7)

Transfers to
outsidehousehold3.31(51.6)

Loan
payments
362.5(232.7)

16,316.90
9172
0.29

5,213.32
9172
0.33

353.379172
0.26

1,559.02
9172
0.20

19.0
(1272.4)

393.7(1388.1)

1898.8***(525.0)33.0(75.0)

796.9***(271.5)523.283388
0.22

5,874.11
3388
0.20

16,404.64
3388
0.29

5,281.50
3388
0.34

354.343388
0.25

1,658.38
3388
0.16

Panel C: Some self-employment but no manufacturing during baseline (N=160)
Treated months 1-13
594.3
738.7
-86.2
370.6
(3024.8)(1804.4)(1239.5)(1288.8)-97.8(325.0)-111.9(2215.8)

431.4(1819.7)-159.6(669.5)-223.7*(127.2)370.4(522.5)Control mean
Observations
R-squared

VARIABLES
Treated months 1-13

HouseholdIncome3185.3**(1240.6)

Control mean
Observations
R-squared

29,393.04
9172
0.36

29,306.01
3388
0.39

28,634.68
1979
0.39

22,022.68
9172
0.43

22,354.27
3388
0.42

12,077.75
3388
0.32

11,786.89
9172
0.52

9,988.233388
0.47

12,806.08
1979
0.57

9,190.31
1979
0.63

442.351979
0.18

4,919.05
1979
0.16

16,942.40
1979
0.31

4,964.74
1979
0.35

290.711979
0.27

1,122.05
1979
0.24

Panel D: No self-employment during baseline (N=364)
Treated months 1-13
1984.112.8
39.2(2097.1)(1313.9)(768.8)-497.9(1025.7)

102.7(252.8)2019.7*(1157.3)

1555.0(1182.8)445.9(826.8)63.6(70.3)

22.5(397.1)

Control mean
Observations
R-squared

14,114.14
4688
0.48

739.914688
0.23

6,443.58
4688
0.21

16,022.84
4688
0.27

5,250.704688
0.28

375.314688
0.23

1,640.54
4688
0.20

29,734.67
4688
0.32

22,300.75
1979
0.57

9,879.11
9172
0.38

21,666.27
4688
0.35

7,123.76
4688
0.31

Notes: This table reports on the effect of treatment on financial outcomes. All regressions use data across survey rounds 2 - 18, and outcomes are Winsorized at the 99% level. Panel
A uses the full sample of respondents in the study, Panel B uses all respondents who ever reported being self-employed in a manufacturing business in the five baseline rounds, Panel C
uses all respondents who ever reported being self-employed in the five baseline rounds but not in a manufacturing business, and Panel D uses all respondents who never reported being
self-employed in the five baseline rounds. Each column within a panel reports results of separate regressions using individual- and month-level fixed effects. Standard errors clustered at
the zone (treatment unit) and survey wave level using the method of Cameron, Gelbach, and Miller (2011) are reported in parentheses. The unit of observation is theindividual/month and the reported coefficients correspond to dummy variables equal to one for individuals offered weekly home visits from National Savings Bank deposit collectors
in the months indicated. All columns in the table use survey data, and outcomes are monthly flows for the variables indicated. Data include four months of pre-treatment data and 13
treated months. Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; *** significant at 1%.

5

Table 7: Savings Impacts Comparing Control to Control-to-Box Treatment (Switches on in Round 12)
Survey Data

NSB Institutional Data
# of Program
Transactions

Program
Deposits

Program
Deposits Withdrawals

Total # of
Transactions

Bank
Savings

Informaland Cash Savings

Total Savings

Panel A: Savings Impacts

(1)

(2)

(3)

(4)

(5)

(6)

(7)

Treated with Box Collection

1.04***

446.1**-33.3

1.06***

138.2-788.3*-704.7(0.23)(179.0)(208.2)(0.25)(244.0)(418.7)(520.9)Control group mean

0.098

39.4

-4.53

0.62

740.8

4253.95192.2

Observations

4890
0.50

4890
0.12

4890
0.099

4890
0.45

4890
0.23

4890
0.28

4890.00
0.29

R-squared
Panel B: Earnings and Labor Impacts

Survey Data

Y/N: Wage
Employment?

Y/N: Ag
employment?

Y/N: Selfemployment?

Wages earned

Business income

Wage hours

SE hours

Treated with Box Collection(1)
0.063**(0.030)(2)0.00085(0.022)(3)-0.11***(0.036)(4)782.7*(447.7)(5)-929.9(585.4)(6)
2.94**(1.27)(7)-2.27(1.86)

Control group mean
Observations
R-squared

0.15
4890
0.83

0.59
4890
0.91

0.55
4890
0.91

1158.44890
0.80

5831.8
4890
0.68

5.72
4890
0.81

25.7
4890
0.84

Notes: This table reports on the effect of the box collection treatment on savings outcomes (Panel A) and Earnings and Labor outcomes (Panel B). Results use datafrom round 2-18; the control group for this analysis remains untreated throughout, and the box treatment begins in round 11 when zones that had previously had no
direct ability to save were given access to lock boxes in the zone center that were collected weekly or biweekly by bank agents for NSB. Each column within a panel
reports results of separate regressions using individual- and month-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey wave level using
the method of Cameron, Gelbach, and Miller (2011) are reported in parentheses. The unit of observation is the individual/month. Outcomes are Winsorized at the
99% level. Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; *** significant at 1%.

6

Table 8. Does Deposit Collection Increase Savings More for Individuals with a Lower Immediate Discount Factor?
Dependent Variable:

Immediate Discount Factor * TreatedTreated at average value of Immediate_DF
Control group mean
Observations
R-squared

(1)

(2)

(3)

(4)

(5)

(6)

SurveyExperiment 'Sin'
Good
Consumption
(7)

(8)

(9)

(10)

-8038.8(14686.6)
3235.2**(1281.2)-6.50(7.10)
1.56**(0.71)

0.100(0.19)-0.034**(0.017)-6117.9(5042.2)
491.8(443.0)7914.1(9917.6)850.4(962.8)-0.81(314.6)
4.31(48.6)

0.11(0.49)-0.0076(0.045)-3490.1**(1774.1)
711.3***(202.1)-5433.9**(2661.4)
75.9(321.1)-8527.1**(3867.2)
936.0**(382.4)29307.7
9172
0.36

5.91
9172
0.83

0.53
9172
0.92

5559.09172
0.70

16229.3
9172
0.29

492.6
9172
0.53

0.15
1986
0.44

765.1
9172
0.25

4360.59172
0.32

5280.49172
0.33

Total Household
IncomeWage Hours

Self EmployedBusiness Income

Consumption

Consumption of'Sin' Goods

Bank Savings

Non-Bank
Savings

Total Savings

Notes: This table reports on the heterogeneous effects of treatment on financial outcomes. The interaction 'Immediate Discount Factor * Treated' gives the differential effect of the treatment according to the structural estimate of the beta parameter. The elicitation protocol for thismeasure is described in Section 5.2. This beta parameter is demeaned before interaction, meaning that uninteracted treatment term gives the impact of the treatment at the average value of beta (0.98), and the estimate of the beta parameter is Winsorized at the 10% and 90% levels.
Dependent variables are Winsorized at the 99% level. Each column reports results of separate regressions using individual- and month-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey-wave level, using the method of Cameron, Gelbach, and Miller(2011), are reported in parentheses. The unit of observation is the individual/month and the reported coefficients correspond to dummy variables equal to one for individuals offered weekly home visits from National Savings Bank deposit collectors in the months indicated. All columns
in the table use survey data, and outcomes are monthly flows for the variables indicated. Data include four months of pre-treatment data and 13 treated months. Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; ***significant at 1%.

Table 9. Heterogeneous Impacts by Degree of Control over Savings at Baseline
Dependent Variable:

TreatedTreated * No Savings Control
Control group mean
Observations
R-squared

(1)

(2)

(3)

(4)

(5)

(6)

SurveyExperiment 'Sin'
Good
Consumption
(7)

(8)

(9)

(10)

1739.9(1873.8)2250.8(1819.8)

1.53(0.94)-0.21(0.80)-0.036*(0.020)-0.0071(0.023)686.4(727.2)405.0(799.2)-69.0(1482.7)
1456.4(1204.3)

0.64(65.2)
97.0**(43.3)-0.099*(0.051)
0.16***(0.051)570.3**(267.2)201.0(298.7)138.6(433.2)-155.0(408.5)834.3(572.4)92.6(598.7)29,393.04
9172
0.70

9.30
9172
0.85

0.53
9172
0.96

5,758.68
9172
0.63

16,316.90
9172
0.64

513.34
9172
0.56

0.15
1986
0.52

756.819172
0.31

4,307.439172
0.52

5,213.32
9172
0.52

Total Household
IncomeWage Hours

Self EmployedBusiness Income

Consumption

Consumption of'Sin' Goods

Bank Savings

Non-Bank
Savings

Total Savings

Notes: This table reports on the heterogeneous effects of treatment on financial outcomes. The interaction 'Immediate Discount Factor * Treated' gives the differential effect of the treatment according to the survey response estimate of the β parameter. The β parameter is demeaned
before interaction, meaning that uninteracted treatment term gives the impact of the treatment at the average value of β=0.98. The estimate of the β parameter is Winsorized at the 10% and 90% levels. Dependent variables are Winsorized at the 99% level. Each column reports resultsof separate regressions using individual- and month-level fixed effects. Standard errors clustered at the zone (treatment unit) and survey-wave level, using the method of Cameron, Gelbach, and Miller (2011), are reported in parentheses. The unit of observation is the individual/month andthe reported coefficients correspond to dummy variables equal to one for individuals offered weekly home visits from National Savings Bank deposit collectors in the months indicated. All columns in the table use survey data, and outcomes are monthly flows for the variables indicated.
Data include four months of pre-treatment data and 13 treated months. Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; *** significant at 1%.

1

Table 10. Seetu Saturation Experiment Treatment Effects
Number of Seetus currently
Participating in
Treated

0.27*(0.14)

Monthly amount Saved
through Seetus

Total Monthly Savings

0.16
238.2
198.8
945.8*
844.7(0.13)(198.3)(190.1)(546.3)(585.5)
Seetu Treatment Saturation
1.42***
509.4
1304.7(0.53)(470.2)(2165.2)
Constant
1.263***
1.273***
2,167***
2,170***
2,818***
2,827***(0.08)(0.08)(146.40)(147.60)(441.50)(443.10)Control Group Mean
1.81
1.81
2032.62032.6
5311.95311.9
3255
3255
3255
3255
3255
3255
Observations
0.69
0.69
0.68
0.68
0.29
0.29
R-squared
278
278
278
278
278
278
Number of HHs
Notes: This table reports on the effect of treatment and the saturation of treatment in respondent's seetu (informal savings groups) on financial outcomes. All
regressions use data across survey rounds 2 - 18, and outcomes are Winsorized at the 99% level. Standard errors clustered at the zone (treatment unit) andsurvey wave level using the method of Cameron, Gelbach, and Miller (2011) are reported in parentheses. All columns in the table use survey data, andoutcomes are monthly flows for the variables indicated. Data include four months of pre-treatment data and 13 treated months. 'Treatment' is a dummy
indicating that the respondent household is receiving weekly home visits, and 'Seetu Treatment Saturation' gives the fraction of the respondents seetu that also
received the offer of treatment; this saturation was randomized to 0, 0.2, or 0.4 for seetus that had all members living in the same zone and did not containmore than 24 members. Each column reports results of separate regressions using individual- and month-level fixed effects. Treatment of non-study seetu
members began in round 6. Regressions pool samples surveyed monthly and samples surveyed quarterly. * significant at 10%; ** significant at 5%; ***significant at 1%.

2

FIGURES:

Figure 1. Maps of the Experimental Sample in Mahayangina and Bandarawela

LISTING

Originally Listed:Households within 5-15 km of bank branch, 1 km of main road
163 Zones
3,657 Households
5,080 Individuals

ELIGIBILITY & SAMPLING

Determining Eligible Sample for Study:
Imposing Study Eligibility Requirements:(1) Self-Employed (not full-time wage worker). (2) Home is accessible by Motorbike. (3) No formal bank transaction in past month.
156 Zones
1,469 Households
1,713 Individuals
Assigning Strata & Drawing Sample for Study:
S1: Members of 'Close Seetus' S2: Females who are not S1s,
w/in 1 km:
no duplicate households.

TREATMENTASSIGNMENT

N=101

S3: Males who are not S1s, noduplicate households.

S4: Fellow seetu member of
S1s who are not S2s or S3s,
no duplicate households.

N=207

N=259

N=228

Treatment Assignment at Zone Level
Allocated to Control, Surveyed at Baseline
78 Zones
406 Household & Individuals
S1:
S2:
S3:
S4:
53
103
109
141

ATTRITION

Allocated to Treatment, Surveyed at Baseline
78 Zones
389 Households & Individuals
S1:
S2:
S3:
S4:
48
125
98
118

Lost due to panel attrition in the household survey by Round 20: 0 zones, 27 individuals & households

ENDLINESURVEY

Surveyed at Endline

S1:
50

Allocated to Control
78 Zones
390 Households & Individuals
S2:
S3:
99
105

Figure 2. Overview of Study Design

S4:
136

S1:
47

Allocated to Treatment
78 Zones
378 Households & Individuals
S2:
S3:
120
95

S4:
116

Treatment Begins

0

.5

1

1.5

2

2.5

Number of financial transactions per month

Aug '10

Oct '10

Dec '10 Feb '11
Treatment, allControl

Apr '11round

Jun '11 Aug '11 Oct '11
Treatment, non-NSB

Figure 3. Treatment Impact on Bank Transactions

Dec '11Panel A: Monthly Bank Savings

Panel B: Average Monthly Total Savings

Panel C: Average Monthly Household Income
Figure 4. Cumulative Density Functions Across Treatment and Control
1Treatment Begins

4000

6000

Rupees8000 10000 12000 14000

Total Business Income per Month

Aug '10 Oct '10 Dec '10 Feb '11 Apr '11 Jun '11 Aug '11 Oct '11 Dec '11
round
Treatment

Control

Figure 5. Impact on Business Income2With 95 % Confidence Intervals
7
6
5
4
3
2
1

1000

2000

3000

Treatment Effect on Wage Hours

8

4000

Fan Regression of Wage Hours Worked by Beta

With 95 % Confidence Intervals

00Treatment Effect on Monthly Savings

Fan Regression of Total Savings by Beta

.85

.9

.95
1
Survey Measure of Beta

1.05

.85

Measure of Beta Winsorized at 10% and 90%

.9

.95
1
Survey Measure of Beta

Measure of Beta Winsorized at 10% and 90%

Figure 6. Fan Regression by Time Inconsistency

31.05