Can Self-Help Groups Really Be 'Self-Help'?

K.7 Can Self-Help Groups Really Be ‘Self-Help’? Greaney, Brian, Joseph P. Kaboski, and Eva Van Leemput Please cite paper as: Greaney, Brian, Joseph P. Kaboski, and Eva Van Leemput (2015). Can Self-Help Groups Really Be ‘Self-Help’?. International Finance Discussion Papers 1155r. http://dx.doi.org/10.17016/IFDP.2015.1155r International Finance Discussion Papers Board of Governors of the Federal Reserve System Number 1155r December 2015

Board of Governors of the Federal Reserve System International Finance Discussion Papers Number 1155r December 2015 CanSelf-HelpGroupsReallyBe‘Self-Help’? BrianGreaney JosephP.Kaboski EvaVanLeemput NOTE: International Finance Discussion Papers are preliminary materials circulated to stimulate discussion and critical comment. References to International Finance Discussion Papers (other thananacknowledgmentthatthewriterhashadaccesstounpublishedmaterial)shouldbecleared withtheauthororauthors. RecentIFDPsareavailableontheWebatwww.federalreserve. gov/pubs/ifdp/. This paper can be downloaded without charge from the Social Science ResearchNetworkelectroniclibraryatwww.ssrn.com.

CanSelf-HelpGroupsReallyBe‘Self-Help’? BrianGreaney* JosephP.Kaboski** EvaVanLeemput*** Abstract: We provide an experimental and theoretical evaluation of a cost-reducing innovation in the delivery of “self-help group” microfinance services, in which privatized agents earn payments through membership fees for providing services. Under the status quo, agents are paid by an outside donor and offer members free services. In our multi-country randomized control trial we evaluate the change in this incentive scheme on agent behavior and performance, and on overall village-level outcomes. We find that privatized agents start groups, attract members, mobilize savings, and intermediate loans at similar levels after a year but at much lower costs to the NGO. At the village level, we find higher levels of borrowing, business-related savings, and investment in business. Examining mechanisms, we find that self-help groups serve more business-oriented clientelewhenfacilitatedbyagentswhofacestrongfinancialincentives. Keywords: Microfinance,Self-HelpGroups,PrivatizedDelivery JELclassification: O1,O12,O16 *YaleUniversity. Contact: brian.greaney1@yale.edu **UniversityofNotreDameandNBER.Contact: jkaboski@nd.edu ***The author is a staff economist in the Division of International Finance, Board of Governors oftheFederalReserveSystem,Washington,D.C.20551U.S.A.Theviewsinthispaperaresolely the responsibility of the authors and should not be interpreted as reflecting the views of the Board of Governors of the Federal Reserve System or of any other person associated with the Federal ReserveSystem. Contact: eva.vanleemput@frb.gov. ResearchfundedbytheBill&MelindaGatesFoundationgranttotheUniversityofChicagoConsortiumonFinancialSystemsandPoverty. Wearethankfulforcommentsreceivedfromtheeditor and three anonymous referees, as well as presentations at Boston College, BREAD/Federal Reserve Bank of Minnesota Conference, Clemson University, the NBER Summer Institute, New York University, and UCLA. We have benefited from help from many people at Catholic Relief Services,especiallyMarcBavoisandMikeFerguson,andtheworkofexcellentresearchassistants: LukeChicoineandKatieFirthinthedatacollection,andMelanieBrintnallinthedataanalysis.

1 Introduction Over the past several decades microfinance services have expanded tremendously in developing countries. Anincreasinglycommonmethodofprovidingaccesstomicrofinancetothe“poorestof the poor” are self-help groups (SHGs). In their most common form, SHGs essentially act as tiny savings and loan cooperatives. Currently these SHGs reach an estimated 100 million clients and this number has grown dramatically in recent years; active plans will nearly double this number by 2017.1 Groups are not fully “self-help”, though. Although all funds are raised internally, the groups generally depend on outside assistance from administrative agents in their founding and continuedadministration. Thismotivatesanimportantquestion: Cancostreductionorrecoveryin thedeliveryofself-helpmicrofinanceprogramsbeeffectiveinmakingthemmorefullyself-help? The issue is common for many aid programs concerned with scalabilty, financial sustainability, and other types of aid, but the answer is not obvious. Recent research has shown that small costs to clients greatly reduce both take-up and program effectiveness.2 We provide a theory and evidence that microfinance is different, even in very poor populations: A cost-recovery approach can actuallybeeffectiveforSHGs. The paper examines an innovation to the provision of NGO-sponsored microfinance services inthreeEastAfricancountries: Kenya,Tanzania,andUganda. Thestatusquodeliverymechanism was a typical “continuous subsidy” program, in which the NGO would train agents and then continuallypaythemawageforstartingupafixednumberofSHGsandprovidingfinancialservices. In contrast, the innovation cut off payments to these agents after training, forcing them to become private entrepreneurs who start up any number of SHGs and earn their remuneration from their members. The hope was to not only lower costs to the NGO but also to expand access to services. Some programs already follow such an approach. A major World Bank/Indian government initiative with a goal of reaching 70 million new households is an important example.3 Hence, the 1TheNationalBankforAgricultureandRuralDevelopment(NABARD)programinIndiaalonehasgrownfrom 146,000clientsin1997to49millionin2010. 2See Kremer and Miguel (2007) for an example with deworming pills or Cohen and Dupas (2010)’s analysis of insecticide-treatedbednets. Thesehealth-relatedprogramshavepositiveexternalitiesthatfinancedoesnot. 3TheRuralPovertyReductionPrograminAndhraPradesh,India,wasanearly$300millionprojectbetween2000 and2009,whichhastrained140,000“communityprofessionals”(privatizedproviders),andreached9millionwomen through630,000SHGs. In2010,itwasexpandedintoanationwideprogram,theNationalRuralLivelihoodsMission, whichisspendingacombined$5.1billionfromtheIndiangovernmentand$1billionfromtheWorldBankoverseven 1

types of program and innovation we study are both of great interest. We examine the impact of this delivery innovation using a randomized control trial and a theoretical model in which control areas received the status quo program, while treatment areas received the private entrepreneur innovation. The results are powerful and encouraging for the prospects of self-help groups indeed being “self-help”, in the sense of being financially independent. Our randomization allows us to estimate the causal impacts on outcomes. The number of groups started by the treated agents, who charge fees, are slower to grow initially. However, after one year they reach the same number of clients and have more-profitable groups than the control agents, who provide their services for free. Moreover, the privatization treatment improves the outcomes of clients along many dimensions, leading to higher levels of: savings from business activities; credit, especially to business owners; employees; and business investment. It leads to households spending a higher fraction of their time on their business, and correspondingly less in agricultural activities. These impacts are witnessed despite the fact that clients must pay for services under the private entrepreneur model. (Point-estimates of impacts on household income and consumption are insignificant.) Finally, the composition of the entrepreneurs’ clientele is very different; the clients of the treated agents are more business-oriented and have a larger demand for financial services ex ante. Thus, the costsharing treatment appears to aim the program toward agents who are more likely to use the financial services for business purposes–the traditional goal of microfinance. Thus, cost-sharing could have important distributional consequences for NGOs with objectives beyond average impact and financialsustainability.4 To understand these results, we develop a theory in which cost recovery via membership fees can actually help solve an adverse selection problem that can plague credit cooperatives, especially when services are freely provided. Indeed, varying membership fees within a village can outperform a single membership fee. We provide suggestive evidence supportive of the role of membershipfees: feesarestronglyassociatedwithgreaterlevelsofintermediationandagentsappeartotargettheirfees,varyingthemsubstantiallybothwithinandacrossvillages. Incontrast,we years(WorldBank,2007,2012). 4Wenotetwoconsiderations, however. First, theentirepopulationisquitepoor. Second, wedonotfindthatthe programincreasesfoodvulnerabilityornegativeresponsestoadverseshocks. 2

find no evidence that agent behavior along other dimensions drives these results. Because our experimentlacksvariationinfeesthatisindependentofotherincentives,however,ourresultscannot definitivelyprovetheproposedmechanism. ThespecificvarietyofSHGsthatweevaluateempiricallyarecalledSILCs(SavingandInternal Lending Committees). SILCs are promoted by Catholic Relief Services (CRS), a major nongovernmental development organization, and are representative of other similar SHG programs sponsoredbyotheragenciesinthedevelopingworld.5 Inpractice,SILCsaresmallgroupsof10to 25 members that typically meet on a regular basis to (1) collect savings, (2) lend to members with interest, (3) maintain an emergency “safety net” fund, and (4) share profits from lending activity. They do not receive external financial resources, only assistance from the outside agents who foundandhelpadministerthegroups. Inthissense,theyeffectivelyoperateassmall,independent, quasi-formal,self-financingcreditcooperatives.6 Our empirical findings come from a large multi-country randomized controlled trial involving 276 agents who started a total of over 5,700 groups serving over 100,000 members across 11 districts in Kenya, Tanzania, and Uganda. All agents underwent a training phase. Upon completion, agentsintherandomizedtreatmentareasimmediatelybecame“PrivateServiceProviders”(PSPs): entrepreneurs who need to start new groups and charge fees to group members in order to receive remuneration. In the control areas, field agents (FAs) received wages from CRS for establishing and administering a set number of groups but they were not allowed to charge their clients. This randomization was performed at a geographic level, so that treated agents did not compete with agents in the control group. Several sources of data verify that the randomization was indeed random. In the post-treatment data PSP treatment increases group profitability by approximately 50 percent after one year. After three months, a PSP works with 4 fewer groups and 78 fewer clients, onaverage,thanatraditionalFA,butbyoneyearthedifferencesbecomestatisticallyinsignificant. 5These agencies include CARE, OxFam, Plan, World Vision and perhaps most importantly, NABARD, a large governmentagencyinIndia. 6The “self-help” goals of these groups are not limited to self-intermediation. (Indeed, mature groups in some regions actually leverage their funds through outside loans.) They are also intended to help local communities by building social capital, empowering women, and fostering improved collective action. These aspects–at least in the datawestudy–arerelativelyminorcomparedwiththefinancialactivities. 3

The total amount of savings, number of loans, total credit disbursed, and profits all show similar patterns: Theystartoutlowerbutincreaseovertimeandafteroneyearthedifferenceisstatistically insignificant. PSPs earn only one-sixth of what FAs earn over the first year, but their earnings increaseovertimeandagentattritionislow(lessthan2percentineithergroup). Overall,PSPsare substantially more cost effective, reducing the costs of providing services by over 40 percent after twoyears. Whenconsideringtheinnovation’sbenefitstohouseholds,theresultsareevenmoreencouraging. Despite the fact that households actually pay for services, the PSP approach is significantly moreeffectiveindeliveringoutcomespromotedbymicrofinance. (Weestimatetheseimpactsatthe villagelevel,whereassignmentisrandom,withoutreferencetomembershipwhichisclearlynonrandom). On an intent-to-treat, per-household basis, the PSP leads to nearly $27 (or 50 percent) more credit, $19 (or 90 percent) more business investment, 0.13 (110 percent) more employees hired, and 3 more hours per week (33 percent) in business. The point estimate of $15 (5 percent) more savings, is insignificant, but the $17 estimates for savings from business profits and savings forbusinesspurposesaresignificant. RelatedLiterature This paper contributes to several strands of literature. First, we contribute to a literature on cost recovery in development programs. Previous research on health-related cost sharing (i.e., Kremer and Miguel (2007) for deworming pills, Cohen and Dupas (2010) for insecticide-treated bed nets, and the simulations of Kremer et al. (2011) for clean water sources) highlighted the problemofsmallcostsloweringthenumberofclientsserved.7 Morduch(1999)conjecturedthatan emphasis on cost recovery in microfinance would limit its ability to reach the poorest households. We find that although costs alter the type of clients, the number of members is unchanged (and the cost-savings itself is important to expanding programs elsewhere). Low take-up of health interventions can lead to lower impacts, even on remaining clients, because the interventions have positive externalities. In contrast, we find higher aggregate impacts, and our theory suggests that 7Not all prior empirical evidence has been negative, however, even for services with a public-good aspect. In Argentina,Galianietal.(2005)foundthatprivatizationofwatersuppliesreducedchildmortality,especiallyinpoor areas. 4

financialservicesarequalitativelydifferentthanhealthinterventionsalongthisdimension. Second, there are different theories of microfinance and a burgeoning empirical literature that has yielded mixed results regarding its impacts. Some theories follow the traditional narrative by modeling credit that enables entrepreneurship, investment, and growth (e.g., (Ahlin and Jiang, 2008), (Buera etal., 2012)), whileothers emphasize consumptionsmoothing or simplyborrowing to increase current consumption (e.g., (Kaboski and Townsend, 2011), (Fulford, 2011)). Empirically, although there is evidence of very high returns to capital for some entrepreneurs,8 with a few exceptions, the impacts of microfinance on consumption and entrepreneurial activity have generally been small (e.g., (Banerjee et al., 2015), (Cre´pon et al., 2011), (Kaboski and Townsend, 2012) (Karlan and Zinman, 2010)). Still, Kaboski and Townsend (2005) found that program details matter for impacts, as was the case for two recent studies with sizable impacts on businesses: Attanasio et al. (2011) and Field et al. (2009), who find impacts for joint liability loans and loans with repayment grace periods, respectively. We show that the delivery mode and incentives faced byinstitutionscangreatlyaltertheentrepreneurialimpactofmicrofinance. Third, a large theoretical literature has examined credit markets under asymmetric information, including the design of cooperatives and lending groups (e.g., Banerjee et al. (1994), Ahlin and Townsend (2007), Wang (2013)). Seminally, Stiglitz and Weiss (1981) and De Meza and Webb (1987) analyze the impact of adverse selection on the provision of credit. The former show how it could lead to underprovision when entrepreneurs vary in the dispersion of returns, and the latter show that when entrepreneurs differ in their expected returns, adverse selection could lead to overprovision. Although our agents differ in their expected returns, as in De Meza and Webb (1987), our model has no room for overinvestment because we have a supply of funds in equilibrium, with the value of all projects exceeding their opportunity costs because agents with low returns also have low opportunity costs.9 Our contribution is to show how two-part pricing can mitigateadverseselectioninsuchasetting. Finally, there is a recent literature on SHGs. Two recent randomized control trials of CARE’s 8For example, de Mel et al. (2008) finds returns of 55 to 63 percent annually, substantially greater than market interestrates. 9Themembershipfeesweproposearedistinctfromcollateralbecausetheyaresunk;i.e.,theyarenotcontingent onborrowingorrepayment. 5

VSLA (Village Saving and Loan Associations) program found significant positive short-run impacts on food consumption in Malawi (Ksoll et al., 2012), and consumption, financial services, andassetsinBurundi(Bundervoet,2012). EvaluationsofOxFam’sSHGprogramareongoingbut havefoundfewerimpacts. The remainder of the paper is organized as follows. Section 1 describes the program, experiment, data, and methods. Section 2 presents the results and evidence of selection. Section 3 develops a simple theory of a credit cooperative and the potential impact of membership fees, and suggestivetestsoftheroleofmembershipfeesinthedata. Section4concludes. 2 Program and Methods ThissectiondescribestheoperationoftheSHGprogramswestudy. Wethendocumentthedetails oftheexperiment,ourdata,andourregressionequations. 2.1 SILC Program and PSP Innovation RecallthattheSHGspromotedbyCatholicReliefServicesarecalledSILCs(savingsandinternal lendingcommittees). AtypicalSILCisagroupofbetween10and25memberswhomeetregularly to save, lend to members, and maintain a social fund for emergencies. SILCs allow those with limitedaccesstofinancialservicestosaveandborrowinsmallamounts,whileearningintereston savingsandborrowingflexibly. SHGshavegainedwidesupportamongdevelopmentorganizations because, in contrast to many traditional microfinance institutions, they emphasize savings as well as credit. Research has shown that many people in developing countries lack adequate savings capabilities, and some even value savings accounts that pay negative interest (e.g., Dupas and Robinson(2012)). The advantage over more formal financial institutions is that SILCs are formed and meet locally,allowingmemberstoavoidtransportationandtransactioncoststhatareprohibitiveforthose who save and borrow small amounts. For SILCs in Kenya, Tanzania, and Uganda, meetings are generally weekly, with a median weekly deposit of $1.25. A typical loan would be $20 for 12 weeks at a 12-week interest rate of 10 percent. The loan would be uncollateralized except for the 6

personal savings in the fund.10 Funds accumulate through savings, interest on repaid loans, and fines for late payments/other violations. These funds are held centrally. The funds follow cycles that generally last one year. All loans must be repaid at the end of each cycle, and the total fund is then temporarily dissolved with payouts to members made in proportion to their total savings contributed over the cycle. For SILC, the timing of payouts is typically arranged to coincide with schoolfees,Christmas,orsomeothertimewhencashisneeded. SILCsoffergreaterflexibilitythanrotatingsavingsandcreditassociations(ROSCAs),andthe fact that funds can accumulate in a SILC allows for some of its members to be net savers, while others are net borrowers. The greater flexibility also makes their management nontrivial. They require strict record keeping to keep track of savings, loans, loan payments of various amounts, and payouts due. They also require judgment regarding who should receive loans, how much they should receive, and how to set interest rates. Risks of default are also potentially greater, since some members may borrow disproportionately, and this magnifies the importance of decisions on membership. In contrast to ROSCAs, SILCs do not arise spontaneously. Given their complexity, theroleoftrainedfieldagentsinfounding,administering,andtrainingthemembersthemselvesis critical. Theservicesprovidedbyfieldagentstothesegroupsincludeinitialtrainingandfollow-up supervision in the areas of leadership and elections; savings, credit, and social fund policies and procedures; development of a constitution and by-laws; record-keeping; meeting procedures; and conflictresolution. CRShastraditionallycatalyzedthisprocessbytrainingfieldagents(FAs)tostartSILCgroups. FAtraineesarerecruitedfromthemoreeducatedsegmentofexistingSILCmembers. Theyreceive initial training, begin forming groups within a month, and then receive refresher training three additional times; they are also monitored by a supervisor over the course of a year.11 During the training phase, agents are required to form 10 groups. At the end of the training phase, the agents take an exam; if they pass they are certified. FAs receive a monthly payment during the training phase ($48 in Kenya, $31.50 in Tanzania, and $50 in Uganda), but this payment increases after completion of the training phase (to $54, $59.50, and $65, respectively). The required stock of 10Notallfundsarelentoutasloans;aportionisretainedasasocialfundavailableforemergencyloans. 11Monitoringisdonebycheckingovertheconstitutionsandrecordbooksandoccasionallysittinginonmeetings ofSILCgroupsoftraineeFAs(generallyatleastonceamonth,rotatinggroups). 7

groups also increases by 10 additional groups, which they meet with regularly. Both during and afterthetrainingphase,agentsmustreportquarterlysummaryaccountingdataforeachgroup(e.g., group name, number of members, total loans, total credit, profits, payouts, defaults) following a standardizedMISsystem. Beyondthisdatacollection,thereislittleadditionaloversightfromCRS afterthetrainingphase. CRSintroducedthePSPdeliveryinnovationintothisexistingSILCpromotionprogram;inthe new program, fully trained FAs are certified as such and transition to PSPs, private entrepreneurs whoearnpaymentfortheirservicesfromtheSILCgroupsthemselvesratherthanfromCRS.PSPs negotiate their own payment from the SILC members, with the most common form of payment being afixed fee per membercollected at each meeting.12 After certification, paymentsfrom CRS to PSPs are phased out linearly over four months (75 percent of the training payment in the first month, 50 percent in the second month, etc.). CRS’ goal with this innovation is to lower the resources needed to subsidize SILCs, thereby improving both the long-term sustainability of the groupsandCRS’abilitytoexpandtheprogram. Theinitialimplementationofthisdeliverymodel was a large-scale Gates Foundation–funded program that involved training close to 750 agents to found roughly 14,000 SILCs and reach nearly 300,000 members. The FAs were recruited in three wavesoverthreeyears,asdifferentlocalpartners(typicallyCatholicdioceses)indifferentregions ofKenya,Tanzania,andUgandaentertheexpansion. 2.2 Experimental Design The research focuses on the outcomes of a randomized set of FAs/PSPs from the first two of these waves. Agents in the first wave were recruited and began training in January 2009. This first wave was certified between December 2009 and January 2010. Agents in the second wave were recruited in either October 2009 (Kenya and Tanzania) or January 2010 (Uganda).13 They were certified the following year, in October 2010 and January 2011, respectively. The second wave of agents represented an expansion of the program to new areas. After certification, those 12Forthosegroupsthatchargefees,themedianquarterlyfeepermemberis$0.50,whichamountstoabout3percent ofthemedianmember’squarterlydeposits. 13The original plan was for all three countries to begin in October 2009, but the partners in Uganda experienced operationaldelays. 8

agents randomized as FAs earned monthly payments mentioned previously, which were chosen to compare well with anticipated PSP earnings after certification, and were required to start or assist 10 additional groups. (Unfortunately, PSP earnings fell short of these anticipations, as discussed inSection4.1.) TheresearchincludesdatafrommultipleregionsacrossKenya,Tanzania,andUganda. Within eachregion,alocalpartnersupervisedtheimplementationoftheprograminconjunctionwithCRS andourresearchteam.14 Therandomizationwasstratifiedbycountryandassignmentwasdoneon a geographical basis, with all agents within a given geographical entity receiving the same assignment (FA or PSP). Treatment was assigned at the subdistrict level, with 50 subdistricts assigned to be served by the traditional FA program, and 108 subdistricts by the new PSP model. CRS had the goal of moving fully to the PSP delivery model in order to reduce costs, and all agents were recruited under the auspices of the PSP program. Both the partner organizations and their agents were notified of the particular randomized assignment just prior to certification. FAs did not remain FAs beyond the 12-month experimental phase, and out of concern for human subjects, the FAs were informed that they would transition to PSP assignment after 12 months.15 The geographical levels were chosen to ensure that FAs would not compete against PSPs: sublocations in Kenya, wards in Tanzania, and subcounties in Uganda. (Within any area, PSPs could and did competeamongstthemselves,however,includingchargingdifferentfees.) Therandomizationwas stratifiedbypartner,withrelativelymorePSPregions.16 From among the expansion agents who were recruited, the initial sample included all agents whohadnotyetreachedthecertificationstepatthetimeoftheinitialrandomization. Theoriginal year-1 sample included 51 agents in Kenya and Tanzania. In Kenya, the stratified randomization 14The first-wave partners operated in Mombasa and Malindi (Kenya) and Mwanzaa and Shinyanga (Tanzania). Within Kenya, the second wave included expansion into Mombasa and Malindi, as well as new partners in Eldoret andHomaHills. InTanzania,thesecondwaveexpandedintothreeexistingareasandaddedapartnerinMbulu. The Ugandansample,allsecondwave,includedpartnersinGulu,Kasese,Kyenjojo,andLira. 15In principle, this might reduce the likelihood of measuring differences between PSPs and FAs, since FAs may have behaved like PSPs (e.g., targeted clients, offering better services) in anticipation of this transition. However, whilewedofindsignificantdifferencesinoutcomesandselection,wedonotfinddifferencesintargetingorservices (seeSection2.3).Instead,weattributethedifferencestofees,whichweredefinitelynotchargedbyFAsinanticipation. 16Relatively more of the geographical regions were assigned to PSPs for two reasons. First, the PSP program is less costly for the NGO. Second, the expectation was that the variance in outcomes would be higher under the PSP program. Thesecondwaveaddedrelativelymoreagentsintotheevaluationsample,butsimilarnumbersofFAswere chosenacrosseachsampleinanattempttospreadthecostsofrandomization. Becausetherandomizationwasdoneat ageographicallevel,theratiosofFAstoPSPsarenotnecessarilyconsistentacrosspartnersorcountries. 9

yielded a total of 9 PSPs and 9 FAs spread across two partners, while in Tanzania there were 20 PSPsand13FAsspreadacrosstwopartners. Theyear-2sampleincluded225agentsfromKenya, Tanzania, and Uganda. In Kenya there were 71 PSPs and 24 FAs spread across four partners, in Tanzania there were 44 PSPs and 19 FAs spread across three partners, and in Uganda there were 41PSPsand26FAsspreadacrossfourpartners.17 Onedownsideoftheexperimentisthatitlacksa“true”control,inthesenseofasetofvillages receiving no SILCs whatsoever. Unfortunately, from an evaluation design perspective, CRS declined to create pure control groups. For that reason, we can only make statements about impacts of the PSP program relative to the FA variety, but we have no experimental evidence on absolute impacts. 2.3 Data Data were collected from four sources. The first, the MIS system, collects book-keeping accounting data at the level of SILC group. These group-level data (collected quarterly) include total membership,savings,credit,losses,interestrates,profitability,andpayouts,aswellasagentname and village. In order to pool the data across countries, we use exchange rates to put currency values into dollar equivalents. We analyze these data at the level of the SILC groups, but we also aggregate to (1) the level of the FA/PSP agents who operate them and (2) the level of village and analyzeattheselevels. Thesecondsourceofdata,anagent-levelsurvey,supplementstheMISwithagent-levelcharacteristics (e.g., age, education, languages, work and family background, importance of FA income, and labor) as well as a smaller set of questions (e.g., on targeting of groups, time spent with groups,andnegotiationofpayments)collectedeverysixmonths;additionalgroup-leveldatawere collectedeverysixmonthscoveringmembershipcharacteristics,deliveryofservices,andthecom- 17Therandomizationdoesnotcontainalloftherecruitedagents, particularlyinthefirstyear, forseveralreasons. First, the randomized evaluation was introduced somewhat late in the process (late December 2009). For the first wave, some partners had already certified their trained FAs as PSPs, and these were naturally excluded. Second, a smallnumberwerelostduetodeathorfailureofthecertificationtest.Finally,theinitialrandomizedsamplecontained 268agents,butunfortunatelytheagentsfromtwoofthepartnersinTanzaniahadtobedroppedfromthesampleafter thepartnersignoredrandomizationassignments. Thesepartnersconstituted6FAsand8PSPsinthefirstwave(from justonepartner)and29PSPsand6FAsinthesecondwave. 10

pensation scheme. Unfortunately, response rates on this survey were relatively low, so the sample isnotaslargeandmaysufferfrombiasesinresponserates. The third and fourth sources of data are based on a set of 192 randomly chosen villages. The villages were selected as follows. A subset of 192 agents was chosen among the full-year sample of 225 second-wave agents in April 2010.18 During this time, the agents were all in their training phase and had yet to be notified of their random assignment. For each of the 192 agents chosen, a village was randomly selected from among the villages in which they operated at least one SILC. In May 2010, a key informant survey was administered to that village chief. This survey (the thirdsourceofdata)collecteddataonvillageinfrastructureandproximitytoimportantinstitutions (schools, markets, health clinics, banks, etc.), chief occupations, history of shocks to the village, and,mostimportantly,avillagecensusofhouseholds. Our fourth source of data, a household survey, obtained representative village samples to enable a comparison of village means, without reference to membership in order to identify causal “intention to treat” impacts. The data were stratified over likely initial SILC members and nonmembers using the village census.19 In June, July, and August of 2010, the baseline survey was conducted among 1,920 households in eastern Kenya, Tanzania, and Uganda, respectively. (One village in Uganda was inaccessible and could not be surveyed.) A resurvey of the same households was conducted in Kenya and Tanzania (along with the Ugandan village not surveyed in the baseline) in June and July of 2011, approximately nine months after the agents had received certification. Uganda was resurveyed in October of 2011 , also nine months after agents had received certification. The household survey contained detailed data on household composition, education, occupation and businesses, use of financial services (especially SILC), expenditures, income, response to shocks, and time use, as well as some gross measures of assets, indicators of female empowerment and community participation, and questions about risk-aversion and discounting. 18Theseagentswerestratifiedacrosscountry(83of96inKenya, 47of63inTanzania, and62of67inUganda), buttheywereotherwisechosenrandomly. 19VillagecensuseswerematchedwithalistofknownSILCmembersinordertoselectasampleforthefourthdata source,thehouseholdsurvey. Thesemembersweremembersofagentgroupsduringthetrainingphase. Fromthelist ofSILCandnon-SILCmembers,asampleoffivehouseholdswithmatchedSILCmembersandfivehouseholdswith nomatchedSILCmemberswerechosenwithweightsassignedappropriatelybasedontheirproportionsinthematched villagecensuslist. ForhouseholdswithmatchedSILCmembers, therespondentistheSILCmember, whileforthe othersitwasgenerallythespouseoftheheadofhousehold(appropriatesinceSILCmembersaredisproportionately women). SeeSectionA.10intheonlineappendixformoredetailedinformationontheconstructionoftheweights. 11

Table A.1 in the online appendix presents some summary statistics in the baseline for households withandwithoutSILCmembers. Althoughthepopulationisquitepoor,SILCmemberstendtobe somewhat better off on a number of dimensions. Naturally, membership itself is endogenous, so thismembervs. non-membercomparisoncannotseparatetherolesofselectionandimpact. Thedataarehighquality,butmeasurementerrorisalwaysaconcernwithhousehold-levelsurveydatainadevelopingcountry. Ourworkingdefinitionof“household”reliesonself-identification andisbasedonjointconcepts: botheatingfromthesamepotandlivinginthesamehomeorcompound. Among the data collected, expenditures, time use, and income are the most difficult to measure. Our measures of income probably suffer from the most measurement difficulties.20 We focus on the respondent’s income since it is presumably better measured, and respondents (many ofwhomareSILCmembers)aremorelikelytobeaffecteddirectlybySILC. 2.4 Empirical Methods We use simple regression methods tailored toward the different data sets. We first present our methodsforestimatingimpactandthendiscussourverificationoftherandomization. 2.4.1 MeasuringImpact Ourestimationapproachesdifferslightlydependingonthedatasource. AgentandGroupImpacts Fortheagent-leveldata,weusethefollowingregressionequations: Y = α +X β +γwave +δPSP +ε (1) idnt dt i i n itdn (cid:88)4 Y = α +X β +γwave + δ PSP +ε (2) idnt dt i i s ns itdn s=1 Here,Y representstheoutcomeforagentiindistrictd,subdistrictnattimet. Theoutcomeswe idnt examinefromtheMISdataaretotalmembers,savings,numberofloans,valueofloans,profits,and agentpay. Herewecontrolforseveralthingsbyaddingdistrict-timefixedeffects,α ;adummyfor dt 20SeeSectionA.10intheonlineappendixformeasurementofthesevariables. 12

thewaveofagenti,wave ;andtheaboveagenticharacteristics(gender,age,schoolingdummies, i numberofdependents,andnumberofchildren),X . ThevariablePSP isadummythatispositive i n forhouseholdsintreatmentvillagesduringthefourquartersoftreatment,whilePSP isspecific ns to quarter s. Given eight quarters of data, we look for both an overall effect, δ (equation (1)), and duration-specifictreatmenteffects,δ (equation(2)),foreachofthefourtreatmentquarters. s For the group-level data, the data are no longer aggregated across agents. We use the identical regression,however,exceptinowrepresentsgroupi. Fortheseregressions,thestandarderrorson estimatesareclusteredbysubdistrict. Household-LevelData Forthehousehold-leveldata,wesimplyhavetwocross-sections. Ratherthanfirstdifferencing, which could exacerbate measurement error, we simply add the baseline outcome variable as a controlandestimateimpactusingthefollowingregressionequation:21 Y = α +X β +ρY +δPSP +ε . (3) jdn d j jdn,t−1 n jdn The outcomes Y for household j, living in district d and subdistrict n, depend on a districtjdn specificfixedeffect,thecharacteristicsofthehouseholdX (gender;ageandage-squared;schoolj ing dummies; and the number of adult men, women, and children in the household), and the baseline value for the outcome Y . Again, δ is the measure of the treatment effect. For the jdn,t−1 household data, we cluster standard errors by subdistrict, the level of treatment. We have 147 subdistrictsinthehouseholddata. Here,theimpactoftreatmentisevaluatedatthevillagelevel,withoutreferencetoSILCmembership. The primary reason for this is that SILC membership itself is naturally endogenous. A secondaryreasonisthattheoverallimpactofSILCcouldinvolvespilloverimpacts(eitherpositive ornegative)onnon-members. Intheresultssection,wefocusexclusivelyontheestimatesofδ andδ .22 s 21Ignoringthepanelaspectofthedataandsimplyusingtheendlinedataexpandsthesamplesomewhatandproduces verysimilarresults. 22SectionA.2intheonlineappendixprovidesfullregressionresultsforasampleofeachoftheagent,group,and householdregressions. 13

2.4.2 BaselineRandomization TheabovemethodsrelyontheexogeneityofthePSPtreatment,PSP,whichoughttofollowfrom ourrandomization. Weverifytherandomizationusingseveralmethods. First, using the baseline data, we verify that the randomization was successful in terms of observables. We do this using three data sets: the village-level key informant data, the agent-level data(bothMISandagentcharacteristics),andthehouseholddata. For the agent-level data, we focus on a simple regression on the data used for explanatory variables: X = α+γwave +δPSP +ε , i,n i n i,n where i again indexes the agent and n indexes the subdistrict in which the agent operates. We presenttheresultsforourindependentvariablesusedbelow. Wecontrolforthewaveusingwave . i PSP is a dummy for whether subdistrict n received the PSP program, so that δ = 0 is the n null for the test of random assignment. We cluster the standard errors by subdistrict, the level of randomization. Table 1 shows the baseline estimates for agents operating in the treatment (PSP) and control (FA) areas. We see no significant differences in gender, age, languages spoken, or number of childrenordependentsacrossthetwosamples. Wedo,however,seeasignificantlyhigherfraction ofPSPsreceivingsecondaryeducationandacorrespondinglylowerfractionofPSPswithprimary school completion as the highest schooling attained. We believe this to be a purely random result ratherthanaproblemwiththeimplementationoftherandomization. For the household-level data, we use only the first wave, and data are weighted appropriately (to account for the stratified sampling across likely members and non-members). Hence, a simple meancomparisonsuffices: X = α+δPSP +ε . j,n n j,n Here,j indexeshouseholdj,andthenullofδ = 0isagainthetestforrandomassignment. The top panel of Table 2 shows similar results for the household characteristics. Again, the assignmentoftreatmentappearstohavebeenrandomwithrespecttotheunderlyingcharacteristics 14

Table1: Agent-LevelRandomizationResults Age Gender Primary Primary Secondary Tertiary Languages Children Financial Complete Dependents PSP -0.33 -0.06 0.00 -0.14*** 0.12* 0.02 0.09 -0.33 -0.40 s.e. (1.2) (0.07) (0.01) (0.05)† (0.07) (0.05) (0.08) (0.36) (0.6) FAMean 36 0.69 0.01 0.46 0.43 0.10 1.9 4.6 6.4 Obs. 223 227 226 226 226 226 227 227 226 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated outcome on a PSP dummy and the following controls: age, age squared, gender, dummies for schooling (i.e., primary completed, secondary, and tertiary with a baseline of less than primary complete), number of languages spoken, number of children, number of financial dependents,cohort,andlocationfixedeffects. Theregressionsareweightedbysamplingweights. Standarderrorsare robustandclusteredbysubdistrict. of households, with the exception of education. Here, we see that the fraction of people whose highest attainment is primary school completion is significantly lower (0.08), and some of this is becausethefractionwithsomesecondaryschoolingissomewhathigher(0.02). Again,webelieve thiseducationresulttobepurelyrandom. We perform several exercises to ensure that our results are not driven by the higher schooling of either the agents or recipients in PSP areas. First, we include dummies for highest education attainedinallregressions. Ofcourse,iftherearealsosignificantdifferencesinunobservables,this would not be sufficient. Second, the significant difference in education is concentrated in districts served by two partners: the Archdiocese of Mombasa in Kenya and Tahea in Mwanzaa, Tanzania. All of our significant results are robust to dropping these two areas, as Tables A.13 to A.17 in Section A.8.1 of our online appendix show. Third, we examine the impact of dividing the sample byaveragevillageeducationratherthanPSP/FAtreatment. Wediscussthoseresultsbelow. Finally, we verify that our outcomes from equation (3) do not show “impacts” in the baseline householddata–i.e.,priortotreatment. ThebottompanelofTable2verifiesthisforthe27outcome variablesweexamine. Again,weseethatthedifferencesacrossthecontrolandtreatmentaresmall and insignificant. The only exception is income, which is substantially higher in the PSP villages. Thisisonlysignificantatthe10percentlevel,and,again,webelieveittobepurelyrandom.23 23Randomizationresultsfor23villagecharacteristicsfromthevillagekeyinformantsurveydataalsosupportthat the randomization was indeed random (Table A.5 of the online appendix). These data include the village population, thepresenceofvariousinfrastructure, services, andfacilitiesinthevillage–includingfinancialinstitutions–and whetherthevillagehadexperiencedvariousnaturaldisastersinthepastfiveyears.Thedifferencesbetweenthecontrol 15

Table2: Household-LevelRandomizationResults-BaselineDemographicsandOutcomes PSP FA PSP-FA Demographics/Controls Mean Std. Dev. Obs. Mean Std. Dev. Obs. Mean(cid:52) Age 43 13 1362 43 14 536 0.31 AgeSquared 2006 1277 1362 2007 1336 536 29 Gender 0.61 0.49 1363 0.57 0.50 534 0.03 #AdultMen 1.6 1.1 1380 1.5 1.1 539 0.06 #AdultWomen 1.5 0.92 1380 1.6 0.96 539 -0.05 #Kids 2.6 2.0 1380 2.7 1.9 539 -0.07 NoSchooling 0.21 0.41 1363 0.22 0.42 534 0.01 SomePrimary 0.23 0.42 1363 0.20 0.40 534 0.02 PrimaryCompleted 0.41 0.49 1363 0.48 0.50 534 -0.08***† Secondary 0.12 0.32 1363 0.09 0.28 534 0.02 Tertiary 0.03 0.16 1363 0.02 0.13 534 0.01 Outcomes(measuredpre-treatment) Mean Std. Dev. Obs. Mean Std. Dev. Obs. (cid:52)Coeff. TotalSavings 138 299 1380 134 291 539 -2.5 SavingsforBusinessOwners 159 284 624 151 322 252 -8.6 SavingsfromBusinessProfits 30 169 1380 35 203 539 -5.1 SavingsfromAgric. Profits 31 216 1380 23 114 539 -0.26 SavingsfromSalary/wage 17 105 1380 16 153 539 -2.1 SavingsusedforNewAgric. Activity 38 224 1380 38 170 539 -6.6 SavingsusedforNewNon-Agric. Activity 9.2 125 1380 5.3 31 539 3.9 SavingsusedforExistingBusiness 22 201 1380 16 186 539 2.1 TotalCredit 48 214 1380 42 273 539 3.0 CreditforBusinessOwners 61 231 624 40 108 252 14 CreditfromSILC 4.1 17 1380 3.7 18 539 0.48 CreditfromFormalLenders 36 211 1380 26 269 539 5.8 CreditfromInformalLenders 9.0 26 1380 12 51 539 -3.3 CreditusedforAgric. Activity 13 131 1380 6.8 56 539 4.9 CreditusedtoExpandBusiness 13 127 1380 6.1 46 539 6.6 CreditusedtoStartNewBusiness 1.5 19 1380 1.4 17 539 0.14 StartNewBusiness 0.27 0.44 1380 0.26 0.44 539 0.03 BusinessInvestment 39 147 1380 41 143 539 -2.8 HoursspentinBusiness 15 19 1380 15 19 539 0.53 Non-HHEmployees 0.29 2.0 1380 0.42 4.3 539 -0.12 HoursspentasEmployee 16 18 1380 15 17 539 0.60 Agric. Investment 57 457 1380 44 126 539 5.8 HoursspentinAgric. 27 15 1380 27 15 539 -0.47 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Thetoppanelpresentsthehouseholdrandomizationresultsforthedemographiccontrolsandthebottompanelpresents theoutcomevariables. Thelastcolumnofthebottompanelshowstheestimatedcoefficientsfromaregressionofthe statedoutcomeonaPSPdummyandthefollowingcontrols: age, agesquared, gender, numberofmen, womanand childreninthehousehold,dummiesforschooling(i.e.,someprimary,primarycompleted,secondary,andtertiarywith a baseline of no schooling). All regressions utilize sampling weights. After weighting, the sample is representative at the village level, including all households within FA or PSP villages irrespective of SILC membership. Standard errorsarerobustandclusteredbysubdistrict. 16

2.4.3 ReasonsforImpact Using multiple methods, we explore three potential explanations for the impacts: (1) improved member selection by agents or households, (2) improved effort by agents, and (3) improved effort bymembers. For the first explanation, our methodological approach is to include an interaction between a dummy for the PSP treatment with baseline variables, which are exogenous with respect to the randomizedtreatment,inregressionsexplainingendlinemembership. Thatis,werun M = α +X β +η Zbaseline +η PSP Zbaseline +ε , (4) jvn v j 1 j 2 n j jn whereM isendlinemembership(ofhouseholdjinvillagevandsubdistrictn)andZbaselineindijvn j cates various baseline household characteristics (income; business income; a dummy for whether the household had positive savings; a dummy for whether the household had positive hours in business; and dummies for whether the household’s estimated linear discount factor and hyperbolicdiscountfactorareabovethemedian).24 Notethatthefixedeffectsα arevillage-specific,so v that the coefficient of interest η will be identified from within-village variation in membership.25 2 The η coefficient estimates differential selection in PSP villages, i.e., the extent to which endline 2 membershipismorecloselyrelatedtoZbaseline invillageswithPSPs. j Forthesecondexplanation,theagentquestionnairegivesseveralmeasuresofagents’behavior, including howhouseholds weretargeted for newgroups (basedon demand, need,proximity, local connections,etc.),andthreemeasuresof“effort”: thefrequencyofservicesprovidedtothegroup, thetypeofservicesprovided,andthedistancetraveledtothegroup. Weexaminetheseasoutcome variables in the agent-level regression equations, equations (1) and (2) above. The only difference isthatthesedataareonlyavailableeverysixmonths,soourtime-specificestimatesinequation(2) aresemi-annualratherthanquarterly. FAvillagesandtreatmentPSPvillagesareallsmallandinsignificant. Theloneexceptionisanimaldiseasewithinthe pastfiveyears,whichoccurredin41percentofPSPvillagesbutonly21percentofFAvillages,statisticallysignificant atthe1percentlevel. 24Thehyperbolic(δhyp)andlinear(βlin)discountratesareestimatedbyusingindifferencevaluations(V)between time0andtimetusingthefollowingformulas: V =δhyperβtV . 0 t Weobtainedtwoestimatesusingtwosetsofquestions: (1)tradeoffsbetween0and1monthtogetherwith12and 13monthsand(2)0and3monthstogetherwith12and15months. Weusedtheaverageofthetwoestimates. 25Alternativeregressionswithoutthesefixedeffectsyieldverysimilarresults. 17

For the third explanation, we have data on the total hours per week spent working from the householdtime-usedata. Althoughadmittedlylimited,hoursworkingdoesgiveussomeinformationontherespondents’overalllevelsofeffort. 3 Results We evaluate the impacts of the PSP program on PSP agents and groups themselves first and then onhouseholds. Finally,weexaminepotentialexplanationsforthedifferentialimpactofPSPs. 3.1 Impact on Agents and Groups Table3presentstheagent-levelresultsforvariousmeasures. Thesecoefficientscanbeinterpreted as treatment effects on the agents and the overall level of services intermediated by them.26 As we are performing multiple testing, we also include Bonferroni corrections at a statistical level of α where α and m represent the significance level and the number of regressions in each table, m respectively. The first row presents the overall impact δ from equation (1). With the exception of agent payments, which are quarterly flows, the dependent variables are accumulated stocks. On average across the four quarters, PSPs start 2.6 fewer groups, reach 62 fewer clients, and earn $150 less in payments per quarter, all of which are significant at the 1 percent level. Based on these numbers, one might be skeptical that the PSP program will expand SILC services as well as theFAprogramwill. The remaining rows, which present the duration-specific estimates of δ from equation (2), ofs fer stronger insight, however: PSPs start off more slowly than FAs, but they improve over time. Thismaybedemanddriven,asthePSPserviceisnotfree,butitmayalsobeasupplysidestrategy of PSPs as they, for example, attempt to learn about their markets slowly. PSPs do significantly worse over the first three quarters in starting groups, reaching members, and intermediating loans, but these differences narrow over time and by the fourth quarter of treatment are not statistically distinguishable. Thus, by the end of the year, PSPs seem to be providing levels of services com- 26Withrespecttotheclientsthemselves, thesetreatmenteffectsontheagentscouldencompassboththeselection ofdifferentclientsandcausalimpactontheclients. Thisestimationdoesnotdistinguishbetweenthetwo. 18

Table3: PSPImpactsonAgent-LevelOutcomes Groups Members Savings Loans Loan Profit Earnings Value AllQuarters -2.6*** -62*** -1090 -35* -1050 -400 -150*** s.e. (0.93)††† (24)† (800) (18) (730) (310) (5.0)††† Quarter1 -3.6*** -78*** -1150* -46** -1280** -290 -160*** s.e. (0.91)††† (25)†† (650) (18)† (650) (230) (5.2)††† Quarter2 -2.4*** -63*** -1740* -45** -1720* -870* -150*** s.e. (0.91)† (23)† (940) (19) (920) (490) (6.4)††† Quarter3 -3.1*** -70*** -1320 -37* -1300* -540 -140*** s.e. (1.1)†† (27)† (870) (20) (750) (380) (6.3)††† Quarter4 -1.6 -40 -170 -12 55 130 -150*** s.e. (1.3) (29) (1090) (22) (910) (370) (4.9)††† FAMean 20 430 7610 230 7100 2140 180 Obs. 865 865 865 865 865 865 865 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated group-level outcome on a PSP (the randomized treatment)orPSP*Quarterdummyandthefollowingcontrols:age,agesquared,gender,numberoflanguagesspoken, numberofchildren,numberoffinancialdependents,dummiesforschooling(i.e.,primarycompleted,secondary,and tertiary with a baseline of less than primary complete), cohort, and location-date fixed effects. The regression is weightedbysamplingweights. Standarderrorsarerobustandclusteredbysubdistrict. parable to the FAs’. Payment for PSPs remains lower than for FAs, however, with the gap in cumulativepaymentswideningovertime. Indeed,ifwecalculatethecumulativepaymenttoPSPs attheendoftheyear,theaverageis$550lessthanthe$708averagecumulativeearningsofFAs.27 The smaller effects on the level of services in the early years are driven entirely by the fact that PSPs have fewer groups. Indeed, running comparable regressions at the group level yields no statistically negative impacts of PSPs, even early on (Table A.7 of the online appendix). Over time, we see relative improvements in membership, savings, loans, and profits over time, even at the group level. By the fourth quarter, a PSP’s typical individual group has more savings, more credit, higher profits, perhaps an extra member, and statistically indistinguishable agent pay per group. In relative terms, these group-level differences are considerable–nearly 50 percent higher thanthecontrolmeansforsavingsandprofitand25percenthigherforloanvalue. Insum,PSPsappeartohaveslowerstarts,butwithinfourquarterstheyappeartobestatistically indistinguishablefromFAsintermsofthenumberofgroupstheystart,clientstheyreach,savings 27Table A.18 in Section A.8.2 of the online appendix shows the unweighted regression in Table 3. The point estimatesandsignificancelevelsarehighlyrobust. 19

theymobilize,andcredittheirgroupsprovide. Theyearnsubstantiallyless,especiallystartingout, buttheirgroupsareultimatelymoreprofitable. Nevertheless, given the PSP’s substantially lower cost to the NGO relative to FAs, after only one year the PSP’s costs per member reached are substantially lower than the FA’s costs. In the training year, both FAs and PSPs earn an average of $518. In the year after certification, FA costs amounts to $714, while PSP costs are only the first-quarter phase-in value: $65. Thus, over two years,thecostofaPSPisjustabouthalf(i.e.,(518+65)/(518+714))ofthecostofanFA.Since the cost of additional years is zero for PSPs, these numbers will almost certainly continue to fall over time. Averaged over the course of the first year, PSPs reach 62, or about 15 percent, fewer members (368 vs. 430), so the per-member cost of the PSP program is just over half (55 percent) of what the FA program costs. Since PSPs reach similar numbers of members by the end of the year, the relative cost of PSPs per-members reached will also almost certainly fall over time. If PSPscontinuetogrowrelativetoFAs,thentheirrelativecostcouldfallevenmorerapidly. AlegitimateconcernmightbePSPretention,giventheirmuchlowerearnings. Sofar,however, thedropoutratesareverylowacrosstheboard–1.6percent(3of185)forPSPsand1.1percent(1 of91)forFAs. Infact,thismayindicatenotthatPSPpayistoolow,butratherthatFAswerepaid morethantheminimumamountneededtoretainthem. 3.2 Impact on Households Although the PSP program appears to be cost effective in reaching households and providing services,anotherimportantquestioniswhetherithassimilareffectsonthehouseholdsitreaches. We nowturntothehouseholddatatoevaluatetherelativeimpactsofPSP-runSILCsonhouseholds.28 We first examine savings, credit, and productive decisions before examining the overall impact on incomeandexpenditures. Table 4 presents the impact estimates of δ in equation (3) for savings and borrowing behavior. With respect to savings (top panel), we see no significant impact on overall aggregate savings, notably including no effect on the savings of business owners, but the reported source and use of 28Herewehavethevillage-levelanalogtotheinterpretationcaveatinfootnote26. Thecausalimpactsonvillages encompass both causal changes on household-level behavior (e.g., reason for saving) and changes in the relative importanceofbehavior(e.g.,levelsofsaving)acrosshouseholds. 20

savings are both impacted. The PSP program leads to an additional $17 of savings (per household inthevillage)comingfrombusinessprofits(significantatthe5percentlevel),butithasnoimpact on the amount of savings coming from agriculture or wage income. Similarly, an additional $16 per household was saved by households that report using savings for existing businesses, and this estimate is significant at the 1 percent level. These estimates are substantial in percentage terms, amounting to increases of 120 percent and 400 percent, respectively, relative to the FA villages. Thus,PSPsseemtohaveimportanteffectsonreportedbusiness-orientedsavings. Table4: PSPImpactonEndlineHouseholdSavingsandCredit Source Purpose PANELI:Savings Total Business Business SellAgric. Salaryor NewAgric. NewNon-Agric. Existing Owners Profit Product Wage Activity Activity Business PSP 15 -3.7 17** -3.9 8.5 0.52 -2.2 16*** s.e. (13) (16) (6.2)† (8.7) (5.3) (11) (2.5) (4.7)††† FAMean 131 152 14 39 10 38 4.2 4.0 SampleMean 141 153 24 37 15 37 2.6 15 Median 61 83 0 0 0 0 0 0 PANELII:Credit Total Business SILC Formal Informal Agric. Expanding StartNew Owners Activity Business Business PSP 27** 23*** 4.4** 15 8.6*** 7.5*** 9.0*** 1.9 s.e. (11) (8.5)† (2.0) (9.7) (2.9)†† (2.8)† (3.0)†† (1.3) FAMean 41 32 7.6 22 10 4.6 3.5 1.7 SampleMean 56 50 10 30 16 8.7 9.9 3.0 Median 11 15 0 0 0 0 0 0 Obs. 1891 865 1891 1891 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e.,someprimary,primarycompleted,secondary,and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sampleisrepresentativeatthevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILC membership. Standarderrorsarerobustandclusteredbysubdistrict. Turning to credit (the bottom panel), we see that the PSP program led to substantially higher levelsofborrowing. Theestimateof$27isanincreaseofover60percentrelativetotheFAmean, anditissignificantata5percentlevel. Thecomparably-sizedestimateof$23forreportedbusiness owners amounts to an even larger percentage increase, which is significant at the 1 percent level 21

despitethemuchsmallersamplesize. TheadditionalcreditdoesnotcomeexclusivelyfromSILC, although per-household levels of credit from SILCs are $4 higher in PSP villages (significant at the5percentlevel). Weseethatborrowingfrominformalsourcesactuallyplaysalargerrole,with acoefficientof$9thatisstronglysignificantatthe1percentlevel.29 ThereportedpurposeforborrowingisalsoaffectedbythePSPprogramwithanadditional$8ofcreditforagriculturalactivities and $9 of credit for existing businesses (both significant at the 1 percent level). Both of these are increasesofover100percent. Incontrast,thereisnoimpactoncreditfornewbusinesses.30 Table5delvesmoredeeplyintotheimpactofPSPsontheproductivedecisionsofhouseholds. Ingeneral,PSPsleadtorelativelymorepositiveimpactsonbusinesseffortsbut,ifanything,fewer positiveimpactsonagriculture. WefindnosignificantimpactofthePSPprogramonnewbusiness starts (although the power of the test is clearly weak).31 We do, however, find significant impacts on the intensive margins of business. Business investment rises by $20 per household in response to the PSP treatment. Thus, business investment under the PSP treatment is roughly twice its level under the FA control. Likewise, time spent in business is higher by three hours per week, a difference of about 33 percent relative to FA control villages. The number of non-household membersemployedbythehouseholdsinthesampleislowoverall(0.19perhousehold),withmost households employing no outside workers. Still, the coefficient of 0.13 employees per household, significant at a 5 percent level, represents an increase of over 100 percent relative to the FA level. We do not see a significant corresponding increase in the hours spent as an employee, however. Respondents may be less likely than other household members to work as employees. The point estimateispositive,butinsignificantandsmallrelativetothemean. Finally,welookatagricultural decisions. Although credit for stated agricultural activities had been positively impacted by PSPs, 29Whilesomestudieshavefoundthatmicrofinancesubstitutesfororcrowdsoutinformalborrowing(e.g.,(Banerjee et al., 2015)), other programs have led to increases (e.g., (Kaboski and Townsend, 2011), (Kaboski and Townsend, 2012)). Itispossiblethatfundsareeitherleveraged,relenttoothers,orthatrepaymentitselfleadspeopletoborrow fromadditionalsources. 30Table A.20 in Section A.8.2 of the online appendix shows the equivalent unweighted regressions from Table 4. Onthesavingsside,wefindsimilarpointestimatesonsavingscomingfrombusinessprofitsandsavingsgoingtoan existingbusinesswiththesamestatisticalsignificancelevels. Withregardstocredit,welosesignificanceoncreditfor businessownersandcreditfromSILC. 31The insignificant point estimate would indicate that the fraction of households starting new businesses in PSP areaswas5percentagepointshigher. Theratesofbusinessownershipandbusinessstartsarehighinthedata. Inthe endlinesample,42percentofhouseholdsownabusinessand24percentreportedstartinganewbusinessinthepast 12months. 22

the relative effect on agriculture investment is insignificant, and agricultural investment remains substantially larger than business investment. The lack of an impact on agriculture may be due to thefactthatloandurationwastypicallyshorterthancropcycles. PSPsleadtofewerhoursspentin agriculture relative to FAs, however. The coefficient of –3 (hours per week per respondent) nearly offsetsthepositiveimpactonhoursspentinbusiness.32 Table5: PSPImpactonEndlineHouseholdProductiveDecisions StartNew Closed Business Hoursspent Employees Hoursspent Agric. Hoursspent Business Business Investment inBusiness (non-HH) asEmployee Investment inAgric. PSP 0.05 -0.17*** 20*** 3.4** 0.13** 0.87 4.2 -2.8* s.e. (0.05) (0.06)† (5.7)††† (1.5) (0.05) (1.5) (9.9) (1.4) FAMean 0.20 0.49 21 9.4 0.11 14 67 32 SampleMean 0.24 0.42 35 12 0.19 15 69 29 Median 0 0 0 0 0 10 28 30 Obs. 1891 865 1891 1891 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e.,someprimary,primarycompleted,secondary,and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sampleisrepresentativeatthevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILC membership. Standarderrorsarerobustandclusteredbysubdistrict. We have also examined two simple summary measures of welfare: income and expenditures. Unfortunately,however,theevidenceisweak,andourexperimentlackspoweralongthesedimensions. The point estimates are substantial for total income, business income, total expenditures, and total consumption (roughly 25 percent increases in total income and business income, and roughly 10 percent in consumption and expenditures) but they are not significant, with the exception of total expenditures, and that is only at the ten percent level. Nonetheless, the fact that these estimates are not negative might be at least somewhat surprising, since clients must pay for their servicesoutofpocket.33 One concern we had was that the PSP-led groups might have a greater impact on businessorientedbehavior,butthatthismaycomeattheexpenseofotherpotentialbenefitsoftheprogram, such as consumption smoothing (through risk-sharing, credit, or dissaving in response to shocks) 32TableA.21intheonlineappendixshowstheunweightedregressionsforTable5.Welosesignificanceonbusiness investment,thenumberofemployeeshiredandhoursspentinagriculture. 33TheresultsareshowninTableA.8intheonlineappendix. 23

or financing the purchase of durables. To evaluate this, we looked at several measures, including (1) the probability of “ever going to sleep hungry,” (2) the probability of experiencing various adverse shocks, and (3) the “number of weeks until finances returned to normal” following an adverse shock.34 The point estimates on PSP were generally positive, but none were significant. That is, we certainly do not see evidence that PSPs underperform along this dimension. Instead, weviewthetwoprogramsascomparablealongthisfront. 3.3 Reasons for Differential Impact In this section, we explore potential mechanisms that may drive the observed impacts. We find strong suggestive evidence that PSP programs cater to different people, and very weak evidence fortheeffectofincentivesonotherdimensions. Table 6 presents the results of endline membership regressions on baseline household characteristicsandtheirinteractionwiththePSP treatmentfollowingequation(4). Thetoppanelshows the results for regressions with village fixed effects that highlight within-village selection, while the results in the bottom panel combine both within- and across-village selection. Focusing on the top panel, the first row presents the estimates of the direct impact of the household characteristic (ηˆ ). It shows that in general, characteristics such as income, business income, positive 1 hours working in business, positive savings, and discount rates do not strongly predict membership. The second panel shows the differential selection within PSP treated villages (ηˆ ). Here 1 higher baseline incomes, higher baseline business incomes, spending time working in business, havingpositivelevelsofsavings,andhavinghigherhyperbolicdiscountfactors(i.e.,sufferingless fromhyperbolicdiscounting)wereallassociatedwithahigherprobabilityofSILCmembershipin PSPvillages. Theseimpactsarebothstatisticallyandeconomicallysignificant. Themeanimpacts on the probability of membership range from 0.02 (business income) and 0.20 (positive savings). Finally, our five measures are not independent, so the last column shows the results for the first principle component across all five measures. It is, again, strongly significant and quantitatively important. 34The one exception was the probability of a business failure. If business investments are risky as our theory assumes,thisisunderstandable,sincethePSPsaremakingmorebusinessinvestments. 24

Table6: EndlineMembershipSelectiononBaselineCharacteristics Income Business Positive PositiveHrs. LinearDisc. Hyperbolic 1stPrinc. Income Savings inBusiness Factor,β Disc. Factor,δ Comp. Characteristic -5e-05 -2e-05 -0.006 0.01 -0.12 -0.06 -0.01 s.e. (4e-05) (1e-04) (0.08) (0.06) (0.08) (0.04) (0.02) PSP*Characteristic 2e-04*** 3e-04* 0.23** 0.12* 0.07 0.17*** 0.10*** s.e. (6e-05)†† (2e-04) (0.09)† (0.07) (0.09) (0.06)† (0.03)†† VillageFE Yes Yes Yes Yes Yes Yes Yes PSP -0.08 -0.05 -0.30*** -0.11* -0.10** -0.08* -0.03 s.e. (0.05) (0.05) (0.10)†† (0.07) (0.05) (0.05) (0.05) Characteristic -8e-05* -6e-05 -0.17* 0.02 -0.16** -0.02 -0.02 s.e. (4e-05) (8e-05) (0.10) (0.06) (0.07) (0.06) (0.02) PSP*Characteristic 1e-04** 3e-04* 0.30*** 0.15** 0.11 0.09 0.09*** s.e. (6e-05) (2e-04) (0.10)†† (0.07) (0.08) (0.06) (0.03)†† VillageFE No No No No No No No Obs. 1877 1877 1877 1877 1877 1877 1877 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of household endline membership on on the stated baseline outcome,theirinteractioneffectswithaPSPdummy(therandomizedtreatment)andthefollowingcontrols: age,age squared, gender, numberofmen, womanandchildreninthehousehold, dummiesforschooling(i.e., someprimary, primarycompleted,secondary,andtertiarywithabaselineofnoschooling).Theregressionsareweightedbysampling weightsandarereportedbothwithandwithoutvillagefixedeffects. Afterweighting,thesampleisrepresentativeat thevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILCmembership.Standarderrors arerobustandclusteredbysubdistrict. Table 6 represents only a selection of the most salient results from our selection analysis. We conducted a wide variety of alternative specifications and included many different selection variables (i.e., Zbaseline) such as hours spent in agriculture or wage labor, presence and levels of j credit, levels of savings, business investment, expenditures, and consumption. We also ran separate regressions, replacing membership with dummies for leavers (baseline members but endline non-members)orjoiners(baselinenon-membersbutendlinemembers)separatelyandrunningregressions without fixed effects. Significance varied considerably across these different exercises, but both the significant results and the insignificant point estimates overwhelmingly support the story of the results presented in Table 6. The PSP groups appear more attractive to agents who are wealthier (i.e., who have higher consumption, higher savings and credit) and more businessoriented (i.e., who have fewer hours in wage labor and agriculture and more investment). Finally, we note that the fact that the results are equally strong when village fixed effects are included suggests that the selection we uncover is driven by patterns within the village, not differential 25

membershipratesacrossvillages. Nonetheless,weinvestigatealternativehypotheses. ThefirstalternativehypothesisisthatPSPs behave differently in either their targeting or their effort. The top panel of Table 7 shows no evidencethatPSPsbehavedifferentlyintargetingservicestovillagesclosertotheirhome(proximity), villages with which they have existing connections, or villages with greater perceived need (potentially driven by altruism) or demand (presumably driven by profit). In the bottom panel, we findnoevidenceofgreatereffortasmeasuredbydistancetraveledtoSILCsornumberofservices provided. Indeed,theonlysignificantestimatesinTable7showthatPSPsaremorelikelytowork only part-time, less likely to work more than part-time, and more likely to meet with their groups atleastbiweekly. Itisnonethelesspossiblethatunobservedeffortvariedacrossthetworegimes. Table7: ImpactofPSPTreatmentonAgentEffort/Behavior Targeting Proximity Connections Need Demand Other AllQuarters 0.02 -0.03 -0.04 -0.03 -0.01** s.e. (0.06) (0.05) (0.04) (0.04) (0.00) Quarters1&2 0.01 -0.04 0.01 0.02 -0.01 s.e. (0.05) (0.06) (0.05) (0.06) (0.01) Quarters3&4 0.03 -0.03 -0.10* -0.08 -0.01 s.e. (0.09) (0.07) (0.05) (0.07) (0.01) FAMean 0.32 0.54 0.84 0.30 0.01 Obs. 3816 3816 3816 3816 3816 Effort/WorkTime Average Average# Workl.t. WorkHalf Workg.t. WorkFull Biweekly Distance Services HalfTime Time HalfTime Time Meetings AllQuarters 0.43 -0.05 0.25*** -0.11 -0.17* 0.02 0.08** s.e. (0.63) (0.27) (0.08)†† (0.09) (0.09) (0.04) (0.04) Quarters1&2 -0.38 0.11 0.31*** -0.14 -0.24* 0.06 0.04 s.e. (0.67) (0.29) (0.10)†† (0.13) (0.12) (0.05) (0.06) Quarters3&4 2.3* -0.42 0.13* -0.04 -0.01 -0.08 0.13*** s.e. (1.2) (0.48) (0.07) (0.06) (0.11) (0.10) (0.05)† FAMean 4.5 2.8 0.04 0.21 0.68 0.06 0.41 Obs. 146 146 135 135 135 135 3792 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated agent-level outcome on a PSP (the randomized treatment) or PSP*Half dummy and the following controls: age, age squared, gender, number of languages spoken, numberofchildren,numberoffinancialdependents,dummiesforschooling(i.e.,primarycompleted,secondary,and tertiary with a baseline of less than primary complete), cohort, and location-date fixed effects. The regressions are weightedbycountry-specificsamplingweights. Standarderrorsarerobustandclusteredbysubdistrict. 26

The second alternative hypothesis is that the clients themselves put forth more effort. To evaluate this hypothesis, we can only focus on the total time spent working per week. While the composition of hours was impacted by the PSP program (recall Table 5), the overall total number ofhourswasnotsignificantlyaffected. Insum,wefindnoevidencethateithertheagentsormembersworkedharderinresponsetothe incentives of the PSP program, but we do find substantial evidence that the PSPs provide services toawealthier,morebusiness-orientedpopulation. 4 The Role of Membership Fees Given the evidence that membership selection is based on business-oriented characteristics, we developamodeltoprovideapotentialmechanism. Morespecifically,inSection3.1,wedevelopa stylizedmodelofacreditcooperativeoperatinginthefaceofadverseselectionwherelow-quality members can drive out high-quality members, lowering entrepreneurial activity (and aggregate output). Section 3.2 formulates the theoretical role of membership fees, showing that they can potentiallysolvethisadverseselectionandtherebyincreaseentrepreneurialactivity(andaggregate output).35 WethenempiricallytestthemodelpredictionsinSection3.3andwefindthatbothagent intermediation outcomes and household outcomes are strongly associated with fees, consistent withthetheory.36 4.1 Model We develop a one-period static equilibrium designed to capture a group cycle. In practice, groups generally continue beyond the cycle, but neither members nor groups need to commit to future participation.37 Since the outcomes of interest involve entrepreneurial activity–rather than consumption smoothing or risk-sharing, for example–we model agents with entrepreneurial projects 35Wepresenttheseresultsbutrelegatethetechnicalderivationsandproofstoouronlineappendix(seeSectionA.9). 36Thustheimpactofourmodelcreditcooperativeisrelatedtothechargingoffees.Asmokinggunempiricaltestof themodelwouldinvolverandomizingmembershipfees.Lackingsuchexogenousvariation-themodelwasdeveloped exposttounderstandtheimpacts. 37BondandRai(2009)showhowtherepeatedgamenatureoflendinggroupscangiveincentivesforfuturerepaymentinamodelwithstrategicrepayment. Weruleoutstrategicrepayment. 27

who, for simplicity and clarity, are risk neutral. In the data, we measured selection based on income, business activity, savings, and other measures of patience. In the model, we capture this using differences in average productivity and default. Although neither are directly observed in our data, higher productivity implies high average income and business income in the model, and the first principal component of our measures in the data is strongly negatively correlated with businessfailureandnegativeincomeshocks.38 4.1.1 Environment Consideraneconomywithtwostochasticprojecttechnologiesthatdifferintheirscaleandproductivity. The small-scale project requires one unit of capital, which it transforms, when successful, into A units of output. A large-scale project transforms k > 1 units of capital into Ak units of output. Thelarge-scaleprojectismoreproductiveinthatA > A. There is a unit measure of individuals, who are each endowed with one unit of capital for operating the technologies. All individuals have access to the small-scale project, but each person has access to the more productive large-scale project only with probability π. The individuals are divided into two types, i ∈ {L,H} that differ in their inherent probability of success. A fraction of individuals, θ , have a lower probability of success in production, p , while the remaining L L 1 − θ individuals succeed with probability p > p , where p p ∈ (0,1). We assume that L H L L, H θ p < (1−θ )p , so that the total number of potential successful type-H people exceeds the L L L H number of successful type-L people. When individuals fail, production yields zero output. In ordertoyieldinterestingresultsregardingadverseselection,wemakethestrongerassumptionthat p A > p A. That is, we assume the expected payoff of type-H individuals with the small-scale H L projectexceedsthatoftype-Lindividualswiththelarge-scaleproject. Since the large-scale project is more productive, but no individual is endowed with enough capital to operate it, there is potential demand for intermediation services. We model the timing andoperationofacreditandsavingscooperativeasfollows. Individualsdecidewhethertobecome members of a cooperative before finding out whether they have access to the large-scale technol- 38Themodelhasdirectimplicationsfordefaultratesandreturnsonsavingsaswell. Defaultratesarenotoriously difficulttomeasureempirically,butwedofindhigherprofitabilityamongthePSPgroups. 28

ogy. Members of a credit cooperative deposit their capital into the cooperative with a promised gross return of R . Individuals then find out whether they have access to the large-scale technol- D ogy,anddecideofwhethertoborrowatagrossinterestrateofR ,whichequatesdemandforloans B withavailabledeposits. Thecooperativeisabletoeffectivelydistinguishbetweenindividualsborrowing for large-scale production and those borrowing for small-scale production. The member’s type is unknown to the cooperative when it makes loan decisions, however, so that all borrowers pay the same borrowing rate. Unsuccessful members default on their loans and also forfeit their savings. Successful members repay their loans and then receive the return, R , on their savings, D whicheffectivelydissolvesthefund. Finally, consider that there is a minimum intermediation cost of C needed to remunerate the agentadministratingthecooperative,butweassumethatthiscostispaidbyanoutsideorganization untilSection3.2. 4.1.2 IndividualDecisions Individuals simply maximize their expected income. A member of the cooperative receives in expectation (cid:0) (cid:1) p Ak −R k +R (5) i B D ifsherunsalarge-scaleproject; p (A−R +R ) (6) i B D ifsherunsasmall-scaleproject;and R (7) D if she simply saves. An individual not in the cooperative can neither invest in the large-scale activitynorsave,soshesimplyearns p A i whichwerefertoasheroutsideoption. 29

4.1.3 Equilibrium Anequilibriummustsatisfythreeconditions: (1)individuals’choicesregardingjoiningthecooperative– whether and which project to undertake–must be optimal; (2) given R and R , the cooperative B D mustearnzeroprofits;and(3)themarketforfundsmustclear. Givenindividuals’optimizationandR ,thedemandforcredit(permember)isastepfunction, D involvingwillingness-to-paythresholdsthatcanbesolvedbyequatingthevalueofborrowingand investing(i.e.,(5)or(6)forthelarge-orsmall-scaleprojects,respectively)withthevalueofsimply saving (i.e., (7)) and solving for R .39 Type-H individuals with the large-scale opportunity have B the highest willingness to pay (R ) while type-L individuals financing the small-scale project BH havethelowestwillingnesstopay(R ). TheorderingoftheotherthresholdsdependsonR and BL D otherparametervalues. Wefocusontheinterestingcase,inwhichtype-Lindividualshaveahigher willingnesstopayeventhoughtheirexpectedpayoutislower(i.e.,p A > p A)becausethiscase H L can lead to adverse selection. This arises because Type-Ls fail more often, and so they have less to gain, but limited liability (from less than full collateral) can give them a higher willingness to pay. Moreover, to simplify the analysis without losing the interesting features of the equilibrium, we focus on instances when market clearing is simplified because the total demand for loans from thosewithlarge-scaleprojectsequalsthesupplyofsavings(πk → 1).40 Defining f as the fraction of members of the cooperative who are type L, we can derive a L break even condition for the cooperative showing that the borrowing rate must exceed the savings ratebecauseofincompleterepayment: φ(f )R = R . (8) L B D 39Theborrowingthresholdsfortype-iindividualsforthelarge-andsmall-scaleproject,respectively,are (cid:18) (cid:19) 1−p R = A− i R Bi p k D i (cid:18) (cid:19) 1−p R = A− i R Bi p D i 40Formally,wemakethefollowingparameterassumption: πk =1+ε. whereepsilonisanarbitrarilysmall,positivenumber,andweanalyzethemodelundertheconditionslim πk+ε ε→0+ andlim πk+ε. ε→0− 30

where φ(f ) ≡ pavg(fL) < 1 is the effective repayment rate given the partial collateral of L πpavg(fL)+(1−π) savings. Notethatφisincreasinginf ,sinceType-Lsfail,andtherefore,defaultmoreoften. L We define B(f ;p˜) as the type-i individual’s net benefit of joining the cooperative–i.e., the L i difference between the expected incomes of members and nonmembers in the cooperative. Given oursimplifications,wecaneasilyderive (cid:2)(cid:2) (cid:3) (cid:3) B(f ;p˜) = πp˜ A−R (f ) k +R (f ) +(1−π)R (f )−p˜A L i i BL L DL L DL L i (cid:0) (cid:1) = p˜ A−A +[(1−π +πp˜)φ−p˜]R (f ), i i i BL L wherep˜ indicatesthesuccessprobabilityoftheparticularindividual(seeSectionA.9intheonline i appendix). Therearetwoforcesatworkinthisequation. Oneforce,clearlyseeninthefirstterm,is the fact that the cooperative allows the more productive large-scale projects to be financed, which isalwaysanadvantageandbecomeslargerastheindividual’sprobabilityofsuccessincreases. The second term captures the compositional force, which depends on the average success rate in the cooperative compared to the individual’s own success rate. The smaller the average success rate, the larger the wedge between borrowing and savings rates. For type-H individuals, this force is (weakly)negative,whilefortype-Lindividualsitis(weakly)positive. ExaminationofB(f ;p˜)leadstothemajorresultsformalizedinthefollowingproposition. L i Proposition1 Giventheassumptionsabove, (i)Type-Lindividualsalwaysjoin,B(f ;p˜ ) > 0. L L (ii)Intermediatevaluesofπ existatwhichtype-H individualswon’tjoinacooperativeofalltype- L members, B(1;p˜ ) < 0, although they benefit more than type-L do from joining a cooperative H ofalltype-H members,B(0;p˜ ) > B(0;p˜ ). H L ProofofthepropositionisstraightforwardandgiveninSectionA.9intheonlineappendix,but we offer some simple intuition here. Type-L individuals can only do better by joining, since both of the above-mentioned forces are positive for them. A poor composition lowers the benefits of joiningbecausehigherdefaultrateslowerthesavingsraterelativetotheborrowingrate(i.e.,lower φ). This wedge matters more for type-H, however, since borrowers only pay the borrowing rate and earn the savings rate when successful, and they succeed more often. Moreover, the type-H 31

individuals have a higher outside option, so they benefit less from joining a cooperative with poor composition. Finally, when the composition is good, type-H individuals can have more to gain from financing large projects, since they succeed more often and earn a premium over the deposit rate.41 The left panel of Figure 1 shows these results graphically for an intermediate value of π ∈ (π,π). In such a case, although type-L individuals always join, type-H join only if type-L are ˆ ˆ less than some f , defined by the root B(f ;p˜ ) = 0. If the proportion of type-L individuals in L L H ˆ the population is high enough, θ > f , then type-H individuals never join and the equilibrium L (denotedfE)isfE = 1. Thatis,alltype-Ljoin,butnotype-H do.42 L L Figure1: BenefitsofJoiningvs. FractionType-L 4.2 Theoretical Results on Membership Fees Now consider the possibility of recouping the intermediation cost, C, by introducing a flat membership fee F > 0. We show how this could actually increase total output and the surplus of 41Ifπ istoohigh,type-H willalwaysjoin. Ifitistoolow,theirbenefitsofjoiningwillnotexceedType-L’s. The requirementforintermediatevaluesofπ underscoresthefactthattheresultsrelyonindividual’shavinguncertainty overbeinganetborrowerornetsaver. Ifthetimingweresuchthatindividualsknewwhethertheyhadalarge-scale projectbeforejoining,thentype-H individualswiththelarge-scaleprojectwouldalwaysjoin. 42If θ < fˆ , multiple equilibria exist: two stable equilibria at either f = 1 or f = θ, and an equilibrium, L L L f =fˆ , thatisunstabletoperturbationsaroundf . Ofcourse,inallcasestherearealsoadditionaltrivialequilibria L L L wherenoonejoins. 32

members.43 In the left panel of Figure 1, the benefit at lower levels of f is higher for type-H individuals. L Theythereforehaveahigherwillingnesstopayformembershipinacooperativewithlowerlevels oftype-H members. Amembershipfeehasthepotentialofdrivingouttype-Lindividuals,thereby ˜ inducing type-H individuals to join. Define B(f ;p˜) = B(f ;p˜)−F. The membership fee, F, L i L i ˜ ˜ can ensure that the intersection of B(f ;p˜ ) = B(f ;p˜ ) is less than zero. If the relative benefits L H L L of type-H are high enough, this can actually increase average income even net of payments. In such a case, illustrated in the right panel of Figure 1, the unique equilibrium value of fE is at the L pointwheretype-Lindividualsareindifferent,B ˜ (f ;p˜ ) = 0.44 L L We summarize this in the following proposition, and we give the details of parameter value requirementsinSectionA.9oftheonlineappendix. Proposition2 There exist values of π, θ, and p satisfying Proposition 1 such that a membership L fee, F, that induces some (or even all) type-L members not to join the cooperative will induce type-H memberstojoinandincreasethetotalincomeintheeconomynetoffees. Of course, if C is too large (that is, if it exceeds the potential benefits of type-H members, (1−θ )B(0;p˜ )),requiringthecooperativetorecoupcoststhroughaflatmembershipfeewould L H makethecooperativefinanciallyunsustainable. Consider now the optimal policy, in the sense of maximizing total output. Total output is increasinginthenumberofindividualswhofinancethelarge-scaleproject,buttheaverageoutput ˜ gain is larger for type-H individuals. The optimal single fee sets the intersection of B(f ;p˜ ) = L H ˜ B(f ;p˜ )inFigure1justbelowzerobecauseitmaximizesthenumberoftype-Lwhoenter,while L L alsoensuringthatalltype-H enter. Thisfeeleavesthememberswithnosurplus,however. 43Wedonotincludethecost,C,inthecapitalresourceconstraintofthemodelinordertomaintainthesimplicity ofourstylizedassumptionthatπk−εequalstheamountofdepositsavailableforloans. Onecouldmotivatetheseby anadditionalstylizedassumption: introduceaninitialendowmentofD > C output. Weneedtofurtherassumethat itcannotbeusedforinvestment,norisitstorableacrosstheperiodofthemodel. Otherwise,thefundcoulddemand thisascollateral. Westressthatentrycostsdifferfromcollateralintwoimportantways: (1)collateraliskeptbythe borrowerinthecaseofrepayment,and(2)forsmallπ,entrycostsarelessthanfullcollateral. 44Since total output is increasing in the number of agents who finance the large-scale project, the single fee that maximizestotaloutputsetstheB˜(f ;p˜ ) = B˜(f ;p˜ )justbelowzero. Thismaximizesthenumberoftype-Lwho L H L L enter,whileensuringthatalltype-H enter. Thisleavesthememberswithnosurplus,however. Sincetype-Lmembers willneverearnanysurpluswiththemembershipfee,thesinglefeethatmaximizestotalsurplustomembersistheone thatmakestype-Lmembersindifferentatf =0. L 33

Alternatively,wecansolvefortheequilibriumthatmaximizestotalsurplus. Undertheassumption that θ < pH , type-H members joining adds more to the surplus than type-L members L pL+pH joining. Inthiscase,thefeethatmaximizestotalsurplustomembersistheonethatmaximizesthe surplusoftype-H members. Thisisthelowestfeethatkeepstype-Lmembersout;thatis,itsolves B ˜ (0;p˜ ) = 0. Call this F∗. The loss of type-L members does not lower the surplus because for L anymembershipfeeequilibriuminwhichtype-H join,thesurplusoftype-Lmembersiszero. Finally,considermoreflexiblecontractsthatcanachievethefirst-bestinthesenseofmaximizingtotaloutputbyhavingeveryonejointhecooperative. Acooperativecouldeffectivelyscreenby offering two different contracts, {F,φ}, which have the flavor of two-part tariffs. The cooperative can attract both types by offering a large F together with a large φ, which is attractive to type-H, andasmallF togetherwithasmallφ,whichisattractivetotype-L.45 Naturally,theoutput(netof fees)wouldbemaximizedsinceallindividualswouldbeinthecooperative. A similar equilibrium, where total output is maximized and everyone joins the cooperative, could also be achieved by starting two different cooperatives with different membership fees. The contracts that maximize the member surplus in the cooperative attracting type-H members would charge F = F∗ (and have φ(0) as an equilibrium, break-even value), and the contract maximizing member surplus in the cooperative attracting type-L would have F = 0 (and have φ(1) as an equilibrium,break-evenvalue). Denoteoutput(netoffees)underthisequilibriumwithtwodifferentcooperativesasY∗,output 2 (net of fees) under the single F∗ fee equilibrium as Y∗, and output under no fees as Y∗; the 1 0 followingpropositionsummarizeshowthebenefitsoftheprogramvarywithfeestructureinthese threeexamples. Proposition3 For values of π and θ satisfying Proposition 2, the maximum output under two fees exceeds that under the single fee, F∗. Likewise, the maximum output under a single fee, F∗, exceedsthatundernofee(Y∗ > Y∗ > Y∗). 2 1 0 Propositions2and3motivateasimpletestinSection3.3. 45Therearemanysuchcontractsthatwouldaccomplishthis.ThereisalsothepossibilityofadjustingR awayfrom B (cid:2) (cid:3) (cid:2) (cid:3) R ,whichwehavefocusedon. Inparticular,anyR ∈ R ,R forthefirstcontractandR ∈ R ,R BL B BH BH B BL BL forthesecondwouldaccomplishthis. Sinceindividualsareriskneutral,thisonlyaffectsexpostinequality,nottheir exantevaluation. 34

Finally, we note that while the varying membership fees could potentially increase the total surplus of individuals, by including both types, the true social surplus would be net of the cost of financial intermediation, C. For a very high C that exceeds the benefit of serving the type-H population, (1−θ )p (A−A), social surplus is maximized with no cooperatives and no mem- L H bers. For a very low intermediation cost, C, that is less than the benefits of serving the type-L population, θ p (A−A), social surplus is maximized with two cooperatives and everyone served. L L For intermediate values of C, social surplus is maximized with only one cooperative serving the type-H individuals. One might thus interpret the model as illustrating a rationale for potentially excluding the poorest of the poor from microfinance: The benefits of their receiving microfinance do not exceed the costs, and their participation may actually drive out potential recipients who would benefit more. 4.3 Empirical Evidence on Membership Fees The model suggests a strong role for membership fees in leading to the relative impacts of PSPs. Inthissection,weexaminethisempiricallybyfocusingdirectlyonthesefees. Our agent-level data contains information on PSP payments by the groups themselves. Althoughthesepaymentsarenotrandomizedandsoarepotentiallyendogenous,ourmodelsuggests that variation could be driven by differences in intermediation costs (C) across villages which could reflect actual time and labor costs or the time and labor costs net of any altruistic motive (e.g.,family,friends). Variationineithercouldplausiblybeexogenous. We document substantial fee variation across groups.46 The quarterly per-group fee is $5.80, onaverage;thestandarddeviationis4.60;andtheinterquartileratiois3.1. Moreover,wefindthat 56percentoffeevariationoccursacrossvillages,withjustunderhalf(44percent)occurringwithin villages. Groupswithinthesamevillagecanbechargeddifferentfees,eitherbyasinglePSPorby differentPSPs. PSP-specificfixedeffectsexplainlessthan40percentofvariation,however. Thus, thedataindicateahighdegreeofpricetargetingwithinandacrossvillagesandbyindividualPSPs. 46Tomatchthetimingofthehouseholddata,weuseonlythosegroupsthatchargedfeesinthefourthquarterofthe randomization,andwetrimthelowerandupper5percentofoutliers. 35

We perform two analyses to test the role of membership fees. First, we evaluate the extent to which financial intermediation in the agent data is associated with the charging of fees. Second, weexaminewhetherthehouseholdoutcomesaredrivenbythefeestructureofvillages. 4.3.1 AgentOutcomes Themodelhaspredictionsforeconomiesofhouseholds,whichweinterpretasvillages. Topursue theanalysisfurther,wethereforeaggregatetheagent-leveldatabyvillageanddistinguishbetween villages where no fees are charged (413 villages), villages where a single uniform fee is charged (367villages),andvillageswithvariablefees–i.e.,differentgroupsarechargeddifferentfees(424 villages). Werunregressionsoftheform Y = α +γwave +(cid:36) NoFeePSP vdt dt d 1 v +(cid:36) UniformPSP +(cid:36) VariablePSP +ε (9) 2 v 3 v itdn, where Y are the same MIS outcomes (total members, total groups, savings, number of loans, vdt value of loans, profits, and agent pay) aggregated by village, v. First, we run this regression using the per-group averages. The role of fees in the theory suggests that for the per-group averages, both (cid:36) and (cid:36) should be bigger than (cid:36) . That is, fees should enable higher levels of services, 2 3 1 exceptperhapsformembership. RecallthatthesecoefficientsareallrelativetotheFAvillages. TheresultsareshowninTable8. Theyshowhowthetypicalgroupvariesbythefeeschargedin the village. Except for loans, the positive significant estimates are all concentrated on the villages that charge fees, especially those with variable fees. Thus, fees seem to be closely related to the level of services that individual groups provide. Villages with uniform fees have significantly higher membership, and those with variable fees have significantly higher credit, membership, savings, and profits. The groups in PSP villages where no fees are charged are not statistically distinguishable from groups in FA villages. These PSP villages may be a combination of villages where PSPs offer free services out of social connections or altruism and villages in which PSPs anticipate introducing fees at a later date. Altruism would be an exogenous source of variation in the context of the model, while delayed fees might be potentially endogenous if correlated with willingnesstopay,forexample. 36

Table8: Effectof“VillageType”onPer-GroupOutcomes Members Savings Loans LoanValue Profit Obs. NoFee -0.71 26 0.70 19 22 413 s.e. (0.63) (45) (1.3) (35) (16) UniformFee 1.6** 26 0.26 44 14 367 s.e. (0.69) (33) (1.1) (31) (8.3) VariableFee 1.6** 110** 3.3 100** 20* 424 s.e. (0.74) (55) (2.0) (46) (10) FAMean 21 250 8.0 200 50 Obs. 1760 1760 1760 1760 1760 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Theresultsareestimatedcoefficientsforaregressionofthestatedoutcome(aggregatedfromtheMISgroup-leveldata tothevillagelevelanddividedbythenumberofgroupsoperatinginthevillage)onavillagetypedummy,locationdatefixedeffects,andthecohortoftheagentworkinginthatvillage. Theomittedvillagetypeisvillageservedbyan FA.Theregressionsareweightedbysamplingweights. Standarderrorsarerobustandclusteredbysubdistrict. Second, we run regression (9) using the aggregate village totals. The theory suggests that the ability to vary fees should allow for more intermediation through a greater number of groups. Thus, (cid:36) should exceed (cid:36) , even for membership. Again, these coefficients are all relative to the 3 2 FAvillages. Table9: Effectof“VillageType”onTotalOutcomes Groups Members Savings Loans LoanValue Profit Obs. NoFee -0.43** -9.1** 77 -1.3 18 64 413 s.e. (0.19) (4.2) (140) (4.2) (110) (55) UniformFee -1.1*** -20*** -200** -8.8*** -200** -45** 367 s.e. (0.14)††† (3.4)††† (88) (3.3)†† (80)† (19) VariableFee 2.0*** 46*** 1020*** 33*** 960*** 180*** 424 s.e. (0.23)††† (5.2)††† (210)††† (7.4)††† (180)††† (35)††† FAMean 2.4 51 610 21 530 120 Obs. 1760 1760 1760 1760 1760 1760 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated outcome (aggregated from the MIS group-level datatothevillagelevel)onavillagetypedummy,location-datefixedeffects,andthecohortoftheagentworkingin thatvillage. TheomittedvillagetypeisvillageservedbyanFA.Theregressionsareweightedbysamplingweights. Standarderrorsarerobustandclusteredbysubdistrict. Table9presentstheresultsandhighlightstheroleofvariablefees. Here,thepositiveestimates are almost exclusively in the villages where variable fees are charged. Indeed, uniform fees are associated with fewer groups, members, and services than in FA villages, but variable fees are 37

associated with more groups, members, savings, loans, credit, and profits. This is consistent with thetheorythatvariablefeescancatertolargerpopulationsthanuniformfees,yieldinghigherlevels ofintermediationandlargertotalimpacts(recallProposition3). 4.3.2 HouseholdOutcomes Next, we examine whether the fee structure of villages appears to be related to household outcomes. Recall that we have household data for only a small subset of villages. Among these, only two villages charge a single uniform fee, so we cannot divide the sample into three groups. Instead, we simply distinguish between PSP villages where fees are charged (952 villages) and PSP villageswherenofeesarecharged(318villages). We first examine whether the charging of fees is related to underlying baseline characteristics byrunningregressionsoftheform Y = α +X β +δPSP +ε jdn0 d j fee jdn where the baseline (time=0) outcome for household j (living in district d and subdistrict n), Y jdn0 depends on a district-specific fixed effect, and the characteristics of the household, X (gender; j age and age-squared; schooling dummies; and the number of adult men, women, and children in the household). PSP is a dummy for PSP villages where a fee is charged. The coefficient δ is fee relative to those PSP villages where no fees are charged. We add the district-specific fixed effects to control for any regional heterogeneity, since our fee analysis cannot fall back on randomization forexogeneity. Usingtheaboveequation,weexamine27differentoutcomes.47 Forthevastmajorityofthese, wefindthatthePSPvillagesarestatisticallyindistinguishablefromthebaseline,withtheexception that villages where fees are charged significantly have higher savings from business profit, have morecreditfromSILCandinformalsources,andspendmorehoursinbusinessesthanFAvillages in the baseline. Our household results nevertheless control for any baseline differences, but we interpretourresultsasevidencethatfeevariationisreasonablyexogenous. 47TheresultsarereportedinTablesA.9,A.10,andA.11inSectionA.6oftheonlineappendix. 38

WethenexaminehowtheendlineresultsinTables4and5areconcentratedamongthedifferent feevillages. Werunregressionsthataccountforanybaselinedifferencesandtaketheform Y = α +X β +Y +δ PSP +δ PSP +ε jdn1 d j jdn0 1 nofee 2 fee jdn The endline outcomes Y (for household j living in district d and subdistrict n), depend on a jdn1 district-specific fixed effect; the baseline outcome, Y ; and the characteristics of the household, jdn0 X (gender; age and age-squared; schooling dummies; and the number of adult men, women, and j children in the household). PSP is a dummy for PSP villages where no fee is charged, and nofee PSP is a dummy for PSP villages where a fee is charged. The coefficients δ and δ are all fee 1 2 relativetotheFAvillages. The results are reported in Tables 10 and 11, which are exact analogs to Tables 4 and 5. We find that the overall positive results from the PSP are driven by the PSP villages where groups are charged a fee. For example, in Table 10, villages with fees use more savings for existing business,havemorecreditgoingtobusinessowners,obtainmorecreditfromSILCs,andusemore credit for agricultural activities and expanding existing business. The results in Table 11 are a bit more mixed, however. We find a more statistically significant increase in business investment in PSP villages with fees, but the point estimate is actually smaller. We find fewer hours spent in agriculture. However, we find lower rates of business closures in villages without fees, and more hoursspentasemployees.48 To summarize, we find that the relative gains in intermediation and household outcomes that we measure for PSPs generally appear to be linked to the charging of fees, though not in every analysis. Although fees (rather than other aspects of PSP behavior) seem to be closely related to impacts, the high level of variability in fees suggest that it might be difficult to replicate the results of the privatization scheme by using a centrally mandated uniform fee, for example. A randomizationonthefeesthemselveswouldaddgreaterinsightintothesequestions,however. 48Though not reported in the tables, we actually find a marginally significant positive impact in total household consumption in villages where fees are charged. We also note, however, that selection itself seems to occur in PSP villages regardless of whether fees are charged. Indeed, the differences between the fee and no-fee villages are not statisticallysignificant. Thisis,admittedly,puzzlingevidenceforourfeeinterpretation. 39

Table10: PSPImpactonEndlineHouseholdSavingsandCreditbyVillageType Source Purpose PANELI:Savings Total Business Business SellAgric. Salaryor NewAgric. NewNon-Agric. Existing Owners Profit Product Wage Activity Activity Business NoFeePSP 29 -1.8 8.8 -11 14 -0.44 1.0 6.9 s.e. (18) (32) (7.0) (12) (9.3) (15) (3.3) (4.3) FeePSP -10 -25 12* -3.2 3.4 -9.7 -3.6 15*** s.e. (14) (17) (6.3) (9.1) (4.4) (11) (2.9) (5.3)†† PANELII:Credit Total Business SILC Formal Informal Agric. Expanding StartNew Owners Activity Business Business NoFeePSP 16 0.72 3.8 2.2 9.9 -0.83 7.0 6.1 s.e. (19) (26) (2.9) (15) (7.5) (4.3) (7.5) (4.0) FeePSP 15 21** 6.0*** 4.1 5.8* 4.9* 6.2** 0.87 s.e. (11) (10) (2.3)† (9.1) (3.1) (2.9) (3.1) (1.4) Obs. 1731 779 1731 1731 1731 1731 1731 1731 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Theresultsareestimated“intenttotreat”coefficientsforaregressionofthestatedoutcomeontwodummyvariables: PSPhouseholdswithnofeechargedandPSPhouseholdswitheitherauniformorvariablefeecharged,thebaseline outcomeandthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildreninthehousehold, dummiesforschooling(i.e.,someprimary,primarycompleted,secondary,andtertiarywithabaselineofnoschooling). Theregressionsareweightedbysamplingweights. Afterweighting,thesampleisrepresentativeatthevillage level,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILCmembership. Standarderrorsarerobust andclusteredbysubdistrict. Allregressionsincludecountryanddistrictfixedeffects. Table11: PSPImpactonEndlineHouseholdProductiveDecisions StartNew Closed Business Hoursspent Employees Hoursspent Agric. Hoursspent Business Business Investment inBusiness (non-HH) asEmployee Investment inAgric. NoFeePSP -0.03 -0.25*** 26* 2.9 0.15 3.8** -8.6 -3.4** s.e. (0.06) (0.10)† (14) (1.9) (0.11) (1.6) (11) (1.6) FeePSP 0.06 -0.09 14** 1.8 0.09 1.4 1.2 -5.5*** s.e. (0.07) (0.07) (6.4) (1.7) (0.07) (1.2) (10) (1.7)††† Obs. 1731 779 1731 1731 1731 1731 1731 1731 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Theresultsareestimated“intenttotreat”coefficientsforaregressionofthestatedoutcomeontwodummyvariables: PSPhouseholdswithnofeechargedandPSPhouseholdswitheitherauniformorvariablefeecharged,thebaseline outcomeandthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildreninthehousehold, dummiesforschooling(i.e.,someprimary,primarycompleted,secondary,andtertiarywithabaselineofnoschooling). Theregressionsareweightedbysamplingweights. Afterweighting,thesampleisrepresentativeatthevillage level,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILCmembership. Standarderrorsarerobust andclusteredbysubdistrict. Allregressionsincludecountryanddistrictfixedeffects. 40

5 Conclusion We have presented evidence from a randomized trial of an innovation for privatized entrepreneurs whoearnremunerationbychargingfeesformembershiptotheirclients. Thesomewhatsurprising empirical results indicate that through this cost-saving innovation, these microfinance services can indeed be “self-help” in the sense that, after initial training, the group administration can be financed through client-based fees. Relative to the continuously NGO-subsidized model, the private entrepreneurs expanded services more slowly but ultimately reached similar numbers of people and provide similar levels of services. The privately provided groups also had relatively stronger impacts in terms of the narrative microfinance dimensions of business entrepreneurship andinvestment. As an example of a successful cost-recovery innovation–successful in terms of its intended goalofenablingNGOresourcestostretchfurther,reachinggreaternumbersofpeople–thereasons for success are important for current and future microfinance programs. It does not appear that it was driven by the increased effort from improved incentives toward agents or members putting forth greater effort. Instead, it appears to be driven by privatized entrepreneurs catering to a more business-oriented population, who are willing to pay fees. We have developed a theory of the role of fees in mitigating adverse selection into credit cooperatives. Consistent with the theory, membershipfeesseemtobetightlylinkedtoimpact. On the pro-side, this may target the services toward those who most benefit from them, and, indeed,bettertargetingmayhelpimprovethefunctioningofthegroups. Ontheotherhand,though, aidprogramsmaystillbeinterestedinreachingthosewithalowerwillingnesstopay,whomaybe the truly poorest. Such tradeoffs may be more broadly important in moves toward sustainability or privatization. The distribution of benefits across the population and subpopulations is therefore an ongoing project of further investigation. A larger question is whether it is advisable to provide microfinance services to all populations. PSPs might improve welfare by limiting credit access to hyperbolic discounters, for example. Conversely, targeting populations that are more businessorientedmayberiskier,potentiallyleadingtofuturemicrofinanceruns(BondandRai,2009). Another remaining question is whether privatization matters beyond the incentives to charge 41

fees that it provides. If not, as the theory suggests, the favorable outcome and reduced costs could be attained by NGOs simply charging membership fees without privatizing. If the incentives do matter, then heterogeneous responses of PSPs to these incentives may provide insights. Unfortunately, our current data do not offer exogenous variation in payments or PSP behavior to further evaluatetheseissues. Experimentalevidenceonfeesisanareaforfurtherresearch,asisexamining thegeneralityoftheseresultsfortheprovisionofotherfinancialservicestothepoor. References AHLIN, C. AND N. JIANG (2008): “CanMicro-CreditBringDevelopment?” JournalofDevelopmentEconomics,86,1–21. AHLIN, C. AND R. M. TOWNSEND (2007): “Using Repayment Data to Test Across Models of JointLiabilityLending,”EconomicJournal,117,F11–51. ATTANASIO, O., B. AUGSBURG, R. DE HAAS, E. FITZSIMONS, AND H. HARMGART (2011): “Group Lending or Individual Lending? Evidence from a Randomised Field Experiment in Mongolia,”WorkingPapers136,EuropeanBankforReconstructionandDevelopment. BANERJEE, A. V., T. J. BESLEY, AND T. W. GUINNANE (1994): “Thy Neighbor’s Keeper: The Design of a Credit Cooperative with Theory and a Test,” Quarterly Journal of Economics, 109, 491–515. BANERJEE, A. V., D. KARLAN, AND J. ZINMAN (2015): “Six Randomized Evaluations of Microcredit: IntroductionandFurtherSteps,”AmericanEconomicJournal: AppliedEconomics,7, 1–21. BOND, P. AND A. S. RAI (2009): “Borrowerruns,”JournalofDevelopmentEconomics,88,185– 191. BUERA, F. J., J. P. KABOSKI, AND Y. SHIN (2012): “The Macroeconomics of Microfinance.” Tech.rep.,NationalBureauofEconomicResearch. 42

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Appendix For Online Publication This is an online appendix of additional empirical results, robustness tests, and mathematical proofs for the paper, “Can Self-Help Groups Really Be Self-Help?” by Greaney, Kaboski, and Van Leemput. We have organized the results into the following sections: A.1) summary statistics bymember/non-memberofSILC,A.2)sampleregressions,A.3)additionalrandomizationresults, A.4)group-levelresults,A.5)additionalhouseholdresults,A.6)baselinerandomizationacrossfee vs. no fee, A.7) endline results for different PSP villages, A.8) additional robustness results, A.9) themathematicalappendixforthemodel,andA.10)datadescription. A.1 Summary Statistics by Member/Non-Member Table1: SummaryStatisticsSILCversusnonSILC SILC Non-SILC SILC-Non-SILC Mean Std. Dev. Mean Std. Dev. Mean(cid:52) Savings 153 371 131 263 24 Credit 48 165 45 236 1.2 Income 289 485 356 665 -68* Consumption 1429 1516 1428 1538 1.2 BusinessOwner 0.55 0.50 0.36 0.48 0.19***††† NoSchooling 0.22 0.41 0.21 0.41 0.01 SomePrimary 0.26 0.44 0.22 0.41 0.04* PrimaryCompleted 0.40 0.49 0.44 0.50 -0.04 Secondary 0.11 0.32 0.10 0.31 0.01 Tertiary 0.02 0.13 0.03 0.16 -0.01 Obs. 968 951 ***,and**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and †indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. ThetablepresentsbaselinemeancomparisonresultsforhouseholdswithSILCmembersandhouseholdswithoutSILC members. Allresultsutilizesamplingweights. 1

A.2 Sample Regressions Table2: SampleAgent-LevelRegression Earnings PSP*Quarter1 -160*** s.e. (5.2)††† PSP*Quarter2 -150*** s.e. (6.4)††† PSP*Quarter3 -140*** s.e. (6.3)††† PSP*Quarter4 -150*** s.e. (4.9)††† Age 0.56 s.e. (1.7) AgeSquared -0.00 s.e. (0.02) Gender -1.4 s.e. (4.1) PrimaryComplete 7.9 s.e. (9.9) Secondary 14 s.e. (11) Tertiary 9.8 s.e. (12) Languages -1.3 s.e. (3.8) Children -0.04 s.e. (0.69) FinancialDependents -0.23 s.e. (0.37) Cohort -3.9 s.e. (12) Obs. 865 RSquared 0.88 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated group-level outcome on a PSP*Quarter dummy and the following controls: age, age squared, gender, number of languages spoken, number of children, number of financialdependents,dummiesforschooling(i.e.,primarycompleted,secondary,andtertiarywithabaselineofless than primary complete), cohort, and location-date fixed effects. The regression is weighted by sampling weights. Standarderrorsarerobustandclusteredbysubdistrict. 2

Table3: SampleGroup-LevelRegression Profit PSP*Quarter1 8.3 s.e. (9.9) PSP*Quarter2 -13 s.e. (12) PSP*Quarter3 2.3 s.e. (10) PSP*Quarter4 22** s.e. (11) Age 4.7** s.e. (2.3) AgeSquared -0.05* s.e. (0.03) Gender 5.2 s.e. (8.2) PrimaryComplete 13 s.e. (11) Secondary 15 s.e. (12) Tertiary 35** s.e. (16) Languages 2.7 s.e. (6.0) Children -4.0** s.e. (1.9) FinancialDependents 1.8 s.e. (1.3) Cohort 3.9 s.e. (10) Obs. 15,747 RSquared 0.03 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively.†††,††,and†indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively.The resultsareestimatedcoefficientsforaregressionofthestatedoutcomeonaPSP*Quarterdummyandthefollowing controls: age,agesquared,gender,numberoflanguagesspoken,numberofchildren,numberoffinancialdependents, dummiesforschooling(i.e.,primarycompleted,secondary,andtertiarywithabaselineoflessthanprimarycomplete), cohort,andlocation-datefixedeffects. Theregressionsareweightedbysamplingweights. Standarderrorsarerobust andclusteredbysubdistrict. 3

Table4: ExampleofaHousehold-LevelRegression TotalCredit PSP 27** s.e. (11) TotalCreditBaseline 0.15* s.e. (0.08) Age 6.0** s.e. (2.3)† AgeSquared -0.06** s.e. (0.02) Gender -4.2 s.e. (13) SomePrimary 43** s.e. (19) PrimaryComplete 5.9 s.e. (8.5) Secondary 129*** s.e. (40)†† Tertiary 218** s.e. (88) #AdultMales -4.6 s.e. (4.3) #AdultFemales 20*** s.e. (7.5)† #Children -1.4 s.e. (2.8) Obs. 1891 RSquared 0.10 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e.,someprimary,primarycompleted,secondary,and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sampleisrepresentativeatthevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILC membership. Standarderrorsarerobustandclusteredbysubdistrict. 4

A.3 Additional Randomization Results Table5: KeyInformantMeanComparisons PSP FA PSP-FA Mean Std. Dev. Obs. Mean Std. Dev. Obs. Mean(cid:52) Population 1292 1466 139 1120 1166 55 171 PowerGrid 0.27 0.44 139 0.22 0.42 55 0.04 MonthsInaccessible 2.8 3.8 139 2.6 2.9 55 0.22 BankDistance 27 28 139 23 17 55 3.5 Primary 0.74 0.44 139 0.65 0.48 55 0.09 Secondary 0.36 0.48 138 0.34 0.48 55 0.02 PostSecondary 0.06 0.24 136 0.07 0.25 54 -0.01 Hospital 0.43 0.50 137 0.44 0.50 55 -0.01 Factory 0.06 0.23 137 0.05 0.23 53 .0004 MFI 0.14 0.35 136 0.23 0.43 52 -0.09 Bank 0.02 0.15 137 0.02 0.14 54 0.003 ROSCA 0.76 0.43 132 0.65 0.48 52 0.11 ASCA 0.66 0.48 123 0.61 0.49 49 0.05 SACCO 0.16 0.37 138 0.11 0.32 55 0.05 FSA 0.05 0.23 122 0.06 0.23 51 -0.004 MobileMoney 0.12 0.33 137 0.10 0.31 55 0.02 Moneylender 0.19 0.39 132 0.15 0.36 54 0.04 Drought 0.58 0.35 121 0.61 0.38 51 -0.03 Flood 0.49 0.35 92 0.55 0.38 36 -0.06 CropFailure 0.51 0.34 88 0.52 0.39 37 -0.01 AnimalDisease 0.41 0.32 68 0.21 0.24 30 0.20*** Bandits 0.29 0.31 36 0.19 0.24 20 0.10 Violence 0.77 0.32 12 0.67 0.45 6 0.10 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. Table6: RandomizationResultsExcludingMombassaandTahea Age Gender Primary Primary Secondary Tertiary Languages Children Financial Complete Dependents PSP -1.7 -0.11 0.01 -0.09 0.05 0.03 0.02 -0.48 -0.26 s.e. (1.3) (0.08) (0.01) (0.05) (0.08) (0.07) (0.09) (0.44) (0.71) FAMean 35 0.72 0.00 0.32 0.55 0.13 2.0 4.6 6.2 Obs. 182 185 184 184 184 184 185 185 184 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated outcome on a PSP dummy and the following controls: age, age squared, gender, dummies for schooling (i.e., primary completed, secondary, and tertiary with a baseline of less than primary complete), number of languages spoken, number of children, number of financial dependents,cohort,andlocationfixedeffects. Theregressionsareweightedbysamplingweights. Standarderrorsare robustandclusteredbysubdistrict. 5

A.4 Group-Level Results Table7: PSPImpactsonGroup-LevelOutcomes Members Savings Loans LoanValue Profit Payment AllQuarters 0.26 46 0.57 19 5.5 -4.4*** s.e. (0.59) (50) (1.0) (25) (9.0) (0.89)††† Quarter1 0.22 21 -1.7 -12 8.3 -9.3*** s.e. (0.62) (58) (1.3) (31) (9.9) (0.63)††† Quarter2 0.06 16 0.53 -0.07 -13 -6.7*** s.e. (0.59) (53) (1.1) (24) (112) (0.80)††† Quarter3 0.33 39 1.3 17 2.3 -3.5*** s.e. (0.64) (53) (1.3) (29) (10) (1.0)††† Quarter4 0.37 96* 1.5 58* 22** -0.77 s.e. (0.63) (51) (1.4) (33) (11) (2.0) FAMean 21 240 9.9 230 53 9.5 Obs. 16,289 15,747 15,747 15,747 15,747 14,907 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. TheresultsareestimatedcoefficientsforaregressionofthestatedoutcomeonaPSPorPSP*Quarterdummyandthe followingcontrols: age, agesquared, gender, numberoflanguagesspoken, numberofchildren, numberoffinancial dependents,dummiesforschooling(i.e.,primarycompleted,secondary,andtertiarywithabaselineoflessthanprimarycomplete),cohort,andlocation-datefixedeffects. Theregressionsareweightedbysamplingweights. Standard errorsarerobustandclusteredbysubdistrict. 6

A.5 Additional Household Results Table8: PSPImpactonEndlineHouseholdIncomeandExpenditures Total Business Total Total Income Income Expenditures Consumption PSP 111 9.2 190* 169 s.e. (84) (12) (112) (107) FAMean 358 54 1600 1512 SampleMean 451 62 1717 1613 Median 196 0 1394 1314 Obs. 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, woman and children in the household, dummies for schooling (i.e., some primary, primary completed, secondary, and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sample is representative at the village level, including all households within FA or PSP villages irrespective of SILCmembership. Standarderrorsarerobustandclusteredbysubdistrict. Notethatincomeandoutcomeswerenot completelybalancedinthebaseline. 7

A.6 Baseline Randomization across Fee vs. No Fee This subsection shows initial differences for the PSP villages in which fees were and were not charged. Table9: BaselineHouseholdSavingsandCreditacrossFeevs. NoFeeVillages Source Purpose PANELI:Savings Total Business Business SellAgric. Salaryor NewAgric. NewNon-Agric. Existing Owners Profit Product Wage Activity Activity Business FeePSP 34 21 32*** 28 -5.0 35 8.2 42 s.e. (42) (43) (12)† (28) (14) (37) (6.3) (26) PANELII:Credit Total Business SILC Formal Informal Agric. Expanding StartNew Owners Activity Business Business FeePSP 7.3 -56 1.5* 0.60 5.1* -8.9 -18 0.45 s.e. (18) (34) (0.87) (18) (2.8) (16) (13) (1.1) Obs. 1237 555 1237 1237 1237 1237 1237 1237 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. ThesampleincludesonlyPSPvillages. Theresultsareestimatedcoefficientsforaregressionofthestatedoutcome on a dummy that signifies whether fees were charged in the PSP village (the baseline are PSP villages in which no feeswerecharged)andthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildreninthe household, dummies for schooling (i.e., some primary, primary completed, secondary, and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. Standard errors are robust and clustered by subdistrict. Table10: BaselineHouseholdProductiveDecisionsacrossFeevs. NoFeeVillages StartNew Business Hoursspent Employees Hoursspent Agric. Hoursspent Business Investment inBusiness (non-HH) asEmployee Investment inAgric. FeePSP -0.003 1.9 3.7* 0.01 0.10 -10 -0.35 s.e. (0.06) (12) (2.1) (0.17) (2.5) (19) (1.4) Obs. 1237 1237 1237 1237 1237 1237 1237 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. ThesampleincludesonlyPSPvillages. Theresultsareestimatedcoefficientsforaregressionofthestatedoutcome on a dummy that signifies whether fees were charged in the PSP village (the baseline are PSP villages in which no feeswerecharged)andthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildreninthe household, dummies for schooling (i.e., some primary, primary completed, secondary, and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. Standard errors are robust and clustered by subdistrict. 8

Table11: BaselineHouseholdIncomeandExpendituresacrossFeevs. NoFeeVillages Total Business Total Total Income Income Expenditures Consumption FeePSP -42 15 146 155 s.e. (85) (15) (140) (133) Obs. 1237 1237 1237 1237 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. ThesampleincludesonlyPSPvillages. Theresultsareestimatedcoefficientsforaregressionofthestatedoutcome on a dummy that signifies whether fees were charged in the PSP village (the baseline are PSP villages in which no feeswerecharged)andthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildreninthe household, dummies for schooling (i.e., some primary, primary completed, secondary, and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. Standard errors are robust and clustered by subdistrict. A.7 Additional Endline Results for Different PSP Villages This subsection shows the endline income and expenditures results for household across different villagetypes. Table12: PSPImpactonEndlineHouseholdIncomeandExpenditures Total Business Total Total Income Income Expenditures Consumption NofeePSP 23 12 20 4.2 s.e. (125) (20) (111) (99) FeePSP 216 18 166* 153* s.e. (162) (14) (93) (91) Obs. 1731 1731 1731 1731 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Theresultsareestimated“intenttotreat”coefficientsforaregressionofthestatedoutcomeontwoPSPdummieswhich representPSPvillagesinwhichnofeesandfeeswerechargedrespectively, thebaselineoutcomeandthefollowing controls: age, age squared, gender, number of men, woman and children in the household, dummies for schooling (i.e., some primary, primary completed, secondary, and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sample is representative at the village level, including all householdswithinFAorPSPvillagesirrespectiveofSILCmembership. Standarderrorsarerobustandclusteredby subdistrict. 9

A.8 Additional Robustness Results A.8.1ResultswithoutMombassaandTahea Table13: PSPImpactsonAgent-LevelOutcomeswithoutMombassaandTahea Groups Members Savings Loans LoanValue Profit Earnings AllQuarters -3.2*** -67** -530 -31 -480 -100 -150*** s.e. (1.0)††† (28) (820) (22) (790) (260) (6.1)††† Quarter1 -4.4*** -87*** -950 -46** -1190* -200 -160*** s.e. (1.0)††† (28)†† (680) (21) (710) (240) (6.0)††† Quarter2 -2.8*** -63** -1010 -36 -950 -500 -140*** s.e. (1.0)†† (27) (870) (23) (920) (360) (8.1)††† Quarter3 -3.7*** -75** -540 -38 -700 -120 -140*** s.e. (1.1)††† (32) (870) (25) (860) (280) (8.0)††† Quarter4 -2.0 -43 350 -5.6 920 410 -150*** s.e. (1.4) (35) (1280) (26) (1030) (440) (5.9)††† FAMean 21 460 7930 250 7410 2110 180 Obs. 715 715 715 715 715 715 715 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. TheresultsareestimatedcoefficientsforaregressionofthestatedoutcomeonaPSPorPSP*Quarterdummyandthe followingcontrols: age, agesquared, gender, numberoflanguagesspoken, numberofchildren, numberoffinancial dependents,dummiesforschooling(i.e.,primarycompleted,secondary,andtertiarywithabaselineoflessthanprimarycomplete),cohort,andlocation-datefixedeffects. Theregressionsareweightedbysamplingweights. Standard errorsarerobustandclusteredbysubdistrict. 10

Table14: PSPImpactsonGroup-LevelOutcomeswithoutMombassaandTahea Members Savings Loans LoanValue Profit Earnings AllQuarters 0.65 68 0.14 35 12 -3.2*** s.e. (0.59) (60) (1.2) (30) (10) (1.0)††† Quarter1 0.47 35 -2.0 -5.5 13 -8.7*** s.e. (0.65) (66) (1.5) (35) (11) (0.60)††† Quarter2 0.61 36 0.14 18 -7.1 -5.6*** s.e. (0.58) (63) (1.5) (27) (12) (0.89)††† Quarter3 0.77 59 0.50 31 11 -2.1** s.e. (0.61) (63) (1.5) (34) (11) (1.1) Quarter4 0.69 130** 1.4 82.22** 30** 0.81 s.e. (0.60) (63) (1.7) (41) (12)† (2.4) FAMean 21 250 10 240 53 9.1 Obs. 13,805 13,377 13,377 13,377 13,377 12,573 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. TheresultsareestimatedcoefficientsforaregressionofthestatedoutcomeonaPSPorPSP*Quarterdummyandthe followingcontrols: age, agesquared, gender, numberoflanguagesspoken, numberofchildren, numberoffinancial dependents,dummiesforschooling(i.e.,primarycompleted,secondary,andtertiarywithabaselineoflessthanprimarycomplete),cohort,andlocation-datefixedeffects. Theregressionsareweightedbysamplingweights. Standard errorsarerobustandclusteredbysubdistrict. 11

Table15: PSPImpactonEndlineHouseholdSavingsandCreditWithoutMombassaandTahea Source Purpose PANELI:Savings Total Business Business SellAgric. Salaryor NewAgric. NewNon-Agric. Existing Owners Profit Product Wage Activity Activity Business PSP 32** 2.5 15** 8.2 15*** 6.5 0.10 19*** s.e. (13) (21) (6.8) (9.2) (4.9)†† (10) (1.7) (5.8)†† FAMean 105 132 18 34 8.2 29 2.3 5.1 SampleMean 133 141 28 40 16 34 2.3 17 Median 49 64 0 0 0 0 0 0 PANELII:Credit Total Business SILC Formal Informal Agric. Expanding StartNew Owners Activity Business Business PSP 32** 22** 4.8** 21* 7.4** 10*** 8.9*** 1.6 s.e. (13) (11) (2.4) (12) (2.9)† (3.7)† (3.4)† (1.3) FAMean 43 34 8.2 24 9.9 5.7 4.2 1.8 SampleMean 62 53 11 34 15 11 11 2.7 Median 11 15 0 0 0 0 0 0 Obs. 1702 779 1702 1702 1702 1702 1702 1702 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sampleisrepresentativeatthevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILC membership. Standarderrorsarerobustandclusteredbysubdistrict.ThesampleincludesallhouseholdswithinFAor PSPvillages-excludingvillagesinMombassaandTahea-irrespectiveofSILCmembership. Table16: HouseholdProductiveDecisionsResultsWithoutMombassaandTahea StartNew Closed Business Hoursspent Employees Hoursspent Agric. Hoursspent Business Business Investment inBusiness (non-HH) asEmployee Investment inAgric. PSP 0.07** -0.23*** 21*** 4.3*** 0.16*** -0.69 -6.9 -1.6 s.e. (0.04) (0.06)††† (6.0)††† (1.6)† (0.05)†† (1.9) (13) (1.5) FAMean 0.22 0.46 47 13 0.23 17 87 26 SampleMean 0.23 0.39 53 15 0.25 16 95 26 Median 0 0 0 0 0 10 16 24 Obs. 1702 779 1702 1702 1702 1702 1702 1702 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sampleisrepresentativeatthevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILC membership. Standarderrorsarerobustandclusteredbysubdistrict.ThesampleincludesallhouseholdswithinFAor PSPvillages-excludingvillagesinMombassaandTahea-irrespectiveofSILCmembership. 12

Table17: HouseholdIncomeResultsWithoutMombassaandTahea Total Business Total Total Income Income Expenditures Consumption PSP 127 15 224 200 s.e. (107) (15) (138) (130) FAMean 398 61 1635 1540 SampleMean 487 68 1741 1630 Median 161 0 1366 1252 Obs. 1702 1702 1702 1702 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,and tertiary with a baseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sampleisrepresentativeatthevillagelevel,includingallhouseholdswithinFAorPSPvillagesirrespectiveofSILC membership. Standarderrorsarerobustandclusteredbysubdistrict.ThesampleincludesallhouseholdswithinFAor PSPvillages-excludingvillagesinMombassaandTahea-irrespectiveofSILCmembership. 13

A.8.2UnweightedRegressions This subsection shows the unweighted endline results for both the agent, group and household data. Table18: PSPImpactsonAgent-LevelOutcomes Groups Members Savings Loans Loan Profit Earnings Value AllQuarters -2.8*** -65*** -1250 -39** -1210 -440 -150*** s.e. (0.94)†† (24)† (830) (18) (740) (320) (4.9)††† Quarter1 -3.7*** -80*** -1190* -48*** -1340** -310 -170*** s.e. (0.91)††† (25)††† (650) (18)† (640) (230) (5.2)††† Quarter2 -2.6*** -67*** -1890* -49** -1880** -910* -150*** s.e. (0.91)†† (23)†† (960) (19)† (940) (490) (6.3)††† Quarter3 -3.2*** -74*** -1520* -42** -1480* -590 -150*** s.e. (1.1)†† (27)†† (900) (20) (770) (390) (6.1)††† Quarter4 -1.8 -43 -420 -17 -160 69 -150*** s.e. (1.3) (30) (1150) (22) (920) (380) (5.0)††† FAMean 20 430 7610 230 7100 2140 180 Obs. 865 865 865 865 865 865 865 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Theresultsareestimatedcoefficientsforaregressionofthestatedagent-leveloutcomeonPSP,therandomizedtreatment, or PSP*Quarter dummy and the following controls: age, age squared, gender, number of languages spoken, numberofchildren, numberoffinancialdependents, dummiesforschoolingi.e. primarycompleted, secondary, and tertiarywithabaselineoflessthanprimarycomplete),cohort,andlocation-datefixedeffects. Agent-leveloutcomes are aggregated from the MIS data group-level outcomes. All regressions are unweighted, standard errors are robust andclusteredbysubdistrict. 14

Table19: PSPImpactsonGroup-LevelOutcomes Members Savings Loans LoanValue Profit Payment AllQuarters 0.26 47 0.55 17 5.6 -4.4*** s.e. (0.60) (52) (1.0) (26) (9.2) (0.91)††† Quarter1 0.25 21 -1.8 -14 8.6 -9.5*** s.e. (0.63) (60) (1.3) (32) (10) (0.65)††† Quarter2 0.06 17 0.53 -1.7 -12 -6.8*** s.e. (0.60) (55) (1.1) (25) (12) (0.81)††† Quarter3 0.32 38 1.3 15 1.9 -3.8*** s.e. (0.65) (54) (1.3) (29) (10) (1.0)††† Quarter4 0.38 99* 1.5 57* 22** -0.69 s.e. (0.64) (54) (1.4) (34) (11) (2.1) FAMean 21 240 9.9 230 53 9.5 Obs. 16,289 15,747 15,747 15,747 15,747 14,907 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated coefficients for a regression of the stated group-level outcome on a PSP (the randomized treatment)orPSP*Quarterdummyandthefollowingcontrols:age,agesquared,gender,numberoflanguagesspoken, numberofchildren, numberoffinancialdependents, dummiesforschoolingi.e. primarycompleted, secondary, and tertiary with a baseline of less than primary complete), cohort, and location-date fixed effects. All regressions are unweighted,standarderrorsarerobustandclusteredbysubdistrict. 15

Table20: PSPImpactonEndlineHouseholdSavingsandCredit Source Purpose PANELI:Savings Total Business Business SellAgric. Salaryor NewAgric. NewNon-Agric. Existing Owners Profit Product Wage Activity Activity Business PSP 26* 8.7 18** 5.8 8.3 15 -1.4 14*** s.e. (15) (26) (8.6) (13) (5.8) (14) (1.6) (5.4)† FAMean 129 163 32 53 18 41 3.4 14 SampleMean 140 157 40 56 20 48 2.4 21 Median 53 63 0 0 0 0 0 0 PANELII:Credit Total Business SILC Formal Informal Agric. Expanding StartNew Owners Activity Business Business PSP 26** 22 2.4 19 6.4** 13* 9.8* 5.2 s.e. (13) (14) (2.9) (12) (2.9) (7.8) (5.4) (3.6) FAMean 59 53 16 30 11 11 11 3.2 SampleMean 77 80 18 43 15 18 21 5.8 Median 16 21 0 0 0 0 0 0 Obs. 1891 865 1891 1891 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,and tertiarywithabaselineofnoschooling). Allregressionsareunweighted,standarderrorsarerobustandclusteredby subdistrict. Table21: PSPImpactonEndlineHouseholdProductiveDecisions StartNew Closed Business Hoursspent Employees Hoursspent Agric. Hoursspent Business Business Investment inBusiness (non-HH) asEmployee Investment inAgric. PSP 0.02 -0.10** 12 2.7** 0.05 -1.0 14 -0.28 s.e. (0.03) 0.05 (9.1) (1.2) (0.06) (1.2) (26) (0.90) FAMean 0.23 0.49 43 13 0.22 16 85 27 SampleMean 0.24 0.42 51 14 0.24 15 93 27 Median 0 0 0 0 0 12 20 25 Obs. 1891 865 1891 1891 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,and tertiarywithabaselineofnoschooling). Allregressionsareunweighted,standarderrorsarerobustandclusteredby subdistrict. 16

Table22: PSPImpactonEndlineHouseholdIncomeandExpenditures Total Business Total Total Income Income Expenditures Consumption PSP 1.6 -0.33 197* 182* s.e. (176) (21) (118) (107) FAMean 579 92 1867 1738 SampleMean 596 92 2001 1857 Median 207 0 1564 1457 Obs. 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomized treatment), the baseline outcome and the following controls: age, age squared, gender, number of men, womanandchildreninthehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,and tertiarywithabaselineofnoschooling). Allregressionsareunweighted,standarderrorsarerobustandclusteredby subdistrict. 17

A.8.3HouseholdEndlineResults-NoBaselineControls This subsection shows the endline result for the household data without controlling for initial conditions. Table23: PSPImpactonEndlineHouseholdSavingsandCredit Source Purpose PANELI:Savings Total Business Business SellAgric. Salaryor NewAgric. NewNon-Agric. Existing Owners Profit Product Wage Activity Activity Business PSP 16 -3.0 16** -3.5 9.3 0.27 -2.2 16*** s.e. (16) (21) (6.6) (8.8) (6.0) (11) (2.5) (4.7)††† FAMean 131 152 14 39 10 38 4.2 4.0 SampleMean 141 153 24 37 15 37 2.6 15 Median 61 83 0 0 0 0 0 0 PANELII:Credit Total Business SILC Formal Informal Agric. Expanding StartNew Owners Activity Business Business PSP 29** 27*** 4.5** 17* 7.9*** 7.8*** 10*** 2.1 s.e. (11)† (9.0)†† (2.0) (10) (3.0)† (2.9)† (3.1)†† (1.3) FAMean 41 32 7.6 22 10 4.6 3.5 1.7 SampleMean 56 50 10 30 16 8.7 9.9 3.0 Median 11 15 0 0 0 0 0 0 Obs. 1891 865 1891 1891 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomizedtreatment)andthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildrenin thehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,andtertiarywithabaseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sample is representative at the village level, including all households within FA or PSP villages irrespective of SILC membership. Standard errorsarerobustandclusteredbysubdistrict. 18

Table24: PSPImpactonEndlineHouseholdProductiveDecisions StartNew Business Business Hoursspent Employees Hoursspent Agric. Hoursspent Business Closed Investment inBusiness (non-HH) asEmployee Investment inAgric. PSP 0.05 -0.17*** 20*** 3.5** 0.12** 0.97 4.5 -2.8* s.e. (0.05) (0.06)† (6.0)††† (1.4) (0.05) (1.5) (10) (1.4) FAMean 0.20 0.49 21 9.4 0.11 14 67 32 SampleMean 0.24 0.42 35 12 0.19 15 69 29 Median 0 0 0 0 0 10 28 30 Obs. 1891 865 1891 1891 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomizedtreatment)andthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildrenin thehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,andtertiarywithabaseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sample is representative at the village level, including all households within FA or PSP villages irrespective of SILC membership. Standard errorsarerobustandclusteredbysubdistrict. Table25: PSPImpactonEndlineHouseholdIncomeandExpenditures Total Business Total Total Income Income Expenditures Consumption PSP 131 11 208* 184* s.e. (86) (12) (115) (109) FAMean 358 54 1600 1512 SampleMean 451 62 1717 1613 Median 196 0 1394 1314 Obs. 1891 1891 1891 1891 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. The results are estimated “intent to treat” coefficients for a regression of the stated outcome on a PSP dummy (the randomizedtreatment)andthefollowingcontrols: age,agesquared,gender,numberofmen,womanandchildrenin thehousehold,dummiesforschooling(i.e. someprimary,primarycompleted,secondary,andtertiarywithabaseline of no schooling). The regressions are weighted by sampling weights. After weighting, the sample is representative at the village level, including all households within FA or PSP villages irrespective of SILC membership. Standard errors are robust and clustered by subdistrict. Note that income and outcomes were not completely balanced in the baseline. 19

A.8.4MeanComparisonEndline This subsection shows the endline mean comparison results for the agent-, group- and householdleveldatawithoutanycontrols. Table26: MeanComparisonofPSPImpactsonAgent-LevelOutcomes Groups Members Savings Loans LoanValue Profit Earnings AllQuarters -2.4* -49* -630 -26 -490 -280 -150*** s.e. (1.2) (29) (860) (23) (950) (360) (3.5)††† Quarter1 -5.1*** -120*** -2650*** -78*** -2620*** -650* -170*** s.e. (1.2)††† (27)††† (800)††† (21)††† (910)†† (390) (3.1)††† Quarter2 -3.5*** -75*** -1760** -46** -1600* -700** -150*** s.e. (1.2)†† (28)† (840) (22) (900) (340) (4.6)††† Quarter3 -1.6 -27 -360 -0.80 150 -330 -140*** s.e. (1.3) (29) (900) (24) (970) (360) (4.7)††† Quarter4 0.43 23 2240** 19 2080* 570 -150*** s.e. (1.4) (32) (1030) (26) 1170 (420) (3.5)††† FAMean 20 430 7610 230 7100 2140 180 Obs. 865 865 865 865 865 865 865 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. Table27: MeanComparisonofPSPImpactsonGroup-LevelOutcomes Members Savings Loans LoanValue Profit Payment AllQuarters 0.10 62 1.0 41 9.5 -4.4*** s.e. (1.0) (42) (1.2) (33) (9.5) (0.84)††† Quarter1 -0.77 10 -1.1 -16 5.1 -8.6*** s.e. (1.0) (49) (1.3) (43) (14) (0.54)††† Quarter2 -0.11 11 0.60 -3.0 -4.5 -6.1*** s.e. (1.0) (42) (1.3) (31) (8.8) (0.69)††† Quarter3 0.35 68* 2.1* 63* 8.2 -3.4*** s.e. (1.0) (40) (1.2) (33) (9.3) (1.0)††† Quarter4 0.67 130*** 1.8 99*** 26** -2.0 s.e. (1.0) (48)†† (1.4) (38)† (11) (1.7) FAMean 21 240 9.9 230 53 9.5 Obs. 16,289 15,747 15,747 15,747 15,747 14,907 ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. 20

Table28: MeanComparisonofPSPImpactsonHouseholdEndlineOutcomes PSP FA PSP-FA Outcomes(measuredpost-treatment) Mean Std. Dev. Obs. Mean Std. Dev. Obs. Mean(cid:52) TotalSavings 145 249 1380 131 232 539 11 SavingsforBusinessOwners 153 261 624 152 260 252 -4.1 SavingsfromBusinessProfits 28 172 1380 14 73 539 14* SavingsfromAgric. Profits 36 115 1380 39 159 539 -4.8 SavingsfromSalary/wage 16 99 1380 10 113 539 6.0 SavingsusedforNewAgric. Activity 37 196 1380 38 163 539 -2.4 SavingsusedforNewNon-Agric. Activity 2.0 18 1380 4.2 30 539 -2.2* SavingsusedforExistingBusiness 20 121 1380 4.0 47 539 16***†† TotalCredit 62 222 1380 41 172 539 22** CreditforBusinessOwners 58 168 624 32 100 252 26** CreditfromSILC 12 38 1380 7.6 24 539 4.3** CreditfromFormalLenders 32 212 1380 22 158 539 10 CreditfromInformalLenders 18 56 1380 10 30 539 7.6***†† CreditusedforAgric. Activity 10 104 1380 4.6 40 539 6.2 CreditusedtoExpandBusiness 12 102 1380 3.5 24 539 8.9** CreditusedtostartNewBusiness 3.6 41 1380 1.7 20 539 1.8 StartNewBusiness 0.25 0.43 1380 0.20 0.40 539 0.05** ClosedBusiness 0.47 0.50 624 0.66 0.47 252 -0.19***††† BusinessInvestment 41 130 1380 22 90 539 19***†† HoursspentinBusiness 13 23 1380 9.4 16 539 3.4***†† Non-HHEmployees 0.23 0.86 1380 0.11 0.54 539 0.12***†† HoursspentinEmployee 15 18 1380 14 18 539 0.83 Agric. Investment 70 171 1380 67 215 539 2.1 HoursspentinAgric. 28 14 1380 32 16 539 -2.6***††† TotalIncome 487 2443 1380 358 1495 539 129 BusinessIncome 65 231 1380 54 218 539 11 TotalExpenditure 1763 1548 1380 1600 1327 539 165** TotalConsumption 1652 1446 1380 1512 1243 539 144** ***,**,and*indicatestatisticalsignificanceatthe1%,5%,and10%confidencelevels,respectively. †††,††,and† indicatestatisticalsignificancewithaBonferronicorrectionatthe1%,5%,and10%confidencelevels,respectively. 21

A.9 Mathematical Appendix We present some more details of the model results. First, we derive the bounds for π and π in Proposition 1. We start with π. Define the additional benefit of type-H members as ∆(f ) = L B(f ;p˜ )−B(f ;p˜ ). It is trivialto show that d∆(fL) < 0as statedin Proposition 1. We need to L H L L dfL derivetheconditionsfor∆(0) > 0. (cid:2)(cid:0) (cid:1) (cid:3) ∆(0) = (p −p ) A−A +(πφ(0)−1)R (0) > 0 H L BL SubstitutinginR (0) = p Ak/(p k +(1−p )φ(0))andsimplifyingyields BL L L L (cid:2)(cid:0) (cid:1) (cid:3) −p Ak + A−A +p A φ(0) > 0 L L Nowsubstitutinginφ(0) = p /(πp +(1−π))andsimplifyingyields H H p A L π > = π ∈ (0,1). (cid:0) (cid:1) p A−A +p A H L Nowconsiderπ. WecansolvebyderivingtheconditionsforB(1;p ) < 0,whichis H (cid:0) (cid:1) B(1;p ) = p A−A +[(1−π +πp )φ(1)−p ]R (1) < 0 H H H H BL Again,substitutingR (1) = p Ak/[p k +(1−p )φ(1)]andφ(1) ≡ pL yields,after BL L L L πpL+(1−π) muchsimplification p A−p A H L π < ≡ π ∈ (0,1). (cid:0) (cid:1) p A−A +p A−p A H H L 22

Clearly,π > π ifandonlyif1 p A−p A > p A. H L L Here left-hand side measures the (per unit) capital production loss of adverse selection, while theright-handsideistheoutsideoptionoftype-L. Thisconditionalwaysholdsasp → 0,andthe L upperboundonp is L (cid:18) (cid:19) A p < p = p L L H A+A Next,wederiveθ fromProposition2. First,noticethattotalsurplus(netofF∗)ishigherunder F∗ ifandonlyiftotaloutput(netofF∗)ishigherunderF∗,sinceoutputisonlydistributedamong members, and the outside options are always the same. Knowing that F∗ leads to f = 0, we can L expresstheconditionthattotaloutputishigherundertheF∗ as: (cid:0) (cid:1) (1−θ) p A−F∗ +θp A > (1−θ)p A+θp A H L H L SubstitutinginF∗ = B(0;p˜ )andsimplifyingyields L (cid:0) (cid:1) p A−A −B(0;p˜ ) H L θ < = θ ∈ (0,1) (cid:0) (cid:1) (p +p ) A−A −B(0;p˜ ) L H L ˆ Next,weneedtoshowthatthereexistsanf suchthat: L (cid:0) (cid:1)(cid:2) (cid:0) (cid:1)(cid:3) (cid:16) (cid:17) A−A p2 +p p 1−π B f ˆ ;p˜ = 0 ⇔ f ˆ = H H L π L H L (p −p ) (cid:2) p2 (cid:0) A−A (cid:1) +p A (cid:0) 1−π (cid:1)(cid:3) H L H L π ˆ Then, substitute in for B(0,p˜ ) and derive a condition for which f < θ. One can show that L L 1RecallthatFootnote8hasanadditionalsufficientconditionof 1 < pL(1−pH) foradverseselectiontohold. The k pH(1−pL) economicsofthisisdrivenbythecollateralratio,however,areassumptionsmadetosimplifymarketclearingtherefore implyπ < pL(1−pH) . Ifthisboundislessthanπ thensufficientconditionsonparametersalsoexisttoensurethatit pH(1−pL) exceedsπ.Namely,itrequiresA/A < (1−p )/(2−p ). Parameterssatisfyingthisconditionaswellastheother H H conditions hold (e.g., A → 0). More generally, this condition constraining π depends on our πk → 1, which was economicallyarbitrarybutdoneforreasonsofsimplifyingalgebra. 23

thisholdswhenthefollowinginequalityissatisfied: (cid:8) (cid:0) (cid:1)(cid:2)(cid:0) (cid:1) (cid:0) (cid:1) (cid:3)(cid:9) p3 p π A−A A−Aπ − A−A π H L (cid:8)(cid:2) (cid:0) (cid:1) (cid:3)(cid:0) (cid:1) (cid:0) (cid:1) (cid:0) (cid:1)(cid:9) +p2 p2 2π2 A−A +Aπ A−A +Aπ(1−π) 3A−2A +A Aπ −A H L (cid:110) (cid:104) (cid:105) (cid:111) +p p3 (cid:0) A−A (cid:1) π (cid:2) 2π − (cid:0) A−A (cid:1) π (cid:3) +(1−π) 3AA(1−π)−A 2 +Aπ (cid:0) 3A−π (cid:1) H L −p4 (cid:8) AA(1−π)2(cid:9) > 0 L ˆ Asp issufficientlycloseto0,asufficientbutnotnecessaryconditionforf < θ is: L L A (cid:0) (cid:1) (cid:0) (cid:1) A−Aπ > A−A π ⇔ π < . 2A−A Recall that we already defined an upper bound π, and it is straightforward to show that the aboveboundexceedsthisupperbound,i.e.: ¯ A p A−p A H L > π = (cid:0) ¯ (cid:1) ¯ 2A−A p A−A +p A−p A H H L ˆ Thereforetheprevioussufficientconditionforf < θ isalwayssatisfiedasp → 0. L L Finally,theresultsfromProposition3arestraightforward. UsingY∗,Y∗ andY todenotetotal 2 1 0 maximumoutputundertwo,oneandzerofees,wehave: (cid:0) (cid:1) Y∗ = (1−θ) p A−F∗ +θp A 2 H L (cid:0) (cid:1) Y∗ = (1−θ) p A−F∗ +θp A 1 H L Y = (1−θ)p A+θp A. 0 H L Y∗ > Y , follows from the assumption that (1−θ)p > θp , while Y∗ > Y∗ follows from 1 0 H L 2 1 A > A. 24

A.10 Data Description A.10.1 Household Survey Data SavingsMeasures The measure of total savings is the sum of all savings the survey respondent records from: the SILC group, merry-go-round (a group that collects money from each member and gives it to one personinturn),agroupoffriendsthatlendwithinterest,abank,amicrofinanceinstitution(MFI), a SACCO/Co-operative (organization that requires you to be a member, e.g., agricultural co-op or workplace co-op), mobile money, a secret hiding place, giving to a friend or family member to keep, crops or grains in storage, and other savings which need to be specified. For the savings comingfromthemerry-go-round,therespondentrecordstheamountofmoneythatheorshewould receive when it is their time to cash out. For crops or grains in storage, the respondent records the amount of money they would receive if they would sell all of it. Total savings are recorded in the localcurrencyandweconvertdatafromlocalcurrenciesintoUSDusingexchangeratesatthetime ofsurveyforeachcountry. Totalsavingsforbusinessownersthenistotalsavingsasjustdescribed forthosesurveyrespondentswhorecordedtoownabusinessinthebaselinesurvey. Besidesbreakingdownthetotalamountofsavings,therespondentisalsoaskedwhatthemost important source and purpose are for these savings. In the paper, we focused on savings coming from three sources: business profits, selling agricultural products and salary or wages. We define themainsourceofsavingsastotalsavingsforthoserespondentsthatrecordbusinessprofits,selling agriculturalproductsandsalaryorwagesasbeingthemostimportantsourceofanytypeofsavings they have. For the main purpose of savings, we also focused on three: new agricultural activity, new non-agricultural business and improve an already existing business. Each purpose of savings isdefinedinasimilarwayasisthesourceofsavings: itistotalsavingsforrespondentsthatrecord new agricultural activity, new non-agricultural business and improve an already existing business asbeingoneofthemainpurposesofsavingsinthelast12months. 25

CreditMeasures Totalcreditisthesumofallloanamountsreceivedinthepast12monthsfrom: theSILCgroup,an ASCA,abank,anMFI,aSACCO/Co-operative,amoneylender,anemployer,abuyerofproducts who gives you cash/input in advance, a local shop/supplier that allows you to take goods/services on credit, family and friends, goods/items on hire purchase, and other sources which need to be specified. Total credit is recorded in the local currency and we convert data from local currencies into USD using exchange rates at the time of survey for each country. Total credit for business owners then is total credit as just described for those survey respondents who recorded to own a businessinthebaselinesurvey. Wedividedthesourceofcreditintothreemaincategories: creditcomingfromtheSILCgroup, formal and informal credit. Formal credit is defined as the sum of all loan amounts received in the past 12 months from the more formal sources i.e. from ASCA, a bank, an MFI, SACCO/Cooperative or a moneylender. Informal credit are all loans in the past 12 months coming from informal lenders: an employer, a buyer of products who gives you cash/input in advance, a local shop/supplierthatallowsyoutotakegoods/servicesoncredit,familyandfriends,andgoods/items on hire purchase. The purpose of credit is defined as total credit for those respondents that record farm inputs or improvements, expanding your business or starting up a new business as being one ofthepurposes. Inthepaperwefocusedmainlyonthesethreepurposes. TimeUseMeasures Weekly time-use measures for the respondent were constructed by asking for the number of rest days and work days in a typical week and then detailing the time-use separately for rest and work daysacrosslaborforownbusiness,ownfarm,homeproduction/childbearing,andmarketlabor. ConsumptionandExpenditureMeasures Expenditures are a sum of the following data. We have weekly spending data on food, beverages (alcoholic and non-alcoholic), and tobacco. Next, respondents record monthly spending on housing, transport and communication, health and medical care, and personal expenses. Finally the 26

survey asked for yearly spending on clothing and footwear, things for the house, education, livestock/agriculture investment, business investment, social obligations, and land. We then convert the weekly and monthly data to yearly data and ad up all expenditures to a yearly measure. All expendituresarerecordedinthelocalcurrencyandweconvertdatafromlocalcurrenciesintoUSD using exchange rates at the time of survey for each country. In order to measure consumption we subtract all investments from the expenditures measure. These include both livestock/agricultural investmentandbusinessinvestment. IncomeMeasures We measure total income as the total income in the past 12 months (to account for seasonalities). These data were collected separately for the respondent personally and the household overall. Besidesreportingtotalincome,thesurveyalsoaskedtobreakdownincomebydifferentactivities: incomefromwageandsalary,businessincomeetc. Thisiswherethemeasureforbusinessincome comesfrom. Moreformally,itisdefinedasincomefortherespondentearnedfromhis/herbusiness that is not a farm/agriculture in the past 12 months. Measurement of home production is another majorissue,especiallyforagriculture. Itislikelythathomeproductionwasnotconsideredincome byrespondents. Bothincomemeasuresaresubstantiallylessthanourmeasureofannualpurchases, whichexcludehome-producedandgratisconsumption. Finally,reportedhouseholdincomeswere only marginally higher than reported income of respondents. Thus, it appears there is also likely underreporting. Incomeisrecordedinthelocalcurrencyandweconvertdatafromlocalcurrencies intoUSDusingexchangeratesatthetimeofsurveyforeachcountry. A.10.2 MIS Data • Allmonetaryvariables(savings,loanvalue,profit,andearnings)areconvertedtoUSdollars usingexchangeratesatthetimeofdatacollection. • Savings,profit,andearningsmeasureaccumulatedtotalsoverthecourseoftheentirecycle. Groups,members,loans,andloanvaluemeasuretotalsatthetimeofdatacollection. 27

• Savings, loans, loan value, profit, and earnings are reported in per quarter terms for grouplevel impacts and as a simple sum across groups each agent is working with at the time of datacollectionforagent-levelimpacts. MembershipMeasures Groups measures the number of groups each agent is working with at the time of data collection. This variable is measured only at the agent level. Members measures the number of members in eachgroupatthetimeofdatacollection. Foragent-levelimpactswesumacrosseachofthegroups aparticularagentisworkingwith. SavingsandLoanMeasures Savings measures the total value of savings over the course of the current cycle, converted to US dollars using exchange rates at the time of data collection. Since savings accumulate over time, we report savings per quarter for the group-level impacts so groups that started at different times will be comparable. For agent-level impacts, we report savings summed across all groups with no adjustment made for weeks in each group’s cycle. Loans gives the number of loans outstanding at the time of data collection. As with savings, we normalize the group-level results to loans per quarter since the number of outstanding loans is likely to grow over time. The agent-level results aresummedacrossallgroupstheagentiscurrentlyservingwithnoadjustmentmadeforlengthof current cycle. Loan value is the value of outstanding loans (converted to US dollars) at the time of data collection. The group and agent-level results are calculated in the same manner as savings andloans. ProfitandEarnings Profit measures the total amount of profit earned over the course of the current cycle by each group (converted to US dollars). Profits include money earned from registration fees, fines, and interest earned from loans and can be positive or negative. For group-level impacts we normalize toprofitperquarter,whileforagent-levelimpactswesumacrossgroupswithnosuchadjustment. Earnings measures the amount of money in US dollars that the group has paid to the agent over 28

the course of the current cycle. The payment may come in several forms, most commonly as a fixed group/member fee, share of savings, or share of profits. For group-level impacts we report earnings per quarter, while for agent-level impacts we report the total across the agent’s groups withnoadjustmentmadeforlengthofcurrentcycle. A.10.3 Weights Wecreateasetofweightsbasedbasedon: (1)samplingweightsand(2)countryweights. Firstwe createthesamplingweights. IneachvillagefiveSILCandfivenon-SILChouseholdsaresampled. However, these might not reflect the underlying data. For instance, imagine a village with 30 households of which 20 are SILC and 10 are non-SILC. If five household are sampled from each category,inthisexample,thenon-SILChouseholdswouldbe“oversampled”comparedtothenon- SILC households i.e. 50% of the non-SILC households are repesented as opposed to only 25% of the SILC households. In order to take this into account, each observation will be weighted by the inverse of its probability of being sampled. In this example SILC household would receive a weightoffourandnon-SILChousholdstwo. ExampleVillage SILC Non-SILC Census 20 10 Sample 5 5 Probabiltyofbeingsampled 0.25 0.50 Weight(=Inverseprobability) 4 2 Second, we create the country weights. Recall that the sample contains data from three countries: Kenya, Tanzania, and Uganda. If we break down the village data by country and treatment wehavethefollowingtable: Kenya Tanzania Uganda Total PSP 65 34 39 138 FA 18 13 23 54 83 47 62 192 29

Now we see that in the overall sample the ratio of PSP vs FA is 138 ≈ 2.6. Note that this ratio 54 is not the same across countries. In Kenya it is 65 ≈ 3.6, in Tanzania 34 ≈ 2.6 , and in Uganda: 18 13 39 ≈ 1.7. This could lead to biased results when estimating the impact of PSP treatment. More 23 specifically, we would be mostly pick up the treatment effects in PSPs in Kenya and Tanzania as theirPSPtoFAratioishigherthanintheoverallsample. Therefore,weneedtoweighthedifferent villagessuchthattheratioineachcountryisthesameasintheoverallsample. Inotherwords: 65wK 34wT 39wU 138 PSP = PSP = PSP = 18wK 13wT 23wU 54 FA FA FA and 65wK +18wK = 83 PSP FA 34wT +13wT = 47 PSP FA 39wU +23wU = 62 PSP FA 30