Does Financial Inclusion Exclude? The Effect of Access to Savings on Informal Risk-Sharing in Kenya

Transcription

1 Does Financial Inclusion Exclude? The Effect of Access to Savings on Informal Risk-Sharing in Kenya Felipe Dizon Erick Gong Kelly Jones January 15, 2016 JOB MARKET PAPER Most recent version here. Abstract In the absence of formal markets to manage risk, individuals often rely on mutual interpersonal transfers, otherwise known as informal risk-sharing arrangements (IRSAs). Theoretically, an improvement in access to savings can lead to substitution away from IRSAs, and this substitution can lead to a reduction in the capacity to manage risk. We estimate the effect of access to savings on bilateral IRSAs using a randomized controlled trial of a microsavings initiative in Kisumu, Kenya. Of a sample of 627 vulnerable women, half were randomly selected to receive a labeled mobile money savings account along with weekly reminders on savings goals. We find that the savings intervention reduced informal risk-sharing, while it did not affect non-mutual interpersonal transfer arrangements. The reduction in risk-sharing did not translate into negative welfare effects. We find some evidence that individuals may have coped with the reduction in risk-sharing by increasing risk-sharing with other risk-sharing partners. Overall, our study suggests that the design of initiatives aimed at improving access to microsavings should consider the reduction in informal risk-sharing, especially in contexts where people might fail to find other means to manage risk. JEL Classification: O12, O16, O17, D14, D91 Keywords: savings, risk-sharing, insurance, kenya, mobile money Corresponding Author: ffdizon@ucdavis.edu. Felipe Dizon is grateful for the guidance and support from his advisers: Travis Lybbert and Steve Boucher. We received invaluable support from Malin Olero of KidiLuanda Community Programme; Petronilla Odonde of Impact Research and Development Organization; Alexander Muia, Elizabeth Kabeu, Sylvia Karanja, and Evans Muga of Safaricom; our field managers Lawrence Juma, Jemima Okal, Matilda Chweya, and Joyce Akinyi; and IPA Kenya. We appreciate feedback from participants at NEUDC 2015, MWIEDC 2015, Giannini ARE student conference 2015, an IFPRI internal seminar, a USF Economics seminar, and a UC Davis ARE Development Workshop. Research funding was provided by the Hewlett Foundation, IFPRI and the UC Davis Blum Center. All activities involving human subjects were approved by IRBs at IFPRI, Maseno University in Kenya, Middlebury College, and UC Davis. All errors are our own. Web appendix available here. PhD Candidate, Agricultural and Resource Economics, University of California, Davis Assistant Professor, Economics, Middlebury College Research Fellow, International Food Policy Research Institute

2 1 Introduction Improving the access of the poor to formal financial markets is a key policy agenda. 1 Within this financial inclusion movement a more recent focus has been placed on initiatives to improve access to microsavings. 2 This is due both to the decrease in costs to deliver microsavings vehicles and to the growing evidence on the positive benefits of microsavings, such as better ability to manage risk. 3,4 Yet, it remains unclear how formal microsavings initiatives interact with existing informal institutions to manage risk. One such institution is the set of informal risk-sharing arrangements (IRSAs) that specify state-contingent interpersonal transfers. These IRSAs are especially widespread in the developing world where formal credit and insurance markets are incomplete (Townsend, 1994). The interaction between formal savings and IRSAs may be important in determining the effect of formal savings on the capacity to manage risk. On one hand, access to formal savings can complement the risk management capacity provided by existing IRSAs in two ways: the savings account holder can draw on savings to supplement the transfers she receives in an IRSA when she experiences a shock, and she can provide more transfers when members of her risk-sharing network experience a shock. On the other hand, access to formal savings can lead to substitution away from IRSAs, and this substitution could lead to a reduction in the capacity to manage risk. It is well established that limited commitment and information asymmetries limit the amount of idiosyncratic risk that can be managed through IRSAs. 5 Access to savings can exacerbate the limited commitment problem in IRSAs by increasing an individual s incentive to renege on her IRSA commitments. As such, access to savings can crowd out IRSAs, thereby reducing the capacity to manage risk (Ligon, Thomas, and Worrall, 2000). 6,7 Moreover, if 1 For example, in 2013 alone, $31 billion was pledged globally to support financial inclusion (CGAP, 2015). 2 For example, in 2010, the Gates foundation provided $500 million to support microsavings initiatives. 3 Advancements in digital technologies such as mobile money, and insights from behavioral economics such as commitment devices (Dupas and Robinson, 2013) and simple reminders (Karlan et al., Forthcoming) are lowering the costs to delivering effective savings technologies. 4 Simply providing access to formal savings accounts has been shown to improve the ability to cope with shocks and one s perceived overall financial situation (Prina, 2015). 5 See, for example, Ligon, Thomas, and Worrall (2002); Thomas and Worrall (1990); Barr and Genicot (2008); Chandrasekhar, Kinnan, and Larreguy (2011). Enforcement problems are only partially solved by repeated interaction (Coate and Ravallion, 1993), balanced reciprocity (Udry, 1994; Platteau, 1997; Fafchamps, 1999; Fafchamps and Lund, 2003; De Weerdt and Dercon, 2006), and social proximity (Kinnan and Townsend, 2012; Attanasio et al., 2012; Chandrasekhar, Kinnan, and Larreguy, 2014). 6 The ambiguous effect of savings on IRSAs in the context of limited commitment has also been derived by Foster and Rosenzweig (2000) with borrowing allowed, by Ligon, Thomas, and Worrall (2002) with a simpler version, and by Gobert and Poitevin (2006) who allow for savings as collateral. 7 The interaction of IRSAs and savings is part of a broader literature that looks at the interaction of IRSAs with 1

3 access to savings reduces risk-sharing, then differential access to savings across risk-sharing partners could lead to inequality in risk-coping abilities. Whether formal savings increases risk managment capacity or reduces risk-sharing is primarily an empirical question. In our study, we estimate the effect of improved access to savings on transfers in existing bilateral IRSAs. Our data best permits us to estimate the effect on a bilateral or two-person IRSA, and these bilateral IRSAs may be the relevant unit of analysis because smaller risk-sharing groups may be more efficient than larger ones. 8 Our study is the first to document a negative effect of access to savings on the amount of insurance provided through IRSAs, thereby demonstrating one way by which expanding access to formal microfinance can undermine existing informal arrangements. One unique feature of our study is that we carefully identify risk-sharing as a mutual exchange agreement made ex-ante (or prior to the realization of shocks). We identify risk-sharing arrangements using potential transfers as opposed to actual transfers, since the value of a risk-sharing arrangement is not the amount one receives, but rather the amount one could receive if she experienced a shock. Identifying risk-sharing based on actual transfers can be problematic if it excludes arrangements where actual transfers did not occur, even if such arrangements did provide insurance against shocks. Moreover, we identify risk-sharing arrangements as mutual arrangements, such that each individual in an arrangement is both a potential provider and receiver of support. 9 The mutuality in IRSAs is the foundation of the limited commitment problem, and limited commitment theoretically drives the substitution away from IRSAs and into formal savings. A second unique feature of our study is that the savings intervention that we evaluate was designed to increase liquid savings, and was thus unlikely to encourage saving for investment. As such, the savings intervention likely affected consumption smoothing, making it a viable substitute for IRSAs. 10 A third unique feature is that we measure treatment spillover effects on the welfare other risk-mitigating strategies. For the effects of public transfers and access to formal financial institutions on IRSAs, see: Angelucci and De Giorgi (2009); Angelucci, De Giorgi, and Rasul (2012); Kinnan and Townsend (2012); Attanasio and Rios-Rull (2000). For the effects of formal insurance on IRSAs and vice versa, see: Berhane et al. (2014); Boucher and Delpierre (2013); Klohn and Strupat (2013); Landmann, Vollan, and Frölich (2012); Mobarak and Rosenzweig (2012). 8 For example, see: Chaudhuri, Gangadharan, and Maitra (2010); Fitzsimons, Malde, and Vera-Hernandez (2015); Genicot and Ray (2003) 9 More specifically, in our study, a pair of individuals i and j are linked together in an IRSA if i would be willing to financially support j if j faces an emergency, and if j would be willing to financially support i if i faces an emergency. 10 Similarly, the savings interventions studied in Chile (Kast and Pomeranz, 2014) and in Nepal (Prina, 2015; Comola and Prina, 2015) mostly altered precautionary savings, and not savings for investment. We, however, argue 2

4 of risk-sharing partners. While formal savings can improve the risk management capacity of direct account holders, those linked to them through IRSAs might see a decrease in their capacity to manage risk if there is a breakdown of IRSAs. Evaluating the effects of microsavings on poverty and risk management should account for these potential spillovers. 11 Our analysis relies on a field experiment conducted in Kisumu, Kenya, a major urban center, where the intervention offered a formal savings product to increase liquid savings. From a sample of 627 vulnerable women, those who were most likely to be negatively affected by shocks, we randomly selected half to receive a free mobile money savings account labeled for emergency expenses and savings goals. We utilize M-PESA, a mobile financial platform that is used widely throughout Kenya. Women who received the account were also asked to set savings goals and were sent weekly SMS reminders on these goals. The intervention was aimed at encouraging women to accumulate liquid savings easily accessible in the event of a shock. 12,13 We find that access to savings reduced risk-sharing. Between risk-sharing pairs, treatment reduced potential transfers by percent and reduced actual transfers by percent. At the extensive margin, treatment led to a reduction in the number of bilateral risk-sharing partners, as it reduced the probability of forming (net of severing) a risk-sharing link by 16 percent. We further show that this negative effect was unique to IRSAs. Thus, the limited commitment problem inherent in these IRSAs, but not in other transfer arrangements, may be explaining the treatment effects. Treatment did not affect actual transfers received for those that did not experience a shock, nor did it affect transfers between non-mutual exchange partners. The reduction in risk-sharing did not translate into negative welfare effects on those who did not receive the savings treatment. Those who did not receive the savings treatment instead increased that among this set of liquid savings instruments, ours is most liquid because we introduce easily accessible mobile money accounts, as opposed to traditional bank accounts. 11 We study the direct effect of savings on welfare in a separate paper (Dizon, Gong, and Jones, 2015). Others have studied spillover effects on welfare, but each of these studies varies on whom they evaluate effects on (Chandrasekhar, Kinnan, and Larreguy, 2014; Dupas, Keats, and Robinson, 2015; Flory, 2011; Kast and Pomeranz, 2014; Comola and Prina, 2015). We focus on welfare spillover effects on risk-sharing partners. 12 Given the ubiquity of M-PESA agents in our study area, it is relatively easy for anyone in our study to access the funds in their labeled mobile savings account. 13 The intervention in our study is similar to a soft commitment design, where savings is encouraged, but there are few restrictions on how savings is withdrawn or used; For example, see: Brune et al. (2015); Dupas and Robinson (2013); Kast and Pomeranz (2014). In contrast, a hard commitment savings intervention requires savings to be locked-up over a certain period of time or has direct monetary penalties for withdrawing funds from one s savings; For example, see: Ashraf, Karlan, and Yin (2006). Hard commitment saving interventions thus make it difficult to use savings for unexpected emergencies. 3

5 risk-sharing with other partners if they were linked to a risk-sharing partner who received the savings treatment. Alongside many other explanations, this may partially explain the lack of welfare spillover effects. Our findings contribute to the empirical literature evaluating the effects of formal savings on interpersonal transfers and consequent effects on welfare. Several studies document nil or negative effects. In Kenya, Dupas, Keats, and Robinson (2015) find that access to a formal savings account reduced the transfers received from one-way support partners. Among female micro entrepreneurs in Chile, Kast and Pomeranz (2014) find that access to a formal savings account reduced short-term debt, especially informal credit received from family and friends, thereby reducing consumption cutbacks and anxiety about the future. 14 Using lab experiments in India, Chandrasekhar, Kinnan, and Larreguy (2014) find that introducing savings had no effect on transfers in limited commitment risk-sharing agreements, so that savings improved consumption smoothing. However, they find that socially distant pairs were more likely to save if allowed to, and that centrality-dissimilar pairs reduced risk-sharing transfers when allowed to save. 15 Meanwhile, other studies document positive effects of savings on transfers. In the same study in Kenya, Dupas, Keats, and Robinson (2015) find that access to a formal savings account increased the transfers sent to within-village mutual sharing partners, but had no effect on the food security of these partners. Among women in Nepal, Comola and Prina (2015) find that access to a formal savings account increased the transfers sent to and the number of in-village financial partners, thereby inducing positive spillovers on health expenditures of these partners. In Malawi, Flory (2011) shows that a marketing campaign of banking services increased the use of formal savings and the gift-giving to the most vulnerable people ineligible to receive the program, thereby improving the food security of these vulnerable individuals. The positive, negative and nil effects uncovered in the literature suggest that both the type of savings initiative and the type of interpersonal financial exchange matter. Some savings initiatives, 14 Consistent with the results of Kast and Pomeranz (2014), we find that in our study the savings intervention reduced informal credit received from family and friends. 15 Using lab games in the Philippines, Landmann, Vollan, and Frölich (2012) show that savings reduces interpersonal transfers. Beyond the effect of microsavings specifically, the introduction of formal financial institutions in India (Binzel, Field, and Pande, 2013) and the strengthening of other risk-sharing institutions in Ethiopia (Berhane et al., 2014) have been shown to reduce interpersonal transfers. And, using observational data from Pakistan and India, Foster and Rosenzweig (2000) find that villages closer to banks tend to use savings more and had a lower incidence of interpersonal transfer arrangements, but the remaining transfer arrangements sustained a higher level of insurance. 4

6 such as those that introduce penalties for withdrawal, may encourage saving for investment, while other programs might encourage liquid savings. Beyond mutual risk-sharing, other motives for transfers include altruism (Ligon and Schechter, 2012), pooling resources for investment (Angelucci, De Giorgi, and Rasul, 2012), and transferring resources due to social pressure (Jakiela and Ozier, 2015). 16 We focus on the effect of liquid savings on risk-sharing, because it is the primary pathway by which encouraging individual savings could potentially harm the capacity to manage risk. This paper is the first to document the potential for negative consequences of formal microsavings initiatives through their impact on informal risk-sharing networks. The remainder of this paper is organized as follows. In section 2 we describe our field experiment and data. In section 3 we present descriptive statistics. In section 4 we present our estimates of the treatment effect on bilateral risk-sharing, and provide evidence that limited commitment likely caused the reduction in risk-sharing. In section 5 we present our estimates of treatment spillover effects on welfare, and explore some explanations for the lack of effects on welfare. Finally, in section 6, we conclude by summarizing our findings and discussing policy implications. 2 Experiment and data collection The field experiment was conducted on a sample of 627 vulnerable women in both urban and rural areas in Kisumu County on the western edge of Kenya. The urban subsample consisted of female sex workers (FSWs) and the rural subsample consisted of widows, separated or divorced women, and never-married female heads-of-household without support from a man. In this section, we describe the field experiment and data collection. We describe the sample in more detail in section 3 below. 2.1 Treatment and randomization Figure 1 summarizes the sample structure and study design. The study had one control arm and two treatment arms. The control group participated in group discussions on the importance of savings. Those assigned to the first treatment (T1 arm) received the same as the control arm, plus a one-on-one activity eliciting savings goals, weekly SMS reminders on the savings goals, and a new free 16 For a useful qualitative discussion on interpersonal exchange relationships in Kenya, see Johnson (2015). 5

7 M-PESA account with zero transaction costs to be used as a labeled savings account. 17 Transaction costs were zero only in the first 12 weeks of the intervention, the most intense intervention period from March to May 2014 (see Figure 2). During this intense 12-week period, in addition to enjoying zero transaction costs, women were surveyed once a week and received weekly SMS reminders. Those assigned to the second treatment (T2 arm) received the same as the T1 arm, however, the M-PESA labeled savings account was interest-bearing for those in the T2 arm, with a 5% monthly interest rate. The interest payments were only paid in the first 12 weeks of the intervention. Elsewhere, we show that the interest payments received by those assigned to the T2 arm did not affect savings (Dizon, Gong, and Jones, 2015). This is consistent with the findings of Kast and Pomeranz (2014) who use a similar interest rate. We thus pool the T1 and T2 arms into a single treatment arm in our analysis. 18 Owning an existing M-PESA account was an eligibility requirement for participation in the study. 19 Thus, the treatment was effectively the provision of a labeled M-PESA account, as opposed to granting first-time access to M-PESA. 20 Operated by the leading mobile service provider Safaricom, M-PESA is a highly successful private enterprise which provides clients with branchless banking via mobile phone. Any individual with a national ID card and Safaricom SIM card can set up an M-PESA account, allowing her to make deposits, withdrawals and transfers using her mobile handset. M-PESA points are ubiquitous; they are located at nearly every shop and one can be found open at nearly any time of day. The unit of randomization is the individual. We first identified geographic clusters: 12 sublocations or politically defined geographic units in the rural subsample, and 15 hotspots or specific areas within the urban subsample where the FSWs meet clients. 21 We then stratified treatment 17 During the first 12 weeks of the intervention, all treatment women received weekly SMS reminders. During the four months that followed those first 12 weeks, only a randomly selected half of the treatment women received SMS reminders, and these SMS reminders were sent monthly. 18 Within both the T1 and T2 arms, we randomly assigned two types of weekly SMS reminders. This also did not have an effect on savings balances (Dizon, Gong, and Jones, 2015). 19 Using data from internal census activities, we can infer that as a result of the M-Pesa criteria for study eligibility we excluded 16% of the vulnerable women from the rural area and 23% from the urban area. It is likely that these women are poorer than our sample which has access to M-Pesa. From an external validity standpoint, our results will not necessarily extrapolate to those worst off in the set of vulnerable women. 20 Jack and Suri (2014) show that access to M-PESA improves risk-sharing by reducing transaction costs. In our study, women in both the treatment and control groups in our study had initial access to M-PESA. We our thus studying the effect of access to savings on risk-sharing, as opposed to the effect of M-PESA on risk-sharing. Our analysis of the effects on risk-sharing applies to a population which has better risk-sharing at baseline, relative to a population that does not have access to M-PESA. 21 Kenya is divided into counties, then sub-counties, then locations, then sub-locations, then villages. There are 47 6

8 randomization by subsample and then by geographic cluster. Each cluster was randomly assigned to either type one or type two. Within each cluster, each individual was assigned into treatment or control. Those assigned to treatment in type one clusters were assigned to the T1 arm and those assigned to treatment in type two clusters were assigned to the T2 arm. We had also stratified treatment randomization by age. 22 Treatment was randomly assigned conditional on geographic cluster and age. To evaluate the success of the randomization, we compare 177 baseline observables between the treatment and control groups, conditional on geographic cluster and age. As expected, we find differences between treatment and control with p < 0.05 for 4% of the variables Sampling and data collection Sampling was conducted during December 2013 and January In the urban area, a sampling team attended scheduled meetings of female sex worker (FSW) peer educators, to census the FSWs who the peer educators support. Each FSW was met with individually for enrollment. In the rural area, the sampling team visited each of the villages in the study, seeking eligible women by talking with local leaders and snowball sampling. Figure 2 summarizes the timeline of data collection and intervention activities. We conducted a baseline survey with 627 women in January 2014 prior to the implementation of the intervention in February We conducted an endline survey with 579 of the 627 women eight months after the intervention. The overall 7.6% attrition rate is similar between treatment and control groups. Furthermore, there is no evidence of differential attrition between treatment and control groups based on baseline characteristics. 24 counties in Kenya, and roughly 2,400 locations and 6,600 sub-locations. Each location has a state appointed chief, and each sub-location has state appointed assistant chiefs. Kisumu county has 7 sub-counties, and our sample falls into the Nyando and Kisumu Central sub-counties. 22 Stratification by age was done through re-randomization. We repeated randomization 500 times. A subset of these 500 randomizations satisfied the pre-specified criteria that the differences-in-means test for the variable age across treatment and control groups must have p < A randomly chosen realization was selected to be used as the basis for treatment assignment. 23 Treatment women were more likely to be divorced or separated, to have a lower resale value of livestock assets, and to have spent more on social events, and were less likely to own chickens, to hold a leadership position in a community group, and to have severe anxiety (using the GAD-7 measure). 24 Among endline attritors we found only 6.7% of 178 baseline variables to be statistically significantly different between treatment and control at p < However, the sample of attritors is too small to rely on for comparison of means between the treatment and control groups. 7

9 2.3 Risk-sharing data Our contribution is to estimate the effect of access to savings on IRSAs. As such, we focus our analysis on the subset of interpersonal financial relationships where the transfers were ex-ante agreed upon, state-contingent, and mutual. Similar to conventional insurance products, the value of an IRSA should not be measured as the value of transfers actually received, but rather as the value that one could potentially receive in case she experiences an unexpected emergency. Moreover, of the set of interpersonal insurance relationships, an IRSA is unique in that the provision of insurance is mutual. The mutuality in an IRSA generates limited commitment problems that can lead to substitution away from IRSAs and into formal savings. In this section, we discuss how we identify IRSAs and measure risk-sharing within an IRSA. To identify a respondent s bilateral IRSAs, or risk-sharing partners, we asked the respondents the following two questions about a candidate individual: could you rely on this person for help if she needed money urgently to pay for an expense?, and could this person rely on you for help if she needed money urgently to pay for an expense? A candidate individual is considered a risk-sharing partner if the respondent reported yes to both of these questions. This identifies risk-sharing partners because it captures the ex-ante, state-contingent, and mutual nature of an IRSA. We capture ex-ante arrangements by asking who one could receive support from; this is elicited independent of realized shocks and actual transfers. 25 We capture arrangements about state-contingent transfers by asking who one could receive support from in case of an urgent expense. We capture mutual transfers arrangements by asking respondents to identify individuals who were both potential providers and recipients of support. In order to evaluate treatment-induced changes in the set of risk-sharing partners, we collected data on one s risk-sharing partners both at baseline and endline. To measure the level of risk-sharing within an IRSA, we ask the following questions about each risk-sharing partner: what is the maximum amount that this person (you) would give you (this person) in the event that you (this person) faced an unexpected expense? The responses generate a measure of potential transfers that we define as bilateral maximum informal insurance agreements Comola and Fafchamps (2014) discuss two important issues that arise when using subjective survey questions to elicit network links. First, when a respondent reports that a link exists, she may mean that a link is desired, as opposed to already formed. Second, bilateral (or mutual) links may actually be unilateral if there is some coercion to link formation, such as a binding social norm. We believe that the questions we used to elicit risk-sharing links were clear; enumerators did not report any difficulty in the interpretation of the IRSA questions. 26 Potential transfers are thus potential or hypothetical in four different ways that compound each other. First, as 8

10 To establish the pool of candidate individuals from which the respondent can identify her risksharing partners, we used a method which restricts the pool to those who are also in the study sample. We presented respondents with photos of women who were part of the research sample and who were in the same geographic cluster. 27 We then asked respondents to identify all of the women they knew, and of these, who were risk-sharing partners, as defined above. We call the risk-sharing partners generated in this photo identification method in-sample partners. The benefits to focusing on these in-sample partners is centered around our ability to match experimental treatment assignments and survey responses of both the respondent and her risk-sharing partner. First, we have treatment status of both people in a risk-sharing pair, which allows us to test for treatment effects depending on whether both or only one in a pair is assigned to treatmet. Second, we have data on shock experience for both people in a pair, which allows us to test for effects on state-contingent transfers. Third, we have welfare measures for both people in a pair, allowing us to test for spillover welfare effects. Fourth, we have data on transfers as reported by both people in a pair, which allows us to test for effects on risk-sharing between a respondent s partner and her partner s partners. 28 One limitation to using in-sample partners is that we may be excluding other risk-sharing partners from the analysis. More importantly, the risk-sharing partners we exclude may be different from those that we include. This limits the external validity of the results; we are only able to infer effects on a subset of one s set of risk-sharing partners. However, the mutual or risk-sharing types of support relationships could be quite prominent in-sample. Because the women in-sample have already discussed, insurance is state-contingent; it is an agreement about potential transfers that can be triggered, not actual realized transfers. Second, informal insurance agreements have no written or binding contracts and are therefore difficult to enforce. Third, maximum insurance agreements only account for the highest amount one can receive or send, they do not account for the full schedule of insurance transfers that correspond to various types or sizes of shocks. Fourth, bilateral insurance agreements do not account for how many people one will actually receive support from or send support to, which may affect the actual transfers received or sent. All these reasons differentiate potential transfers from actual transfers. 27 On average, a geographic cluster had 23.2 individuals. The smallest geographic cluster had 5 individuals, while the largest had 42 individuals. Due to geographic proximity, for the photos, two clusters in the rural subsample were merged and two clusters in the urban subsample were merged. Effectively, the smallest cluster for the photos had 19 individuals. 28 As discussed above, we defined a pair of individuals ij as having a mutual suport relationship if individaul i reports it as such. We could have instead defined a pair to be mutual if both i and j have reported it as such. However, likely because of survey fatigue in the photo identification section of the survey, there are many missing reports of j regarding her relationship with i. This largely reduces the power in analyses which defines mutuality using both the reports of i and j. Recall that a respondent first had to identify the women whom she knew from a set of photos before we asked about the risk-sharing relationship. Respondents may underreport knowing someone from the set of photos in order to shorten the survey process. 9

11 similar incomes and wealth, they are less likely to form non-mutual charitable support relationships. Further, we focus on the effects of savings on bilateral IRSAs, as opposed to effects on a group or network IRSA. The latter requires reconstructing a complete risk-sharing network, which entails some census data of the full network and more detailed data on a random sample of the full network (Chandrasekhar and Lewis, 2011). Neither of these was within the scope of this study. Nonetheless, bilateral IRSAs are a relevant unit of analysis. Some studies have shown that smaller risk-sharing groups can be at least as efficient as larger ones (Chaudhuri, Gangadharan, and Maitra, 2010; Fitzsimons, Malde, and Vera-Hernandez, 2015; Genicot and Ray, 2003). 3 Descriptive statistics In this section we present a range of descriptive statistics. In section 3.1 we describe the sample of women and we show that this sample provides a relevant context to study the interaction of savings and risk-sharing. In section 3.2 we show that treatment women used the new M-PESA account and we highlight the effect of treatment on savings. In section 3.3 we briefly describe the set of risk-sharing partners and the level of risk-sharing between risk-sharing partners. 3.1 Sample of vulnerable women The urban subsample consisted of FSWs, and the rural subsample consisted of women who were deemed to be at high-risk of entering into sex work. Although these women were targeted primarily to study risky sexual behavior, both subsamples of women represent useful populations on which to study the interaction of savings and risk-sharing. They are poor, exposed to a wide range of risks, and rely on informal exchanges to smooth consumption against shocks. Table 1 provides summary statistics for the full sample, and the urban and rural subsamples. The women are highly vulnerable: 66% of the women were severely food access insecure based on the Household Food Insecurity Access Scale or HFIAS (Coates, Swindale, and Bilinsky, 2007). About 70% of the women were either widowed or divorced, and only 40% had more than primary education. On average, women earned 1,648 Ksh per week from income generating activities. 29,30 29 Throughout the paper, we use Kenyan Shillings (Ksh) for all monetary values. The exchange rate at the time of the study was 1 USD=85 Ksh 30 About 40% of the women consider some form of small business as their primary activity, such as selling food products. About 40% of women in the rural subsample are involved in farming activities, while none of the women 10

12 Women in the urban subsample had a higher value of total assets compared to those in the rural subsample, although as expected, women in the rural subsample held more livestock assets (18,435 Ksh) than those in the urban subsample (3,893 Ksh). Because women in the sample had some access to savings and credit at baseline, we interpret our savings intervention as an improvement in access to vehicles that enable liquid savings. On average, a woman in the sample could cover up to 793 Ksh of an emergency expense using personal funds, and total balance across various savings accounts was 2,249 Ksh. The women used a variety of tools to save. About 75% of the women participated in a rotating and savings credit association or ROSCA, 93% had an existing M-PESA account, 11% had another mobile banking account, 24% had a formal bank account, and 33% had savings that were kept at home or with a friend or relative. 31 Moreover, 57% of the women had taken at least one loan in the past 12 months before baseline, and most of these were informal loans from family and friends. Informal transfers were also important; 94% of the women claimed they could rely on at least one person for financial support in case of an emergency expense. Over a 3-month period prior to the intervention, a respondent received $37 and sent $13 on average. Many, but not all, of these transfers were for consumption smoothing. For example, the transfers one received for large and unexpected expenses represented only about half of the total transfers received. 32 Table 2 provides summary statistics on the negative shocks that women experienced over a 7-month period after the intervention, as well as the methods they used to cope with these shocks. About 38% of the women experienced a financially challenging sickness or injury. Arguably, negative health shocks are not highly correlated between risk-sharing partners, and are thereby ideally smoothed out through IRSAs. The median cost to treat a health shock was 350 Ksh (200 Ksh) for women in the urban (rural) subsample. 33 Although the cost of these health shocks seem small, in the urban subsample are. 31 Having an existing M-PESA account was part of the sampling criteria, which explains why we observe almost universal use of M-PESA at baseline. Other mobile banking accounts included mobile money platforms from other mobile service providers. 32 We consider medical, wedding, funeral, or food consumption expenses as large or unexpected. Food requirements are not unexpected, however, if a household is unable to meet its food needs, the situation generally qualifies as an emergency. Not considered as transfers for shocks are: education expenses, inputs for agricultural production, investment in business, purchase of durable good, rent payments, inheritance, repayment or compensation of earlier debt, and transfers with no particular reason. 33 The mean cost to treat a health shock was 880 Ksh (408 Ksh) in the urban (rural) subsample. The mean cost accounts for larger health expenses, while the median cost may represent the cost of smaller and more frequent health shocks. One possible bias to self-reported cost of health treatment is that we usually do not observe the actual health treatment cost for individuals who were not able to afford the cost. As such, we had also asked respondents whether 11

13 they pose a potentially large problem as women who engage in transactional sex have been shown to engage in riskier sexual behavior to cope with such shocks (Robinson and Yeh, 2011). Food price shocks were also common, but these shocks are likely to be correlated between risk-sharing partners, and are unlikely smoothed out through IRSAs. The women used a variety of methods to cope with shocks. The most common coping mechanisms were borrowing money, seeking assistance from others, and relying on own savings. While a variety of coping mechanisms exist, women were unable to fully shield themselves from shocks: 23% (16%) of the shocks experienced by women in the urban (rural) subsample resulted in a reduction of expenses. Moreover, women took no action to cope with 9% (27%) of the shocks experienced by women in the urban (rural) subsample. Although the urban and rural subsamples may present interesting differences with respect to the nature of shocks and coping mechanisms, the sample is not large enough to analyze how the effect of access to savings may be different across these subsamples. Thus, throughout the analysis in this paper, we pool the these subsamples. 3.2 Treatment take-up We describe the use of the new M-PESA account using administrative records from Safaricom. Figure 3 shows the cumulative proportion of the treated sample that had used the new account at least once since the beginning of treatment. By June 2014, the end of the intense intervention period, 62% had used the account at least once (70% in the rural sample and 56% in the urban sample). This take-up is comparable to other microsavings interventions. For example, after one year, active usage of a formal bank account was 39% in Chile (Kast and Pomeranz, 2014) and 80% in Nepal (Prina, 2015), while usage of a simple lockbox in western Kenya was 71% (Dupas and Robinson, 2013). 34 Figure 4 shows the daily balance averaged across individuals who had used the new M-PESA account at least once. The daily mean balance was sharply growing in the beginning of the interthey had an unmet need and how much this unmet need would have cost them. Only 3% of those who experienced a health shock were unable to meet the health expense, and the median and mean unmet health costs were roughly double the health treatment costs for those who were able to meet such expenses. 34 Active usage is defined differently in each of these studies. Kast and Pomeranz (2014) defined active usage as depositing more than the minimum account deposit, Prina (2015) defined active usage as making at least 2 deposits in one year, and Dupas and Robinson (2013) defined usage as having a non-zero amount in the lockbox. 12

14 vention, and it peaked during the intense intervention period. In June 2014, mean balance was 526 Ksh for those that ever used the account. The mean balance in the account did not fall to zero even after the intense intervention period when transactions costs were no longer zero. For example, about nine months after the initial intervention, the mean balance was 200 to 250 Ksh, which was roughly the median cost of treating a health shock. Beyond the provision of a new labeled M-PESA account, the intervention included setting saving goals and receiving weekly SMS reminders on these goals. All treated women set at least one savings goal. Treatment women in the urban (rural) subsample set 1.3 (1.6) goals on average, where the average goal amount was 38,595 Ksh (15,523 Ksh), the median goal amount was 20,000 Ksh (7,500 Ksh), and the average time to complete one goal was 67 (52) weeks. Treatment women in the urban (rural) subsample also committed to set aside 130 Ksh (80 Ksh) on average each week for emergency expenses. The treatment had a positive (but imprecisely estimated) effect on savings. The program did lead to a statistically significant increase in savings for those who reported having problems saving due to spending on temptation goods. Those who faced temptation constraints saw an over threefold increase in mobile banking savings due to the intervention (Dizon, Gong, and Jones, 2015). 3.3 Risk-sharing Figure 5 presents a histogram of the number of baseline risk-sharing partners against the number of non-risk-sharing financial support partners or charitable out partners. Charity-out partners are defined as those who could rely on the respondent for support, but who the respondent could not in turn rely on for support. Of the women in the sample, 33% had no in-sample risk-sharing partners, 31% had one, 18% had two, 8% had three, and 10% had more than three. In contrast, 70% of the women in the sample had no charity-out partners. 35 Figure 5 presents summary statistics on potential transfers one could receive and send across various types of financial support partners. The average amount that one could receive from and send to an in-sample risk-sharing partner was 400 Ksh, while the average amount that one could send to an in-sample charitable-out partner was 122 Ksh. The average potential transfers between 35 Note that charitable support could also flow in the opposite direction: someone from whom the respondent could receive support from but to whom she would not send support. However, these are only reported by 3% of the women, likely due to reporting bias. 13

15 in-sample risk-sharing partners was roughly double the median cost to treat a health shock, and half of the maximum emergency cost one could have self-financed. 4 Effect on risk-sharing In section 4.1 we discuss our estimation strategy, in section 4.2 we present our estimates of the effect of access to savings on risk-sharing, in section 4.3 we separate our estimated effect into an intensive and extensive margin effect, and in section 4.4 we discuss alternative explanations of our result. 4.1 Estimation strategy To measure the effect of access to liquid savings on bilateral risk-sharing, we estimate RS ij = α + γt i + X iδ + ɛ ij (1) where RS ij is risk-sharing at endline between individual i and her risk-sharing partner j. We use two measures of RS ij. The first measure of risk-sharing is potential transfers, defined as the maximum amount one can receive from (send to) a risk-sharing partner in case she (her partner) experiences an emergency. Potential transfers is our key measure of mutual insurance, an ex-ante or pre-shock concept. For comparison, we use actual transfers as a second measure of RS ij. Actual transfers is the total amount one received from (sent to) a risk-sharing partner during the four months prior to endline, and as such is an ex-post or post-shock concept. The vector X i is the set of stratifying variables for treatment randomization, specifically age and 26 geographic cluster dummies. Our independent variable of interest is T i, which is a treatment assignment variable for individual i constant across individual i s set of partners js. The parameter of interest is γ, with ˆγ our intent-to-treat (ITT) estimate. The variable T i indicates that the individual was assigned to receive the treatment package: a labeled mobile money savings account, elicitation of savings goals and SMS reminders. Our ITT estimate would be very close to the treatment-on-treated (TOT) estimate since treatment compliance was 98.4%, where compliance is defined as having received treatment. We use Feasible Generalized Least Squares (FGLS) to estimate the parameters in equation (1), where we model the errors to be equicorrelated within-i. 36 We estimate standard errors as cluster- 36 Individual i fixed effects cannot be included because they would absorb the independent variable of interest, T i. 14

16 robust standard errors, where a cluster is an individual i. We follow the arguments of Cameron and Miller (2015) in our choice of estimation. First, we use FGLS to estimate the parameters because FGLS is more efficient than OLS if errors are correlated within cluster. Second, we estimate cluster-robust standard errors to guard against the assumption we make on equicorrelated errors within cluster. Third, we do not cluster at the geographic cluster level because there is no reason to expect errors to be correlated within geographic cluster as our estimation controls for geographic cluster and treatment is randomly assigned at the individual i-level within each geographic cluster. Our sample includes duplicate risk-sharing pairs, such that both the pairs ij and ji are in the sample if j similarly reports i to be a risk-sharing partner. Including duplicate pairs increases statistical power by leveraging both the reports of i and j. Moreover, the results are robust when we use only the unique pairs. 37 There are three types of risk-sharing pairs in our data: (a) always risk-sharing pair i and j who were risk-sharing at both baseline and endline, (b) newly formed risk-sharing pair i and j who were risk-sharing at endline, but not at baseline, and (c) severed risk-sharing pair i and j who were risk-sharing at baseline, but not at endline. Severed risk-sharing pairs have zero value of potential and actual transfers in the four months prior to endline. 38 In the initial estimation presented in section 4.2 we include all three types of risk-sharing pairs, and as such we estimate a pooled effect which combines intensive and extensive margin effects; while in section 4.3, we disaggregate these intensive and extensive margin effects. We also discuss alternative specifications after presenting our initial estimates of the treatment effect. 4.2 Estimation results Table 3 presents our estimates of the effect of access to savings on risk-sharing. We find strong evidence that access to savings reduced risk-sharing. Results in specifications (1) to (4) show that assignment to treatment reduced potential transfers by 21-28% and reduced actual transfers by 70-78%. The sample of i s should consist of the same people as the sample of partners j, because duplicate 37 Of the 1,102 risk-sharing pairs in our data (as reported by individual i), 728 pairs form a set of unique risk-sharing pairs, while 374 are duplicate pairs. These numbers are balanced between treatment and control groups. There were 357 (371) unique pairs for control (treatment) group respondents, and there were 192 (182) duplicate pairs for for control (treatment) group respondents. 38 A risk-sharing tie could actually be severed or a respondent could simply forget to or fail to mention a specific connection. We cannot differentiate among these cases. In our analysis, all forgotten partners or partners that a respondent did not mention are treated as severed. 15

17 pairs are included. If self-reports of partners and transfers are accurate, then the amount that i reports to have received from a partner j should equal the amount that j reports to have sent to i. As such, the effect on transfers received should equal the effect on transfers sent. We do find that the effect on potential transfers one could receive and and send are similar, and the effect on actual transfers received and sent are similar. Moreover, using chi-square tests we fail to reject the null hypothesis that the ITT estimates in specifications (1) and (3) are equal and that the ITT estimates in specifications (2) and (4) are equal. 39 Additionally, we estimate equation (1) as a linear probability model and as pooled tobit model. We use a binary measure of actual transfers, where RS ij = 1 if any transfer was received (sent) in the four months prior to endline, and RS ij = 0 if otherwise. We re-estimate equation (1) as an FGLS linear probability model, and present the estimation results as specifications (5) and (6) in table 3. We find that the treatment reduced the probability of transfers between risk-sharing pairs by 4.5 percentage points, equivalent to a 34-53% decrease in the probability. In our study, actual transfers are only observed over a four month period. Risk-sharing transfers between a pair ij should be zero if the potential receiver of a transfer did not experience a shock in the four month period. Because of the short observation period, the actual transfers measures are then censored at zero. We re-estimate equation (1) as a pooled tobit model, and present estimations results as specifications (7) and (8) in table 3. We find much large negative treatment effects on actual transfers when we account for this censoring. Our results are robust to the following alternative specifications. First, we weight the dependent variable by one over the number of j partners for each given i, and estimate the same equation (1) using FGLS. This is akin to collapsing the data to the mean across js for each given i. These results are presented in web appendix table A1. Second, we collapse the data to the mean across js for each given i, creating an i-level dataset as opposed to a pair ij-level dataset. We estimate the equation using OLS, but for each observation i we use analytic weights equal to the number of js. This allows for the standard errors to account for the fact that each observation is a more precisely estimated mean as the number of js increases. These results are presented in web appendix table A2. Third, 39 We run a seemingly unrelated estimation (SUE) of the specifications we are comparing, and then run a postestimation chi-square test for the equality of the treatment effect across the two specifications. This accounts for the correlation of the estimators across the two specifications. However, because we cannot run the SUE on an FGLS model, we instead run the SUE using a pooled OLS model with errors clustered at the individual i level. Results are not presented for brevity, but available upon request. 16

18 using the pair ij-level dataset, we estimate the treatment effects using OLS with inverse sampling probability weights, where the probability that each individual i is sampled is proportional to the number of partners j for each i. These results are presented in web appendix table A3. Fourth, we treat a dyad as the unit of observation. As such, we eliminate duplicate dyads and use the sum of reports of individual i and j as the outcome variable. 40,41 These results are presented in web appendix table A Intensive vs extensive margin effects We have uncovered large and significant negative effects on risk-sharing. In this section, we separate the estimated treatment effect into intensive and extensive margin effects Intensive margin To evaluate the intensive margin effect we re-estimate equation (1) but only among pairs that were risk-sharing pairs at both baseline and endline (always risk-sharing pairs). This eliminates the negative extensive margin effect from severed risk-sharing pairs and the positive extensive margin effect from newly formed risk-sharing pairs. Estimation results of the intensive margin effect are presented in table 4 using an FGLS model, an FGLS linear probability model, and a pooled tobit model. The results from this much smaller sample of ij pairs are similar to the results from the sample which included the three types of ij pairs, suggesting that the intensive margin effect was at least partially driving the pooled effect earlier estimated Extensive margin We have not addressed the fact that treatment may have induce changes in the composition of the set of partners. The work of Comola and Prina (2015) identifies the bias introduced in estimating peer effects in the presence of treatment-induced changes in network composition. Such bias will play a smaller role in the estimations that we had presented in section 4.2 because we included three types of pairs: always, severed, and newly formed risk-sharing pairs. The pooled effect we earlier 40 We include pairs where either i or j reports mutuality, so that the number of unique risk-sharing dyads is 801 as opposed to 728 when we only allow individual i to report mutuality of a given pair ij. 41 The sum would likely be lower for pairs where j did not voluntarily report transfers with i, that is where there is only one report for a given pair ij. Using the sum (as opposed to the mean) thus allows for the flow of transfers to be larger when both in a pair report it, as opposed to only one. 17

19 estimated already accounted for some treatment-induced network changes. However, we have not accounted for pairs that were never risk-sharing (i.e. those who were risk-sharing partners neither at baseline nor at endline). 42 Moreover, the severance and formation of risk-sharing links is an interesting question on its own. Similar to Comola and Prina (2015) we test for treatment effects at the extensive margin using two strategies. Our first strategy is to estimate the following equation C i = α + ρt i + X iδ + ɛ i (2) where C i is a measure of the number of risk-sharing partners. We use two measures for C i. First, we let C i be an indicator variable for whether individual i had at least one risk-sharing partner and estimate equation (2) using a linear probability model. Second, we let C i be the number of risk-sharing partners for individual i and estimate equation (2) using OLS with heteroskedasticityrobust standard errors. As before, the vector X i is the set of stratifying variables for treatment randomization. Table 5 presents the results of these estimations as specifications (1) and (2). We find that the treatment reduced the probability of having at least one risk-sharing partner by 8.1 percentage points, equivalent to a 13% decrease in the probability. The estimated treatment effect on the number of partners is similarly negative, but small and statistically insignificant. Because we had only included individuals who had at least one risk-sharing partner in the estimations from section 4.2, the negative extensive margin effect we uncovered here suggests that the earlier estimates were biased upwards. That is, the true negative effect on risk-sharing is larger. 43 The second strategy we use to measure the extensive margin effect is to estimate the probability of forming a link using dyadic regressions. Instead of using the sample of risk-sharing partners, we use a larger sample of dyads. We define a dyad ij as any pair who knew each other within the same 42 Similarly, because our sample in section 4.1 only included individuals i who had at least one risk-sharing partner, we might have had a biased estimate of the effect on risk-sharing if the probability of having at least one risk-sharing partner was affected by the treatment. In this section, we show that the treatment indeed affected the probability of having at least one risk-sharing partner, but it affected it negatively. Thus, the estimates in section 4.1 are biased upwards. 43 We had also estimated equation (2) where C i was instead defined as the mean of a given characteristic (i.e. gender) across all partners j for individual i. This allows us to test whether the type of people that comprises one s set of partners changed. We used arguably time-invariant j characteristics because the goal was to estimate treatment effects on the identities of the partners, as opposed to treatment-induced changes in the quality of the relationship between i and j. We find no treatment effects on attending the same church, relationship, wealth or subjective status in community. Thus, although the probability of having at least one partner was negatively affected by treatment, the type of people that formed one s set of partners was unaffected. 18

20 geographic cluster. We then test for the treatment effect on the probability of forming a risk-sharing link among the ij pairs who knew each other, by estimating the linear probability model L t ij = α ij + δ(t = 1) + ρ 1 D(T i = 1 or T j = 1) + ρ 2 D(T i = 1 and T j = 1) + ɛ ij (3) where L t ij equals one if individual i and j were risk-sharing partners in time t, and zero if otherwise. Following standard practice on dyadic regressions, we assume symmetry by imposing L t ij = Lt ji, where any instance that L t ij Lt ji is assumed to be reporting error on the part of either i or j. We assume L ij = L ji = 1 if at least i or j report a risk-sharing link, and zero if otherwise; we delete any duplicate dyads from the dataset. 44 We pool two time periods, baseline (t = 0) and endline (t = 1), and include a time trend dummy which equals one if t = 1, and zero if otherwise. Our estimations include a dyad fixed effect α ij. Estimation results for equation (3) are presented in table 5 specification (3). The probability of forming a risk-sharing link (net of severing a link) decreased by six percentage points when exactly one person in the pair was assigned to treatment, and decreased by nine percentage points when both people in a pair were assigned to treatment; this is equivalent to a 16% decrease in the probability of forming a risk-sharing link. These dyad level estimates echo the results from i-level regressions. Our estimations of the extensive margin effect suggest two things about the pooled effect earlier estimated in section 4.2: it is at least partially driven at the extensive margin, and it may be biased upward. Thus far, our results suggest that the effect of access to savings has a sizable negative effect on risk-sharing. The extensive margin effect shows that some of the links between risk-sharing partners are fully severed. The intensive margin effect shows that for those links that were not severed, the amount of risk-sharing that remains in the relationship is also reduced. 4.4 Supporting evidence We have interpreted our estimates as the effect of access to savings on risk-sharing, and we posit that this negative effect might be explained by the limited commitment problem in IRSAs or by the exacerbation of this limited commitment problem when access to savings is introduced. Here, 44 For the estimations in section 4.2, including all dyads ij and ji was appropriate because a transfer sent, RS, was such that the amount sent by i to j was not the same as the amount sent by j to i, that is RS ij RS ji. 19

21 we provide further evidence to support our interpretation of our findings. First, in sections and we test whether savings affected other interpersonal support relationships or other types of transfers. If access to savings only affected risk-sharing arrangements and only state-contingent transfers, then the limited commitment story is more likely. Second, in section we test whether the treatment might have altered interpersonal relationships because treatment increased access to savings for some, but not for others. If access to savings negatively affected risk-sharing pairs regardless of whether both were or only one was treated, then the limited commitment story is more likely Charitable support pairs Did treatment only affect risk-sharing pairs or did it also affect other types of financial support relationships? To answer this question, we estimate the treatment effect on pairs who had a charitable support relationship, those pairs where only either i or j could rely on the other person for support, but not vice-versa. Where i is the reference individual, we call those where i could receive support from j charity-in pairs, and those where j could receive support from i as charity-out pairs. We estimate the same equation (1), but instead use the sample of charitable-in and charitable-out pairs, as opposed to the sample of risk-sharing pairs. A key limitation is that our dataset contains very few in-sample charitable pairs. We thus leverage the data we collected about unrestricted partners, unrestricted in the sense that the respondent could report a partner who is not in-sample. To identify unrestricted pairs, we asked the respondent to name all of her financial support partners. 45 We estimate treatment effects on three types of pairs: in-sample charity-out, unrestricted charity-in, and unrestricted charity-out. 46,47 45 Although we had asked the respondent to name all of her financial support partners, she was likely to name only some of these partners because of survey fatigue. She was more likely to mention top-of-mind partners, such as those to whom she was socially closer or those with whom she had a stronger financial support link. Using data from endline, we can infer that less than seven percent of unrestricted partners were also individuals in-sample. We consider this an upper bound, because respondents had the incentive to claim that an unrestricted partner was in-sample. Claiming that a partner was already in-sample meant that fewer survey activities would have been conducted with the respondent. 46 To ensure that the sample of charity-in, charity-out, and risk-sharing pairs form mutually exclusive groups, we define charity-in pairs as pairs which were charity-in at both baseline and endline, and define charity-out pairs as pairs which were charity-out at both baseline and endline. 47 Web appendix figure A1 presents the distribution of the number of baseline unrestricted charitable support partners; about 42% (19%) of the women had at least one unrestricted charity-in (charity-out) partner. At baseline, the average amount that one could receive from and send to an unrestricted charitable support partner were 1,713 Ksh and 960 Ksh, respectively. 20

22 The estimation results are presented in table 6. Across all these subsamples of charitable support pairs, we find no evidence that the treatment affected potential or actual transfers. This suggests that treatment reduced transfers between risk-sharing pairs, but not between other types of support pairs State-contingent transfers In this section we present evidence that the estimated impacts are specific to state-contingent transfers, rather than other transfers that may occur between risk-sharing partners. We separately estimate treatment effects on those who experienced a negative shock, and those who did not. We estimate the following equation RS ij = α + γ 1 (T i S i ) + γ 2 (T i S 0 i ) + βs i + X iδ + ɛ ij (4) where RS ij is actual transfers received by i from j, and S i is a dummy variable equal to one if individual i experienced a negative shock in the past four months, and zero if otherwise. The dummy variable Si 0 is the opposite of the S i dummy; Si 0 is equal to one if individual i did not experience a negative shock in the past four months. Thus, γ 1 is the treatment effect on those who experienced a negative shock, γ 2 is the treatment effect on those who did not experience a negative shock, and β is the effect of a negative shock on transfers received. We also estimate the following closely related equation RS ij = α + γ 1 (T i S j ) + γ 2 (T i S 0 j ) + βs j + X iδ + ɛ ij (5) 48 In web appendix table A6 we present estimates of the treatment effects on the sample of unrestricted risk-sharing partners. The estimated effects are statistically insignificant. We offer two explanations for why we estimate negative statistically significant effects on risk-sharing for in-sample partners, but not for unrestricted risk-sharing partners. First, the sample of unrestricted risk-sharing partners may be more subject to measurement error in the sense that respondents may have reported that the support relationship is mutual, even if the relationship was not truly mutual. In web appendix figure A2 we show that the unrestricted risk-sharing partners hold a higher position in their community than the respondent i, suggesting that unrestricted risk-sharing partners were wealthier than individual i, and as such these reported risk-sharing pairs were more likely to be charity-in pairs. Second, unrestricted risk-sharing partners were socially closer to the respondent than the in-sample partners. In our study, 50% of unrestricted risk-sharing partners was a family member, while less than 10% of in-sample partners was. The social value of a relationship (or social proximity) has been widely shown to mitigate enforceability problems in IRSAs (See Angelucci, De Giorgi, and Rasul (2012); Attanasio et al. (2012); Chandrasekhar, Kinnan, and Larreguy (2011, 2014); Fafchamps and Lund (2003); Kinnan and Townsend (2012); Ligon and Schechter (2012)). If limited commitment in ISRAs is the reason why personal savings crowds them out, then it is clear why this happened to a greater extent for in-sample risk-sharing partners. 21

23 where RS ij is actual transfers sent by i to j, and S j is a dummy variable equal to one if the partner j experienced a negative shock in the past four months, and zero if otherwise. We use equations (4) and (5) to test for two things. First, we test for the relevance of statecontingent transfers. If β > 0 then a person receives more transfers if she experienced a negative shock than if she did not. Second, we test whether treatment reduced state-contingent transfers. If γ 1 < 0 then treatment of i reduced the transfers she received if she experienced a negative shock, or state-contingent transfers. If γ 2 < 0 then treatment of i reduced the transfers she received if she did not experience a negative shock, or transfers that were not state-contingent. We use two measures of negative shock experience. The first measure is a a binary indicator equal to one if the individual s household experienced any of the following financial challenges in the four months prior to endline: illness or injury, death, birth, loss of job, high food prices, low price of items sold, theft, destruction to assets, legal problems, conflict, loss of crops or livestock sickness or death. We call this measure any shock. The second measure is a binary indicator equal to one if the individual s household experienced a financially challenging illness or injury in the four months prior to endline. We call this measure a health shock. For completeness, we present results using both measures. However, we find the health shock measure to be more relevant than the any shock measure, because the any shock measure includes covariate shocks that were not likely smoothed through IRSAs. Table 7 presents estimation results for equations (4) and (5). Focusing on results from equation (4) (see column 3), we find that a negative shock increased transfers received, suggesting that we are in fact measuring state-contingent transfers. Moreover, treatment reduced transfers i received only in the case where i experienced a negative shock, suggesting that treatment reduced state-contingent transfers between risk-sharing pairs, and not other types of transfers. Focusing on results from equation (5) (see column 4), we similarly find that treatment reduced transfers sent to j if j experienced a shock. However, treatment also reduced transfers sent to j even if j did not experience a shock, and the effect of a shock of j on transfers sent to j was instead negative and statistically insignificant. It is puzzling that the transfers sent to j, as reported by i, was unresponsive to the shock experience of j, as reported by j. A straightforward explanation is that the behavior of i was unresponsive to the shock of j, because such shocks may be imperfectly observed by i. This cannot be the case because the sample of is should consist of the sample of js, 22

24 apart from misreporting. As such, measurement error should explain the difference in the effect of the shock of i on transfers received by i and the effect of the shock of j on transfers sent to j, as reported by i. 49, Difference in treatment between a pair Did treatment affect a risk-sharing pair similarly regardless of whether both were or only one was assigned to treatment? Because treatment was randomly assigned at the individual level, we are able to exploit the random treatment assignment both to i and to each of i s risk-sharing partners j. We estimate the following equation RS ij = α+γ 1 D(T i = 1andT j = 1)+γ 2 D(T i = 1andT j = 0)+γ 3 D(T i = 0andT j = 1)+X iδ+ɛ ij (6) where D(T i = 1andT j = 1) equals one if both i and j are in the treatment group, D(T i = 1andT j = 0) equals one if i is in the treatment group but j is in the control group, and D(T i = 0 and T j = 1) equals one if i is in the control group and j is in the treatment group. Thus, γ 1 is the treatment effect if both individuals in a pair were assigned to treatment, γ 2 is the treatment effect if individual i was assigned to treatment, and γ 3 is the treatment effect if individual j was assigned to treatment. Estimation results are presented in table 8. We find that the treatment effect was the same whether both were or only one was assigned to treatment. This suggests that the treatment effect was not driven by discordant treatment status for a risk-sharing pair. 51,52 We, however, find some 49 A second possible explanation for the lack of effect of a shock was the difference in sample size for equations (4) and (5). The sample size slightly drops for equation (5), because endline attrition compounds when we have to match data reported by i with the data reported by j. We had re-estimated equation (4) using only the sample of 988 pairs used to estimate equation (5), and the results hold. 50 A possible explanation for the lack of differential treatment effect by shock was the difference in the treatment variable for equations (4) and (5). In equation (4) we estimated the effect of treatment of i on transfers received by i, so that the receiver was the treated person; whereas in equation (5) we estimated the effect of treatment of i on transfers received by j, so that the sender was the treated person. Re-estimating equation (5) using treatment of j is unlikely to change the results because, as shown in section (4.4.3), the treatment of j did not affect transfers sent to j, as reported by i. 51 The sample size in table 8 is 1035 while the sample in table 3 is This difference is due to enumerator entry error in photo IDs so that we cannot recover the treatment assignment of the partner j that individual i was referring to. As a robustness check, we had run the base estimations in table 3 using only the sample of 1035 pairs. The results are unchanged. 52 Both those in the treatment and control groups attended group sessions to discuss the importance of savings. Thus, another potential effect of the intervention was that the group sessions could have increased social interactions and risk-sharing activity. This is unlikely because the negative treatment effect applied to both the case where both in a pair were treated and the case where only one was treated. Moreover, we directly estimate the effect of attending 23

25 evidence for a difference in treatment effect on actual transfers sent to j if both are treated versus if only j is treated. This is largely driven by differences in the treatment effect of i and j, which we discuss further below. Our estimations have focused on the effect of treatment of individual i. Here, we also find that treatment of individual j negatively affected transfers received and sent, as reported by individual i. This suggests that treatment reduced risk-sharing whether the receiver or the sender was treated. Indeed, we do not expect the treatment effect to differ whether i or j was treated because an IRSA is a mutual exchange relationship. But we find that the effect of treatment of j on potential transfers sent to j was smaller (in absolute value) than the effect of treatment of i, and the effect of treatment of j on actual transfers sent to j was instead positive and statistically insignificant. We suggest two overlapping explanations. First, individual i may be more likely to respond to own treatment than to the treatment of individual j, as the latter is imperfectly observed by i. Second, measurement error may be playing a key role, as we had earlier suggested it did for the null effect of the shock of j on transfers received by j (see section 4.4.2). If j had improved access to savings, it may be easier for i to report that she was less dependent on j than to report that she was less willing to provide support to j. 5 Spillover effect on welfare We have shown that improved access to savings reduced risk-sharing. A reduction in risk-sharing may reduce welfare if individuals do not fully compensate with other means of risk-coping. As such, a reduction in risk-sharing is more likely to reduce welfare for those who do not have improved access to savings. We test for welfare spillover effects on the risk-sharing partners who were assigned to the control group. We estimate the following equation Y ij = α + γt i + βy 0 ij + X iδ + ɛ ij (7) where Y ij is an indicator of welfare at endline for a risk-sharing partner j who was assigned to the control group, and T i is treatment assignment of individual i. We include the baseline value of the the same group session on risk-sharing. In web appendix table A7 we show that pairs that attended the same session increased, not decreased, risk-sharing. However, we do not place much value on these results, because the choice of which training session to attend was endogenous. 24

26 welfare variable Yij 0 as a regressor, making equation (7) an analysis of covariance (ANCOVA) model. We use four different measures of the welfare of j. First, we use a binary indicator equal to one if individual j is categorized as food secure or only mildly food insecure, as opposed to being moderately or severely food insecure based on the HFIAS (Coates, Swindale, and Bilinsky, 2007). The HFIAS module measured food insecurity during the four weeks prior to the survey date. 53 Second, we use the number of meals on the day prior to the survey date for individual j. Third, we use a binary indicator equal to one if individual j reports that she had enough to spend on non-food items in the four weeks prior to the survey date. 54 Fourth, we use a subjective measure of the person s overall financial situation measured on a five-point scale ranging from negative two to positive two. For binary outcome variables, we estimate equation (7) as a linear probability model. Estimation results for equation (7) are presented in table 9. Across all the welfare indicators, we find no evidence that the treatment of individual i affected the welfare of her risk-sharing partners j who were in the control group. 55,56 We additionally estimate welfare spillover effects separately for the js who experienced a negative health shock and for those who did not; results are presented in the bottom panel of table 9. We do not find evidence for negative welfare spillovers regardless of whether the risk-sharing partner did or did not experience a negative health shock. This is unsurprising since we also did not find differential effects on the transfers sent to j by the shock experience of j. We do find that a negative health shock had a statistically significant negative effect across all the welfare indicators; suggesting that our welfare measures are relevant, as they are sensitive to negative health shocks. We explore two possible explanations for the lack of spillover effects on welfare by leveraging aspects of the risk-sharing arrangements in our data. First, in section 5.1 we show that the reduction in risk-sharing was larger for those with fewer risk-sharing partners; however, we still do not find evidence for reduced welfare even among those who experienced larger reductions in risk-sharing. 53 The HFIAS measures food insecurity along three domains: anxiety, quantity and quality. 54 The survey question was: In the past 4 weeks, did you have enough to spend on non-food items like clothes, medication, ceremonies etc? 55 A conventional peer effects equation will measure effects at the i-level, Y i = α + γ T j i + βy i 0 + X iδ 1 + ɛ ij, where T j i the share of i s risk-sharing partners j that were assigned to treatment, and Y i a welfare measure for individual i. We estimate this conventional peer effects equation among the is who were assigned to the control group. We present the results in web appendix table A9; these estimations similarly fail to provide evidence of spillover welfare effects. 56 We had also looked at alternative welfare indicators such as diet diversity, subjective status in community, and the probability of removing someone from school due to lack of money to pay fees. We also do not find evidence of welfare spillover effects using these measures. 25

27 Second, in section 5.2 we show that treatment increased risk-sharing between partners of partners, suggesting one way by which individuals mitigated the treatment-induced reduction in risk-sharing. 5.1 Effect by number of partners The negative effect on bilateral risk-sharing may be different depending on the number of risksharing partners. We test whether the effect on bilateral risk-sharing was affected by the number of immediate risk-sharing partners, or what is known in the network literature as the number of i s partners with whom path length equals one. We estimate the following equation RS ij = α + γ 1 (T i Net 1 i ) + γ 2 (T i Net +1 i ) + βnet 1 i + X iδ + ɛ ij (8) where Net 1 i equals one if individual i had one risk-sharing partner, and zero otherwise, and Net+1 i equals one if individual i had more than one risk-sharing partner, and zero otherwise. Estimation results are presented in table 10. We find that the reduction in risk-sharing is negative and statistically significant only among those who had one risk-sharing partner. Moreover, this difference in effect is statistically significant for the potential transfers measures; that is, we reject the null hypothesis that γ 1 = γ 2. One potential explanation is that the total reduction in risk-sharing is the same for each treated i, and thus the bilateral reduction is smaller for i s who have more risk-sharing partners j. In web appendix table A10, we present results where we instead estimate a heterogeneous treatment effect term that is linear in the number of partners. We find that the negative treatment effect is reduced by 17% for each unit increase in the number of risk-sharing partners. 57 Because the reduction in risk-sharing was largest for an individual j who was connected to a partner i who had only one risk-sharing partner, we separately estimate the welfare spillover effects on j by whether the partner i had one or more than one risk-sharing partners. Results are presented in web appendix table A11; we do not find evidence for reduced welfare regardless of the number of risk-sharing partners of i. 57 We similarly estimate equation (8), but instead using the number of partners of individual j. We do not find evidence for differential effects of the treatment of individual i by the number of the partners of individual j. 26

28 5.2 Effect on partners of partners We test whether treatment affected risk-sharing between partners of partners. We estimate the following equation RS ijk = α + γt i + X iδ + ɛ ij (9) where RS ijk is risk-sharing between j and j s set of risk-sharing partners k, as reported by j, and T i is treatment assignment of i. Individual i is directly connected to j in an IRSA, and individual j is directly connected to k in an IRSA; but, individual i is only connected to k through individual j, and by construction i k. For each j we reduce the observations from each partner k into a single summary statistic in order to simplify the analysis and maintain comparability with previous estimations. We use two measures of risk-sharing RS ijk between j and k. First, for each j, we calculate the mean across k s of potential transfers received and sent. Second, for each j, we calculate the sum across k s of actual transfers received and sent. Thus, each observation is still a pair ij, but the outcome variable is risk-sharing between j and k, not between i and j, while the treatment variable is treatment of i. Estimation results are presented in table 5.2. We find that treatment increased the mean potential transfers received and sent by 15-17%, and increased the total actual transfers received and sent by 52-59%. As i gained improved access to savings, she reduced risk-sharing with j, and j in turn increased risk-sharing with k. 58 Combined with the earlier result that the negative treatment effect was concentrated among those with only one-risk sharing partner, it seems that the negative effect of access to savings on risk-sharing was partially offset by the existence of other risk-sharing partners We expect that the treatment of i increased risk-sharing between j and k, particularly if j and k were in the control group. Thus, in web appendix table A12, we present estimates of equation 9 but only among the ijk triads where both j and k were in the control group. We find a similarly positive effect of the treatment of i on risk-sharing between j and k, but the estimates are statistically insignificant likely due to the small sample size. 59 Where j is a control individual, we do find some evidence that the higher the number of jk pairs, the lower the transfers received by j from k. One explanation for this is that individuals rely on each single person less if she has more people to rely on. This result is consistent with the results presented in table 10: our earlier result in section 5.1 did not imply that having more risk-sharing partners increased risk-sharing, but rather implied that having more risk-sharing partners mitigates the bilateral negative effect of increased access to savings. 27

29 6 Conclusions Combining a randomized controlled trial of a microsavings intervention with rich data on risksharing links and risk-sharing activity, we estimate the effect of access to liquid savings on informal risk-sharing arrangements. Between risk-sharing pairs, access to savings reduced potential transfers by percent and reduced actual transfers by percent. At the extensive margin, we further find that access to savings reduced the probability of forming (net of severing) a risk-sharing link by 16 percent, suggesting that some risk-sharing links are fully severed. We do not find evidence for negative effects of access to savings either on transfers between non-risk-sharing pairs, or on non-state-contingent transfers between risk-sharing pairs. This suggests that the negative treatment effect was unique to risk-sharing arrangements. But, despite the reduction in risk-sharing, we do not find evidence for treatment spillover effects on the welfare of risk-sharing partners. We find that those who did not receive the savings treatment increased risk-sharing with other partners if they had a risk-sharing partner who received the savings treatment, suggesting one way by which the women might have coped with the reduction in risk-sharing. We highlight a few other possible explanations for why reduced risk-sharing did not translate into negative spillover effects on welfare. First, an improvement in access to savings may also have some positive spillovers on welfare, a phenomenon documented in Nepal by Comola and Prina (2015) and in Malawi by Flory (2011). Moreover, even though we observed a reduction in risk-sharing, the negative welfare effects may have been offset by other responses to cope with shocks (Townsend, 1994). Because positive spillovers may have occurred and because individuals may have found other means to cope with shocks, it is not surprising that we observe a net zero impact on the welfare of risk-sharing partners even if risk-sharing was reduced. Second, as insurance is reduced, individuals may be sacrificing risky productive investments, thereby decreasing income in the longer term (Dercon and Christiaensen, 2011). The negative welfare consequences of sacrificing productive investments may take some time to materialize, and as such we would fail to detect these effects over a short period. Third, it may be the case that the negative effect on risk-sharing that we document was sufficiently small relative to existing portfolios of risk-coping so that impacts on welfare were negligible. Indeed, our treatment was designed to increase one s capacity to independently cope with small shocks. Intuitively, a more substantial savings intervention with larger treatment effects 28

30 on savings may lead to larger crowding out of risk-sharing. Overall, our findings suggest that encouraging liquid savings can reduce participation in existing informal risk-sharing arrangements. Such potential unintended consequences should be taken into account when designing programs of this type. Policies that strengthen local exchange arrangements, such as formalizing rules and creating transparent systems (Beaman, Karlan, and Thuysbaert, 2014; Berhane et al., 2014), may address problems of limited commitment and thereby mitigate the negative effects we observed. Although we do not observe negative welfare spillovers of access to savings, we document a substitution away from informal risk-sharing arrangements and into formal savings. Whether more substantial savings programs may induce sufficient reductions in risk-sharing to negatively affect the welfare of risk-sharing partners remains an open question. Our research implies that exploring this question empirically may well be worth the effort and, more broadly, suggests that formal financial services can interact in complex and important ways with pre-existing informal and socially-embedded services. 29

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35 Tables and Figures Figure 1: Sample Structure 34

36 Figure 2: Study Timeline 35

37 Figure 3: Proportion That Adopted the Labeled Account 36

38 Figure 4: Balance in Labeled Account, Among Adopters 37

39 Figure 5: Number of Baseline Financial Support Partners 38

40 Figure 6: Mean Potential Transfers between Financial Support Partners 39