Does Financial Inclusion Exclude? The Effect of Access toSavings 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 interper-sonal 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 substi-tution can lead to a reduction in the capacity to manage risk. We estimate the effect of accessto savings on bilateral IRSAs using a randomized controlled trial of a microsavings initiative inKisumu, Kenya. Of a sample of 627 vulnerable women, half were randomly selected to receivea labeled mobile money savings account along with weekly reminders on savings goals. We findthat the savings intervention reduced informal risk-sharing, while it did not affect non-mutualinterpersonal transfer arrangements. The reduction in risk-sharing did not translate into nega-tive welfare effects. We find some evidence that individuals may have coped with the reductionin risk-sharing by increasing risk-sharing with other risk-sharing partners. Overall, our studysuggests that the design of initiatives aimed at improving access to microsavings should con-sider the reduction in informal risk-sharing, especially in contexts where people might fail tofind 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 KidiLuandaCommunity 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, anda UC Davis ARE Development Workshop. Research funding was provided by the Hewlett Foundation, IFPRI and theUC Davis Blum Center. All activities involving human subjects were approved by IRBs at IFPRI, Maseno Universityin 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

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 institu-

tions 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, if1For example, in 2013 alone, $31 billion was pledged globally to support financial inclusion (CGAP, 2015).2For example, in 2010, the Gates foundation provided $500 million to support microsavings initiatives.3Advancements 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 loweringthe costs to delivering effective savings technologies.

4Simply providing access to formal savings accounts has been shown to improve the ability to cope with shocksand one’s perceived overall financial situation (Prina, 2015).

5See, 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 andLund, 2003; De Weerdt and Dercon, 2006), and social proximity (Kinnan and Townsend, 2012; Attanasio et al., 2012;Chandrasekhar, Kinnan, and Larreguy, 2014).

6The ambiguous effect of savings on IRSAs in the context of limited commitment has also been derived by Fosterand Rosenzweig (2000) with borrowing allowed, by Ligon, Thomas, and Worrall (2002) with a simpler version, andby Gobert and Poitevin (2006) who allow for savings as collateral.

7The interaction of IRSAs and savings is part of a broader literature that looks at the interaction of IRSAs with

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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 arrange-

ments 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 experi-

enced 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 mu-

tuality 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 onIRSAs, 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); Mobarakand Rosenzweig (2012).

8For example, see: Chaudhuri, Gangadharan, and Maitra (2010); Fitzsimons, Malde, and Vera-Hernandez (2015);Genicot and Ray (2003)

9More specifically, in our study, a pair of individuals i and j are linked together in an IRSA if i would be willing tofinancially support j if j faces an emergency, and if j would be willing to financially support i if i faces an emergency.

10Similarly, 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

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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 21-28 percent and reduced actual transfers by 70-78 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 mobilemoney accounts, as opposed to traditional bank accounts.

11We study the direct effect of savings on welfare in a separate paper (Dizon, Gong, and Jones, 2015). Others havestudied 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 andPrina, 2015). We focus on welfare spillover effects on risk-sharing partners.

12Given the ubiquity of M-PESA agents in our study area, it is relatively easy for anyone in our study to accessthe funds in their labeled mobile savings account.

13The intervention in our study is similar to a “soft commitment” design, where savings is encouraged, but thereare 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 belocked-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 touse savings for unexpected emergencies.

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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,14Consistent 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.15Using 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 ofinterpersonal transfer arrangements, but the remaining transfer arrangements sustained a higher level of insurance.

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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 free16For a useful qualitative discussion on interpersonal exchange relationships in Kenya, see Johnson (2015).

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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 op-

posed 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 sub-

locations 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 treatment17During 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 SMSreminders, and these SMS reminders were sent monthly.

18Within both the T1 and T2 arms, we randomly assigned two types of weekly SMS reminders. This also did nothave an effect on savings balances (Dizon, Gong, and Jones, 2015).

19Using data from internal census activities, we can infer that as a result of the M-Pesa criteria for study eligibilitywe excluded 16% of the vulnerable women from the rural area and 23% from the urban area. It is likely that thesewomen are poorer than our sample which has access to M-Pesa. From an external validity standpoint, our resultswill not necessarily extrapolate to those worst off in the set of vulnerable women.

20Jack and Suri (2014) show that access to M-PESA improves risk-sharing by reducing transaction costs. In ourstudy, women in both the treatment and control groups in our study had initial access to M-PESA. We our thusstudying the effect of access to savings on risk-sharing, as opposed to the effect of M-PESA on risk-sharing. Ouranalysis of the effects on risk-sharing applies to a population which has better risk-sharing at baseline, relative to apopulation that does not have access to M-PESA.

21Kenya is divided into counties, then sub-counties, then locations, then sub-locations, then villages. There are 47

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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.23

2.2 Sampling and data collection

Sampling was conducted during December 2013 and January 2014. 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 2014. 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 fallsinto the Nyando and Kisumu Central sub-counties.

22Stratification by age was done through re-randomization. We repeated randomization 500 times. A subset ofthese 500 randomizations satisfied the pre-specified criteria that the differences-in-means test for the variable ageacross treatment and control groups must have p < 0.10. A randomly chosen realization was selected to be used asthe basis for treatment assignment.

23Treatment 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 acommunity group, and to have severe anxiety (using the GAD-7 measure).

24Among endline attritors we found only 6.7% of 178 baseline variables to be statistically significantly differentbetween treatment and control at p < 0.05. However, the sample of attritors is too small to rely on for comparisonof means between the treatment and control groups.

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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.26

25Comola and Fafchamps (2014) discuss two important issues that arise when using subjective survey questionsto elicit network links. First, when a respondent reports that a link exists, she may mean that a link is desired, asopposed to already formed. Second, bilateral (or mutual) links may actually be unilateral if there is some coercionto link formation, such as a binding social norm. We believe that the questions we used to elicit risk-sharing linkswere clear; enumerators did not report any difficulty in the interpretation of the IRSA questions.

26Potential transfers are thus potential or hypothetical in four different ways that compound each other. First, as

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To establish the pool of candidate individuals from which the respondent can identify her risk-

sharing 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 ex-

perimental 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 part-

ners 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 aretherefore difficult to enforce. Third, maximum insurance agreements only account for the highest amount one canreceive or send, they do not account for the full schedule of insurance transfers that correspond to various types orsizes of shocks. Fourth, bilateral insurance agreements do not account for how many people one will actually receivesupport from or send support to, which may affect the actual transfers received or sent. All these reasons differentiatepotential transfers from actual transfers.

27On average, a geographic cluster had 23.2 individuals. The smallest geographic cluster had 5 individuals, whilethe largest had 42 individuals. Due to geographic proximity, for the photos, two clusters in the rural subsample weremerged and two clusters in the urban subsample were merged. Effectively, the smallest cluster for the photos had 19individuals.

28As discussed above, we defined a pair of individuals ij as having a mutual suport relationship if individaul ireports 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 missingreports of j regarding her relationship with i. This largely reduces the power in analyses which defines mutualityusing both the reports of i and j. Recall that a respondent first had to identify the women whom she knew from aset of photos before we asked about the risk-sharing relationship. Respondents may underreport knowing someonefrom the set of photos in order to shorten the survey process.

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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

29Throughout the paper, we use Kenyan Shillings (Ksh) for all monetary values. The exchange rate at the time ofthe study was 1 USD=85 Ksh

30About 40% of the women consider some form of small business as their primary activity, such as selling foodproducts. About 40% of women in the rural subsample are involved in farming activities, while none of the women

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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, nega-

tive 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.31Having 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 othermobile service providers.

32We consider medical, wedding, funeral, or food consumption expenses as large or unexpected. Food requirementsare not unexpected, however, if a household is unable to meet its food needs, the situation generally qualifies asan 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 earlierdebt, and transfers with no particular reason.

33The mean cost to treat a health shock was 880 Ksh (408 Ksh) in the urban (rural) subsample. The mean costaccounts for larger health expenses, while the median cost may represent the cost of smaller and more frequent healthshocks. One possible bias to self-reported cost of health treatment is that we usually do not observe the actual healthtreatment cost for individuals who were not able to afford the cost. As such, we had also asked respondents whether

11

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 mecha-

nisms 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 inter-

they had an unmet need and how much this unmet need would have cost them. Only 3% of those who experienceda health shock were unable to meet the health expense, and the median and mean unmet health costs were roughlydouble the health treatment costs for those who were able to meet such expenses.

34Active usage is defined differently in each of these studies. Kast and Pomeranz (2014) defined active usage asdepositing more than the minimum account deposit, Prina (2015) defined active usage as making at least 2 depositsin one year, and Dupas and Robinson (2013) defined usage as having a non-zero amount in the lockbox.

12

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 between35Note 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

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

RSij = α+ γTi +X′iδ + εij (1)

where RSij is risk-sharing at endline between individual i and her risk-sharing partner j. We use two

measures of RSij . 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 RSij . 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 Xi is the set of stratifying

variables for treatment randomization, specifically age and 26 geographic cluster dummies.

Our independent variable of interest is Ti, 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 γ̂ our

intent-to-treat (ITT) estimate. The variable Ti 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-36Individual i fixed effects cannot be included because they would absorb the independent variable of interest, Ti.

14

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 be-

cause 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 duplicate37Of 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 were357 (371) unique pairs for control (treatment) group respondents, and there were 192 (182) duplicate pairs for forcontrol (treatment) group respondents.

38A risk-sharing tie could actually be severed or a respondent could simply forget to or fail to mention a specificconnection. We cannot differentiate among these cases. In our analysis, all forgotten partners or partners that arespondent did not mention are treated as severed.

15

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 RSij = 1 if any transfer was received (sent)

in the four months prior to endline, and RSij = 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,39We run a seemingly unrelated estimation (SUE) of the specifications we are comparing, and then run a post-

estimation chi-square test for the equality of the treatment effect across the two specifications. This accounts for thecorrelation of the estimators across the two specifications. However, because we cannot run the SUE on an FGLSmodel, we instead run the SUE using a pooled OLS model with errors clustered at the individual i level. Results arenot presented for brevity, but available upon request.

16

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 A4.

4.3 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.

4.3.1 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.

4.3.2 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 earlier40 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.41The 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 transfersto be larger when both in a pair report it, as opposed to only one.

17

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

Ci = α+ ρTi +X′iδ + εi (2)

where Ci is a measure of the number of risk-sharing partners. We use two measures for Ci. First,

we let Ci 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 Ci be the number of

risk-sharing partners for individual i and estimate equation (2) using OLS with heteroskedasticity-

robust standard errors. As before, the vector Xi 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 same42Similarly, 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-sharingpartner was affected by the treatment. In this section, we show that the treatment indeed affected the probability ofhaving at least one risk-sharing partner, but it affected it negatively. Thus, the estimates in section 4.1 are biasedupwards.

43We had also estimated equation (2) where Ci 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’sset of partners changed. We used arguably time-invariant j characteristics because the goal was to estimate treatmenteffects on the identities of the partners, as opposed to treatment-induced changes in the quality of the relationshipbetween i and j. We find no treatment effects on attending the same church, relationship, wealth or subjective statusin 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

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

Ltij = αij + δ(t = 1) + ρ1D(Ti = 1 or Tj = 1) + ρ2D(Ti = 1 and Tj = 1) + εij (3)

where Ltij 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 Ltij = Lt

ji,

where any instance that Ltij 6= Lt

ji is assumed to be reporting error on the part of either i or j. We

assume Lij = Lji = 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 αij .

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,44For 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 RSij 6= RSji.

19

we provide further evidence to support our interpretation of our findings. First, in sections 4.4.1

and 4.4.2 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 4.4.3 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.

4.4.1 Charitable support pairs

Did treatment only affect risk-sharing pairs or did it also affect other types of financial support rela-

tionships? 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 lever-

age 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

45Although we had asked the respondent to name all of her financial support partners, she was likely to nameonly some of these partners because of survey fatigue. She was more likely to mention top-of-mind partners, such asthose to whom she was socially closer or those with whom she had a stronger financial support link. Using data fromendline, we can infer that less than seven percent of unrestricted partners were also individuals in-sample. We considerthis 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 withthe respondent.

46To ensure that the sample of charity-in, charity-out, and risk-sharing pairs form mutually exclusive groups, wedefine charity-in pairs as pairs which were charity-in at both baseline and endline, and define charity-out pairs aspairs which were charity-out at both baseline and endline.

47Web appendix figure A1 presents the distribution of the number of baseline unrestricted charitable supportpartners; 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 1,713Ksh and 960 Ksh, respectively.

20

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.48

4.4.2 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

RSij = α+ γ1(Ti × Si) + γ2(Ti × S0i ) + βSi +X′

iδ + εij (4)

where RSij is actual transfers received by i from j, and Si 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 S0i is the opposite of the Si dummy; S0

i is equal to one if individual i did not

experience a negative shock in the past four months. Thus, γ1 is the treatment effect on those who

experienced a negative shock, γ2 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

RSij = α+ γ1(Ti × Sj) + γ2(Ti × S0j ) + βSj +X′

iδ + εij (5)

48In web appendix table A6 we present estimates of the treatment effects on the sample of unrestricted risk-sharingpartners. The estimated effects are statistically insignificant. We offer two explanations for why we estimate negativestatistically 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 sensethat respondents may have reported that the support relationship is mutual, even if the relationship was not trulymutual. In web appendix figure A2 we show that the unrestricted risk-sharing partners hold a higher position in theircommunity 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-sharingpartners were socially closer to the respondent than the in-sample partners. In our study, 50% of unrestrictedrisk-sharing partners was a family member, while less than 10% of in-sample partners was. The social value of arelationship (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); Fafchampsand Lund (2003); Kinnan and Townsend (2012); Ligon and Schechter (2012)). If limited commitment in ISRAs is thereason why personal savings crowds them out, then it is clear why this happened to a greater extent for in-samplerisk-sharing partners.

21

where RSij is actual transfers sent by i to j, and Sj 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 state-

contingent 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

γ1 < 0 then treatment of i reduced the transfers she received if she experienced a negative shock,

or state-contingent transfers. If γ2 < 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

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.49,50

4.4.3 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

RSij = α+γ1D(Ti = 1andTj = 1)+γ2D(Ti = 1andTj = 0)+γ3D(Ti = 0andTj = 1)+X′iδ+εij (6)

where D(Ti = 1andTj = 1) equals one if both i and j are in the treatment group, D(Ti = 1andTj =

0) equals one if i is in the treatment group but j is in the control group, and D(Ti = 0 and Tj = 1)

equals one if i is in the control group and j is in the treatment group. Thus, γ1 is the treatment

effect if both individuals in a pair were assigned to treatment, γ2 is the treatment effect if individual

i was assigned to treatment, and γ3 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 some49A 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 matchdata reported by i with the data reported by j. We had re-estimated equation (4) using only the sample of 988 pairsused to estimate equation (5), and the results hold.

50A possible explanation for the lack of differential treatment effect by shock was the difference in the treatmentvariable for equations (4) and (5). In equation (4) we estimated the effect of treatment of i on transfers received byi, so that the receiver was the treated person; whereas in equation (5) we estimated the effect of treatment of i ontransfers received by j, so that the sender was the treated person. Re-estimating equation (5) using treatment of jis unlikely to change the results because, as shown in section (4.4.3), the treatment of j did not affect transfers sentto j, as reported by i.

51The sample size in table 8 is 1035 while the sample in table 3 is 1102. This difference is due to enumerator entryerror in photo IDs so that we cannot recover the treatment assignment of the partner j that individual i was referringto. As a robustness check, we had run the base estimations in table 3 using only the sample of 1035 pairs. The resultsare unchanged.

52Both 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 interactionsand risk-sharing activity. This is unlikely because the negative treatment effect applied to both the case where bothin a pair were treated and the case where only one was treated. Moreover, we directly estimate the effect of attending

23

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 explana-

tions. 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

Yij = α+ γTi + βY 0ij +X′

iδ + εij (7)

where Yij is an indicator of welfare at endline for a risk-sharing partner j who was assigned to the

control group, and Ti 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 sessionincreased, not decreased, risk-sharing. However, we do not place much value on these results, because the choice ofwhich training session to attend was endogenous.

24

welfare variable Y 0ij 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.53The HFIAS measures food insecurity along three domains: anxiety, quantity and quality.54The survey question was: “In the past 4 weeks, did you have enough to spend on non-food items like clothes,

medication, ceremonies etc?”55A conventional peer effects equation will measure effects at the i-level, Yi = α+ γT̄ j

i + βY 0i +X′

iδ1 + εij , whereT̄ ji the share of i’s risk-sharing partners j that were assigned to treatment, and Yi a welfare measure for individual i.

We estimate this conventional peer effects equation among the is who were assigned to the control group. We presentthe results in web appendix table A9; these estimations similarly fail to provide evidence of spillover welfare effects.

56We had also looked at alternative welfare indicators such as diet diversity, subjective status in community, andthe probability of removing someone from school due to lack of money to pay fees. We also do not find evidence ofwelfare spillover effects using these measures.

25

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 risk-

sharing 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

RSij = α+ γ1(Ti ×Net1i ) + γ2(Ti ×Net+1i ) + βNet1i +X′

iδ + εij (8)

where Net1i equals one if individual i had one risk-sharing partner, and zero otherwise, and Net+1i

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 γ1 = γ2. 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.57We 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

5.2 Effect on partners of partners

We test whether treatment affected risk-sharing between partners of partners. We estimate the

following equation

RSijk = α+ γTi +X′iδ + εij (9)

where RSijk is risk-sharing between j and j’s set of risk-sharing partners k, as reported by j, and

Ti 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 6= 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 RSijk 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 po-

tential 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.59

58We expect that the treatment of i increased risk-sharing between j and k, particularly if j and k were in thecontrol group. Thus, in web appendix table A12, we present estimates of equation 9 but only among the ijk triadswhere both j and k were in the control group. We find a similarly positive effect of the treatment of i on risk-sharingbetween j and k, but the estimates are statistically insignificant likely due to the small sample size.

59Where j is a control individual, we do find some evidence that the higher the number of jk pairs, the lower thetransfers received by j from k. One explanation for this is that individuals rely on each single person less if she hasmore people to rely on. This result is consistent with the results presented in table 10: our earlier result in section5.1 did not imply that having more risk-sharing partners increased risk-sharing, but rather implied that having morerisk-sharing partners mitigates the bilateral negative effect of increased access to savings.

27

6 Conclusions

Combining a randomized controlled trial of a microsavings intervention with rich data on risk-

sharing 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 21-28 percent and reduced actual transfers by 70-78 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 treat-

ment 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

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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33

Tables and Figures

Figure 1: Sample Structure

34

Fig

ure

2:St

udy

Tim

elin

e

35

Figure 3: Proportion That Adopted the Labeled Account

36

Figure 4: Balance in Labeled Account, Among Adopters

37

Figure 5: Number of Baseline Financial Support Partners

38

Figure 6: Mean Potential Transfers between Financial Support Partners

39

Table 1: Baseline Descriptive Statistics

Full Sample Rural Urbanmean std dev mean std dev mean std dev

DemographicsHousehold size 3.52 2.10 4.20 2.03 2.84 1.95Widowed 0.37 0.48 0.56 0.50 0.17 0.38Divorced or separated 0.33 0.47 0.29 0.46 0.37 0.48Has more than primary education 0.39 0.49 0.32 0.47 0.46 0.50Discount rate 85.8 47.3 74.1 48.6 97.7 42.9Degree of risk aversion (0-6) 2.50 1.69 2.64 1.71 2.35 1.65Income, Expenses and WealthIncome in past 7 days 1647.7 7934.5 1440.7 5120.0 1858.1 10020.2Amount invested in IGAs in past 30 days 4519.8 15499.2 5068.9 16992.2 3961.9 13823.3Does sex work 0.43 0.49 0 0 0.86 0.35Spending on temptation goods in past 7 days 407.9 830.2 206.9 432.3 612.2 1057.7Spending on non-food expenses in past 30 days 1386.5 2598.7 816.0 1845.9 1966.2 3083.2Resale value of livestock assets 11222.2 28542.3 18435.7 36000.0 3892.8 14874.6Value of non-livestock assets 53613.9 74059.4 32079.3 47218.1 75494.8 88640.8Severely food insecure (HFIA scale) 0.66 0.47 0.73 0.44 0.59 0.49Savings and CreditMax emergency can cover by self-financing 792.7 1860.8 393.2 1375.6 1198.6 2177.5Member in at least one ROSCA 0.75 0.43 0.70 0.46 0.80 0.40Last amount received from ROSCA (highest 5282.9 7425.6 3572.7 6846.7 6607.2 7598.5Total savings balance in all accounts 2248.7 9575.6 808.4 3389.4 3712.3 13008.5Has MPESA 0.93 0.25 0.99 0.079 0.87 0.34MPESA: current balance 397.2 1796.4 278.7 2028.6 534.0 1475.4Has other mobile banking 0.11 0.31 0.025 0.16 0.19 0.39Other mobile: current balance 434.2 1484.9 1021.9 2439.6 354.5 1317.8Has formal bank account 0.24 0.43 0.12 0.33 0.36 0.48Formal account: current balance 5959.4 17859.8 2131.2 5963.7 7235.4 20200.2Has other informal savings 0.33 0.47 0.30 0.46 0.36 0.48Informal savings: current balance 1318.9 2889.2 875.8 2694.1 1693.5 3005.8Any loan in past 12 months 0.57 0.50 0.60 0.49 0.54 0.50Interpersonal TransfersCan rely on at least 1 person for support 0.94 0.24 0.93 0.25 0.94 0.23Number of people can rely on 2.46 1.69 2.16 1.56 2.75 1.76Total amount received in past 3 months 3209.3 10272.4 2363.6 12042.9 4068.6 8015.4Total amount received that is for shocks* 1682.1 6917.1 1285.6 8420.8 2085.0 4923.7Sent money to at least 1 person in past 3 months 0.61 0.49 0.53 0.50 0.70 0.46Number of people sent money to 0.80 0.78 0.66 0.75 0.95 0.80Total amount sent in past 3 months 1080.1 2679.2 558.5 1896.6 1610.0 3206.4Transfers: total amount sent that is for shocks* 564.8 2173.6 273.3 1478.0 861.0 2673.2Observations 627 316 311Notes: Temptation goods include jewelry, perfume, cosmetics, clothing, hairdressing, snacks, airtime, meals outside thehome, cigarettes, alcohol and recreational drugs. Other non-food expenses include car battery, wedding and social events,funeral, health, expenses, family planning, electronics, household assets and home improvement. The following purposesare considered transfers for shocks: medical, wedding, funeral, or food consumption expenses. Values are reported inKenyan Shillings (Ksh), 85 Ksh = 1 USD at the time of the study.

40

Table 2: Negative Shocks and Coping Strategies

Rural UrbanPercent of women experienced any of the following shocks...Own illness or injury 0.38 0.38Illness or injury in household 0.38 0.26High food price 0.46 0.58Low price of goods sold 0.04 0.07Own job loss 0.12 0.12Job loss of main income earner 0.03 0.01Birth 0.03 0.06Death 0.03 0.03Theft 0.14 0.12Damage to assets 0.03 0.04Legal or criminal problems 0.00 0.06Conflict or violence 0.04 0.04Major crop loss 0.20 0.00Major illness of livestock 0.08 0.01Death of livestock 0.11 0.01Number of women 309 304Percent of shocks which induced the following coping strategy...Borrowed money 0.28 0.17Reduced expenses 0.23 0.16Relied on own savings 0.18 0.09Sought assistance 0.25 0.26Assistance in exchange for sex 0.09 0.01Nothing 0.09 0.27Tried to increase earnings 0.07 0.09Sold something 0.01 0.03Engaged in spiritual efforts 0.00 0.01Other 0.03 0.02Number of shocks 500 558Notes: Data is for the 7-month period between intervention and endline.

41

Table 3: Access to savings reduced risk-sharing

Potential Actual Potential ActualTransfers Transfers Transfers Transfers

Can Receive Received Can Send SentSpecification: FGLS

(1) (2) (3) (4)i is treatment -103.20∗ -56.45∗∗ -132.00∗∗∗ -42.14∗∗∗

(53.21) (28.03) (50.82) (15.57)

Mean in Control 488.4 81.89 475.4 54.74Specification: FGLS linear probability

(5) (6)i is treatment -0.04∗∗ -0.05∗∗∗

(0.02) (0.02)

Mean in Control 0.12 0.09Specification: pooled Tobit

(7) (8)i is treatment -456.4∗∗ -543.6∗∗∗

(194.6) (174.9)Observations 1101 1102 1102 1102Respondents 442 442 442 442Notes: Unit of observation is a pair i and j, where dependent variables arereported by individual i about her partner j. Each partner j is an in-samplepartner. Sample includes only risk-sharing pairs, defined as those who hada mutual support relationship at baseline or endline. Sample includesduplicate pairs, such that an observation exists for i and j and for j andi, if j also reports a mutual support relationship with i. Specifications 1-4is FGLS with robust standard errors clustered at the respondent i-level.Specifications 5-6 is FGLS linear probability model with robust standarderrors clustered at the respondent i-level. Specifications 7-8 is pooled tobitwith standard errors clustered at the respondent i-level. Standard errorsare shown in parentheses. Level of significance: *** p<0.01, ** p<0.05, *p<0.10, + p<0.15. Values are reported in Kenyan Shillings (Ksh), 85 Ksh= 1 USD at the time of the study. Included as regressors but not shown:age, dummies to account for 27 study clusters, and a constant.

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Table 4: Access to savings reduced risk-sharing at the intensive margin

Potential Actual Potential ActualTransfers Transfers Transfers Transfers

Can Receive Received Can Send SentSpecification: FGLS

(1) (2) (3) (4)i is treatment -167.4+ -47.56 -230.1∗∗ -70.9+

(111.4) (42.74) (108.9) (43.76)

Mean in Control 1007.4 144.5 980.3 111.2Specification: FGLS linear probability

(5) (6)i is treatment -0.07 -0.08∗∗

(0.05) (0.04)

Mean in Control 0.235 0.165Specification: pooled Tobit

(7) (8)i is treatment -313.6∗ -573.1∗∗

(175.3) (239.5)Observations 344 344 344 344Respondents 225 225 225 225Notes: Unit of observation is a pair i and j, where dependent variablesare reported by individual i about her partner j. Each partner j is anin-sample partner. Sample includes only always risk-sharing pairs, definedas those who had a mutual support relationship at both baseline and end-line. Sample includes duplicate pairs, such that an observation exists fori and j and for j and i, if j also reports a mutual support relationshipwith i. Specifications 1-4 is FGLS with robust standard errors clustered atthe respondent i-level. Specifications 5-6 is FGLS linear probability modelwith robust standard errors clustered at the respondent i-level. Specifica-tions 7-8 is pooled tobit with standard errors clustered at the respondenti-level. Standard errors are shown in parentheses. Level of significance: ***p<0.01, ** p<0.05, * p<0.10, + p<0.15. Values are reported in KenyanShillings (Ksh), 85 Ksh = 1 USD at the time of the study. Included asregressors but not shown: age, dummies to account for 27 study clusters,and a constant.

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Table 5: Access to savings reduced risk-sharing at the extensive margin

(1) (2) (3)OLS Regressions Dyad Fixed Effects

Has at least Number of Risk-sharingone partner partners link

i is treatment -0.08∗∗ -0.05(0.04) (0.11)

i or j treatment -0.06∗(0.04)

i and j treatment -0.09∗∗(0.04)

Endline dummy -0.22∗∗∗(0.03)

Observations 559 559 2726Dyads 1363Mean in Control 0.60 1.12 0.55Notes: For specifications 1 and 2, we use OLS with heteorskedasticity-robuststandard errors; the unit of observation is the respondent i. For specification3, we use panel dyad fixed effects with robust standard errors clustered at thepair or dyad level; The unit of observation is a pair i and j. The dependentvariable is a binary variable indicating whether a pair has a mutual supportlink as reported by either i or j. Sample includes all pairs that know eachother within cluster, and sample includes only unique pairs i and j. Eachpartner j is an in-sample partner. Standard errors are shown in parentheses.Level of significance: *** p<0.01, ** p<0.05, * p<0.10, + p<0.15. Includedas regressors in specifications 1 and 2, but not shown: age and dummies toaccount for 27 study clusters. Constant is included in all specifications.

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Table 6: Access to savings had no effect on non-mutual support partners

Potential Actual Potential ActualTransfers Transfers Transfers Transfers

Can Receive Received Can Send SentIn-sample charitable support partners

(1) (2)i is treatment 39.92 23.78

(34.93) (19.68)

Observations 284 284Respondents 177 177Mean in Control 105.2 6.494Unrestricted charitable support partners

(3) (4) (5) (6)i is treatment -125.1 5.93 12.14 -13.82

(221.8) (116.0) (181.4) (119.5)

Observations 548 548 477 477Respondents 271 271 261 261Mean in Control 1066 344 898 565Notes: Unit of observation is a pair i and j, where dependent variables arereported by individual i about her partner j. Sample includes only pairswhich always had a charitable support relationship, i.e. pairs who formeda charitable support relationship at both baseline and endline. Sampleincludes duplicate pairs, such that an observation exists for i and j and forj and i, if j also reports a charitable relationship with i. For specifications1 and 2, we use the sample of in-sample charity-in support pairs, wherei can rely on j, but not vice versa. For specifications 3 and 4, we usethe sample of unrestricted charity-out support pairs, where j can rely oni, but not vice versa. For specifications 5 and 6, we use the sample ofunrestricted charity-in support pairs, where i can rely on j, but not viceversa. Standard errors are shown in parentheses. Level of significance: ***p<0.01, ** p<0.05, * p<0.10, + p<0.15. Values are reported in KenyanShillings (Ksh), 85 Ksh = 1 USD at the time of the study. To account foroutlier problems, outcome values are winsorized at the 99th percentile forthe sample of unrestricted partners. Included as regressors but not shown:age, dummies to account for 27 study clusters, and a constant.

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Table 7: Access to savings reduced transfers received only for those that experienced a negativeshock

(1) (2) (3) (4)Actual Actual Actual Actual

Transfers Transfers Transfers TransfersReceived Sent Received SentAny negative shock Negative health shock

(a) i is treatment and i shock=1 -128.3∗∗ -181.5∗∗(51.03) (83.99)

(b) i is treatment and i shock=0 13.75 -4.56(29.33) (22.53)

i shock=1 95.97∗ 150.1∗(58.14) (85.21)

(a) i is treatment and j shock=1 -34.50∗∗ -35.61∗(16.67) (20.87)

(b) i is treatment and j shock=0 -49.65∗ -45.77∗∗(26.98) (21.81)

j shock=1 -28.10 -28.00(29.42) (31.56)

Chi-Square P-Value (a)=(b) 0.02 0.63 0.04 0.74

Observations 1102 988 1102 988Respondents 442 424 442 424Notes: Unit of observation is a pair i and j, where dependent variables are reported byindividual i about her partner j. Each partner j is an in-sample partner. Sample includesonly risk-sharing pairs, defined as those who had a mutual support relationship at baselineor endline. Sample includes duplicate pairs, such that an observation exists for i and jand for j and i, if j also reports a mutual support relationship with i. Estimation is FGLSwith robust standard errors clustered at the respondent i-level. The shock variables arebinary variables indicating whether a shock was experienced in the four months prior toendline. Standard errors are shown in parentheses. Level of significance: *** p<0.01, **p<0.05, * p<0.10, + p<0.15. Values are reported in Kenyan Shillings (Ksh), 85 Ksh =1 USD at the time of the study. Included as regressors but not shown: age, dummies toaccount for 27 study clusters, and a constant.

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Table 8: Access to savings had a similar negative effect on risk-sharing regardless of whether in apair both were treated or only one was treated

(1) (2) (3) (4)Potential Actual Potential ActualTransfers Transfers Transfers Transfers

Can Receive Received Can Send Sent(a) i is treatment and j is treatment -141.0∗ -95.65∗∗ -151.6∗∗ -37.70∗∗

(72.41) (45.22) (67.79) (15.67)(b) i is treatment and j is control -145.3∗∗ -84.16∗ -183.1∗∗∗ -31.26∗

(69.72) (44.88) (65.90) (17.05)(c) i is control and j is treatment -106.8∗ -62.85+ -99.62∗∗ 17.83

(54.66) (42.83) (46.24) (27.07)

Difference in individual treatment effects -38.50 -21.32 -83.48∗ -49.09∗∗Chi-Square P-Value (b)-(c)=0 0.486 0.42 0.10 0.05

Difference in treatment effect: both treated vs i treated 4.27 -11.49 31.47 -6.44Chi-Square P-Value (a)-(b)=0 0.91 0.32 0.39 0.44

Difference in treatment effect: both treated vs j treated -34.23 -32.81 -52.01 -55.53∗∗Chi-Square P-Value (a)-(c)=0 0.56 0.18 0.32 0.03

Observations 1034 1035 1035 1035Respondents 430 430 430 430Notes: Unit of observation is a pair i and j, where dependent variables are reported by individual i about herpartner j. Each partner j is an in-sample partner. Sample includes only risk-sharing pairs, defined as thosewho had a mutual support relationship at baseline or endline. Sample includes duplicate pairs, such that anobservation exists for i and j and for j and i, if j also reports a mutual support relationship with i. Estimation isFGLS with robust standard errors clustered at the respondent i-level. Standard errors are shown in parentheses.Level of significance: *** p<0.01, ** p<0.05, * p<0.10, + p<0.15. Values are reported in Kenyan Shillings (Ksh),85 Ksh = 1 USD at the time of the study. Included as regressors but not shown: age, dummies to account for 27study clusters, and a constant.

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Table 9: Access to savings had no spillover welfare effects on risk-sharing partners

Outcomes are welfare indicators of jFood Secure or Number of Has Enough to OverallMild Insecurity Meals Cover Non-Food Financial

(HFIAS) in a Day Expenses SituationTreatment effect

(1) (2) (3) (4)i is treatment 0.017 -0.011 -0.022 -0.057

(0.040) (0.042) (0.038) (0.072)

Mean in Control 0.427 2.654 0.439 2.488Treatment effect by health shock

(5) (6) (7) (8)(a) i is treatment and j health shock=1 0.010 -0.022 -0.033 0.079

(0.074) (0.086) (0.057) (0.149)(b) i is treatment and j health shock=0 0.019 -0.026 -0.018 -0.119+

(0.037) (0.040) (0.032) (0.066)j health shock=1 -0.158∗∗ -0.194∗∗ -0.190∗∗∗ -0.588∗∗∗

(0.073) (0.078) (0.060) (0.121)

Chi-Square P-Value (a)=(b) 0.919 0.643 0.843 0.252Observations 525 525 525 525Respondents 310 310 310 310Notes: Unit of observation is a pair i and j, where dependent variables are welfare outcomes of the partner j asreported by j herself. Each partner j is an in-sample partner who is in the control group. Sample includes onlyrisk-sharing pairs, defined as those who had a mutual support relationship at baseline or endline. Sample includesduplicate pairs, such that an observation exists for i and j and for j and i, if j also reports a mutual supportrelationship with i. Estimation is FGLS with robust standard errors clustered at the respondent i-level. Standarderrors are shown in parentheses. Level of significance: *** p<0.01, ** p<0.05, * p<0.10, + p<0.15. Included asregressors but not shown: age, dummies to account for 27 study clusters, and a constant.

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Table 10: Larger networks mitigate the reduction in bilateral risk-sharing

(1) (2) (3) (4)Potential Actual Potential ActualTransfers Transfers Transfers Transfers

Can Receive Received Can Send Sent(a) i Treatment X i Partners=1 -279.6∗∗ -109.7+ -323.6∗∗ -80.95∗∗

(127.8) (75.36) (136.0) (39.86)(b) i Treatment X i Partners>1 -49.89 -34.29 -60.68 -28.90∗

(56.48) (24.53) (46.45) (15.78)i Partners=1 145.4 81.96 224.0∗∗ 42.46

(108.4) (84.76) (108.8) (42.06)Chi-Square P-Value (a)=(b) 0.097 0.340 0.065 0.223

Observations 1101 1102 1102 1102Respondents 442 442 442 442Notes: Unit of observation is a pair i and j, where dependent variables are reported by individuali about her partner j. Each partner j is an in-sample partner. Sample includes only risk-sharingpairs, defined as those who had a mutual support relationship at baseline or endline. Sampleincludes duplicate pairs, such that an observation exists for i and j and for j and i, if j also reportsa mutual support relationship with i. Estimation is FGLS with robust standard errors clusteredat the respondent i-level. Standard errors are shown in parentheses. Level of significance: ***p<0.01, ** p<0.05, * p<0.10, + p<0.15. Values are reported in Kenyan Shillings (Ksh), 85Ksh = 1 USD at the time of the study. Included as regressors but not shown: age, dummies toaccount for 27 study clusters, and a constant.

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Table 11: Partners of partners mitigate the reduction in bilateral risk-sharing

Outcome variables are transfers between j and k(1) (2) (3) (4)

Potential Actual Potential ActualTransfers Transfers Transfers Transfers

Can Receive Received Can Send Senti is treatment 82.17∗∗ 107.4∗ 70.80∗∗ 60.09∗

(39.95) (65.17) (31.96) (36.30)number of k partners 0.902 -24.28∗ -13.56 -2.400

(12.34) (13.77) (11.51) (6.866)

Observations 785 785 785 785Respondents 361 361 361 361Mean in Control 475.7 181.8 470.7 115.2Notes: Unit of observation is a pair i and j. Sample includes only risk-sharingpairs, defined as those who had a mutual support relationship at baseline orendline. Sample includes duplicate pairs, such that an observation exists for iand j and for j and i, if j also reports a mutual support relationship with i.Dependent variables are measures of risk-sharing between individual j and herin-sample partner k, where k is not equal to i. Individual i is a risk-sharingpartner of j, but not a risk-sharing partner of k, while k is a risk-sharing part-ner of j. An individual j with only one in-sample partner is dropped in thisspecification, because that j would not have a k not equal to i. Potentialtransfers is calculated as the mean across k ’s of potential transfers, and actualtransfers is calculated as the the sum of actual transfers across k ’s. Estimationis FGLS with robust standard errors clustered at the respondent i-level. Stan-dard errors are shown in parentheses. Level of significance: *** p<0.01, **p<0.05, * p<0.10, + p<0.15. Values are reported in Kenyan Shillings (Ksh),85 Ksh = 1 USD at the time of the study. Included as regressors but notshown: age, dummies to account for 27 study clusters, and a constant.

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