Referrals: Loan Screening and Enforcement in a

Consumer Credit Field Experiment

Gharad Bryan, Dean Karlan and Jonathan Zinman∗

February 19, 2013

Abstract

Empirical evidence on peer intermediation lags behind a large body of theory and lend-ing practice suggesting that lenders can harness peers to mitigate adverse selection and moralhazard. We develop and implement a two-stage field experiment that permits separate iden-tification of peer screening and enforcement effects using a simple referral incentive mecha-nism under individual liability. We start by formalizing the conditions needed for two-stageexperiments to separately identify ex-ante selection from ex-post incentive effects when thereis selection on incentive effects. Next we test whether these identifying assumptions hold inour implementation setting, and find evidence that they do. Then we estimate peer effects onloan repayment in our setting, and find no evidence of screening (albeit with an impreciselyestimated zero) and large effects on enforcement. The results illustrate the potential utility andportability of both our methodological innovation (the identification tests) and our practical in-novation (the referral scheme).

JEL Codes: C93 D12 D14 D82 O12 O16

1 Introduction

Economic theory assigns credit market failure a central role in explaining poverty and underde-velopment. Borrowing constraints reduce efficiency, increase inequality and can lead to povertytraps (Banerjee and Newman, 1993; Galor and Zeira, 1993). Credit rationing also appears to beempirically important. Making use of experimental or quasi-experimental supply shocks, several

∗Bryan: London School of Economics and Innovations for Poverty Action, g.t.bryan@lse.ac.uk. Karlan: Yale University,M.I.T. Jameel Poverty Action Lab, Innovations for Poverty Action and NBER, dean.karlan@yale.edu. Zinman: DartmouthCollege, M.I.T. Jameel Poverty Action Lab, Innovations for Poverty Action and NBER, jzinman@dartmouth.edu. Theauthors would like to thank Manfred Kuhn and the employees of Opportunity Finance, Luke Crowley, and seminarparticipants at Yale, NEUDC, NBER summer institute and The Cambridge conference on consumer credit and bankruptcy.We would also like to thank The Bill and Melinda Gates Foundation for funding. This paper appeared as the third chapterof Gharad Bryan’s dissertation – he would like to thank The Kauffman Foundation for financial support. All errors are, ofcourse, our own.

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recent papers estimate a large unmet demand for additional credit - for consumers (Karlan andZinman, 2010), for Microenterprises, (Banerjee et al., 2009; Karlan and Zinman, 2011), and for andsmall and medium enterprises (Banerjee and Duflo, 2004). These studies, coupled with a litera-ture often showing high returns to capital (e.g., De Mel et al. 2008), lend credence to policy andprogrammatic efforts to relax borrowing constraints.

But how should one go about relaxing borrowing constraints? Information asymmetries, in-cluding ex-ante selection and ex-post incentive and enforcement problems, are often invoked asthe root causes of borrowing constraints in theory (Stiglitz and Weiss, 1981) and practice (Ar-mendariz et al. 2010). If this is indeed the case, contracts that alleviate asymmetric informationproblems provide one route to greater credit market efficiency.

A popular approach to tackling asymmetric information is based on the presumption thata borrower’s peers can be harnessed to provide information/screening or enforcement that isunavailable to (or more costly for) the lender. Peer-intermediation has been fleshed out overseveral hundred years of lending practice and can be seen in a range of guises including creditcooperatives, credit unions, rotating savings and credit associations, and microlenders such as theGrameen Bank. Peer intermediation has also been analyzed over several decades of theoreticalwork on optimal mechanism design in the face of different asymmetric information problems(e.g., Varian 1990, Stiglitz 1990, Besley et al. 1993, Banerjee et al. 1994, Besley and Coate 1995,Ghatak 1999, Ghatak and Guinnane 1999, Rai and Sjostrom 2004, and Bond and Rai 2008).

Empirical work on peer contracting has, however, lagged behind both theory and practice.Empirical work is important because designing contracts or policy interventions that make thebest use of peers requires empirical evidence on the absolute and relative strengths of screeningand enforcement.1 For example, if selection effects are strong but enforcement is weak, a mecha-nism that uses joint liability to select clients for a first loan but then moves to individual liabilitywould harness much of the screening incentive – a la Ghatak (1999) – but minimise the negativesof joint liability lending.2 Alternatively, if enforcement is largely responsible for the success ofpeer schemes, then the importance of peer mechanisms will decreases as ex-post enforcementthrough debt collection, court action or better identification increase. Despite the fact that insti-tutions are currently grappling with the design of credit contracts (e.g. Gine and Karlan 2010),designs that makes use of strong empirical information are currently limited (or non-existent)presumably because of the lack of strong empirical evidence or practical measurement methodsthat could be implemented buy lenders.

Empirical work separating peer selection and enforcement faces at least four challenges. First,most empirical work on the effects of peers in lending has taken place in the context of jointliability mechanisms.3 These setting are complicated and entail a great deal of strategic interactionbetween borrowers. In these settings, progress on separating selection and enforcement is only

1Throughout the paper we use the term enforcement to refer to a set of actions that might include monitoring, peerpressure, mutual insurance or direct peer assistance.

2See, e.g. Ghatak and Guinnane (1999) for a discussion of some of the cost of joint liability.3One exception is Klonner and Rai (2010), which finds in a non-experimental setting that co-signers improve repayment

performance in “organized” (intermediated) rotating savings and credit associations.

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possible if strong assumptions are made on the way that borrowers interact. For example, Gineand Karlan (2010) only informs us about the extent of enforcement under the assumption thatjoint liability encourages more enforcement than do group loans without a joint liability element.Similarly, Ahlin and Townsend (2007) only provides evidence on selection under the assumptionthat their model correctly captures the strategic situation. Second, as is well known from theliterature on testing contract theory (e.g. Chiappori and Salanie 2003) , it is difficult to separatehidden information and hidden action effects using observational data. For example, a positivecorrelation between the strength of a peer contracting incentive and repayment rates could becaused by either selection or enforcement effects.4

Third, discussions of selection require us to answer the question: selection on what? Whilethe received theory (e.g. Ghatak 1999) suggests that groups select on risk type, it is increasinglyrecognised that selection may be on a host of other variables such as risk aversion, income leveland aspiration (see e.g. Ahlin and Townsend 2007). Selection on these different variables willhave different implications for contract design. Of particular interest to us, and to the best of ourknowledge a point that has not been discussed in the existing literature, is the possibility thatselection is on the the ability to enforce – or what we will refer to as selection on malleability.Selection on malleability is particularly important because tests that ignore this possibility mayover or understate the extent of selection on the probability of repayment – what we will callcredit worthiness or repayment type.5 There are at least two reasons to separate selection onrepayment type and selection on malleability. First, and similar to the motivation for studyingselection on moral hazard as in Einav et al. (2011), is that selection on malleability can be reducedthrough a contract that provide more enforcement incentives. Thus an analysis that does notcorrect for selection on malleability will incorrectly assess the relative performance of contractsthat improve selection and contracts that improve enforcement. Second, knowing whether thereis selection on malleability widens the set of contracts available to the principle. For example, ina setting whether there is significant positive selection on malleability there is a case for contractsthat spend more on enforcement for those that are heavily selected than for those that are not.

Related, as recognised by the literature on using two stage experiments to separate adverseselection and moral hazard (e.g. Karlan and Zinman 2009) even if individuals do not select onmalleability, there may be a correlation between malleability and credit worthiness.6 This corre-lation will mean that peers will exert different amounts of enforcement effort when faced withpeers of different credit worthiness. As a result, comparing default rates across different levelsof selection, conditional on a particular enforcement incentive, will be an apples to oranges com-parison. For example, if credit worthy types are also more responsive to enforcement action, thencomparing low and high repayment types in the presence of enforcement will over estimate the

4Conceptually, this is the same as noting that a positive correlation between insurance coverage and claims is evidenceof either adverse selection or moral hazard, but cannot be used to separate the two.

5We see credit worthiness as an individual characteristic that determines the probability of repayment when there isno attempt at peer enforcement.

6In a adverse selection moral hazard setting this would be correlation between an agents risk type and the solution tothe optimal effort problem.

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extent to which these types differ in the absence of enforcement incentives. To see why this com-plicates contract design, consider trying to work out the tradeoff between a contract that removesall moral hazard and one that generates perfect selection. If we do not account for the applesto oranges comparison we will tend to underestimate the impact of the former contract, whichwould control part of the observed extent of selection problems.

Finally, both theory and recent empirical findings suggest that external validity is likely to bea challenge: the effectiveness of peer intermediation plausibly depends on several factors thatmay vary substantially across settings, like the information environment, the risk-sharing en-vironment, and borrower choice sets. For example, the pioneering theory paper of Besley andCoate (1995) shows that the impact of peer lending will depend on the extent of social sanctions,something that likely differs across environments. Similarly, the work of Ghatak (1999) suggeststhe screening impact of joint liability will depend on the degree of information that agents have,and studies have found plausible heterogeneity in information across different settings (e.g.Udry(1994) and Townsend (1995).) Empirical studies on the effects of joint vs. individual liabilitymechanisms have also produced mixed results, suggesting that heterogeneity of effects may beempirically large (e.g. Gine and Karlan 2010, Carpena et al. 2010 and Attanasio et al. 2011.)7 Sotoo have empirical studies on the effects of access to credit more broadly. For example, while Kar-lan and Zinman (2010) show positive impacts of increased consumer credit access in South Africa,Melzer (2011) finds large negative effects in the U.S. A plausible explanation for these results isthat the impact of peer mechanisms, as well as the impact of credit more generally, depends on ahost of settings specific characteristics that are not currently measurable.

We show that each of these issues can be addressed using a two-stage experiment, buildingon the work of Karlan and Zinman (2009). We see the experiment primarily as a measurementdevice that could be used to determine the strength of screening and enforcement in any setting.This is our response to the external validity problem: we present the experiment in a particularsetting; show that the experiment works in that setting; and provide important results on selec-tion and enforcement in that setting, but ultimately we want to show that the experiment is atheoretically and practically attractive method to measure important parameters for the design ofcontracts. Our hope is that this experiment can be be cheaply implemented by lenders (or otherinterested parties) in any setting to determine whether peer lending can work in that setting, andto work toward designing a contract with an optimal combination of enforcement and selectionincentives.

To show the potential of the experiment, and provide baseline results in a particular setting,we implemented the experiment in conjunction with Opportunity Finance South Africa (a mem-ber of the Opportunity International microfinance network). Opportunity offered existing clientsa 100 Rand ($12) bonus for referring a new borrower who met particular criteria for Opportunity’sindividual liability loan. Opportunity first randomly divided referrers into one of two ex-ante in-centives: referrers in the ex-ante approval group were told that they would receive the bonus

7These papers all use different methods and it is possible that the results are not driven by heterogeneity but rather thedifferent methods. However, it seems worth exploring the possibility that there are real heterogeneous effects.

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Figure 1: 2 × 2 Experimental Design

Approval Repayment

Approval No Incentive Screening Incentive

Repayment Enforcement Incentive

Screening and Enforcement

Incentives

Ex-Ante Incentive

Ex-Post Incentive

if the person they referred was approved for a loan. Referrers in the ex-ante repayment groupwere told that they would receive the bonus if the person they referred repaid a loan on time.Referrers in the ex-ante repayment treatment had both an ex-ante incentive to refer applicants ofgood credit quality (both observable and unobservable to Opportunity), and an ex-post incentiveto encourage repayment. Referrers in the ex-ante approval group only had an incentive to refersomeone they thought would be approved for a loan.

Subsequently, Opportunity randomly surprised some referrers, whose referred applicationshad been approved, with an improvement to their bonus contract.8 Half of the referrers withthe ex-ante repayment incentive were given their bonuses as soon as the loan was approved,thus removing the enforcement incentive. Half of referrers given the ex-ante approval incentivewere offered an additional bonus if the referred loan was repaid, thus creating an enforcementincentive. Thus, within each of the ex-ante groups, half the referrers have an ex-post repaymentincentive and half have an ex-post approval incentive.9

The design produces four groups of referrers, each with a different combination of ex-anteand ex-post incentives, as illustrated in Figure 1.

In Section 4 we provide a formal model of the referral decision and use it to show how thedesign addresses the empirical challenges discussed above. Our model highlights the follow-ing advantages of our experimental design. First, our experiment introduces peer influence ina controlled individual liability setting where there is limited potential for strategic interaction.Hence, we are able to provide a straightforward analysis of selection and enforcement incentives,based on a limited set of standard assumptions about creditor and referrer behaviour. This, webelieve, leads to more transparent tests of the ability to enforce and select. Second, our two-stageexperiment allows us a separate instrument with which to determine selection and enforcement– intuitively enforcement is identified by variation in the ex-post incentive and selection by the

8Lenders frequently contact borrowers with promotions in this market and our cooperating lender continued with theprogram after the experiment.

9The lender also contacted those referrers for whom the contract was not changed and reminded them of the existenceof the contract. This was to rule out attention or signalling channels.

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ex-ante incentive. Because we have two instruments we provide the necessary variation to sep-arate selection and enforcement, and we use our model, along with the data we collect, to showthat we can do so in our setting.

Third, because our experimental design allows us to compare across ex-ante incentive groupsconditional on there being no enforcement incentive (comparing across columns in the top rowin Figure 1) we are able to make an apples to apples comparison of the repayment performanceof differently screened peers – and hence we overcome the problem that enforcement effort maydepend on repayment type leading us to over or underestimate the extent of selection on repay-ment type. Our ability to make this comparison means that we are better able to identify selectionthan previous papers (e.g. Karlan and Zinman 2009 and Einav et al. 2011). Further, our exper-imental design allows us to compute the impact of enforcement on those selected to be creditworthy (comparing rows in column 2 of Figure 1) and for those that were not selected (compar-ing rows in column 1 of Figure 1). This means that we are able to determine the extent to whichmalleability depends on repayment type. Under the assumption that malleability is not correlatedwith repayment type we can use this comparison identify the extent of selection on malleability.10

Otherwise, we identify a composite of the two effects. More broadly, our setting also naturallylimits the set of things that the referrer could select on. Our theoretical model allows for selectionon the basis of search cost or familial obligation as well as credit worthiness and malleability andwe show how these interact.

Results from our implementation show strong enforcement effects. By comparing repaymentrates across ex-post incentives, holding the ex-ante incentive constant we find that the small bonus(100 Rand is equal to about 2% of the average referrer’s gross monthly income and 3% of the aver-age loan size) decreased default from around 20% to 10% in most specifications. The magnitudeof improvement in repayment performance is far above and beyond what referrers and borrow-ers could accomplish with side-contracting, and the improvement in collections (and savings incollection costs) far exceeded the lender’s outlays for bonuses. We also estimate whether referralincentives induced referrers to screen on information unobservable to (or unused by) the lenderby comparing repayment rates across ex-ante incentives, holding the ex-post incentive fixed. Wefind no evidence that peer screening improved repayment, although this is an imprecise zero.

This last finding raises the question of whether our experiment works to generate selection– i.e. were referrers induced to change their behaviour in response to the selection incentive,and did this change lead them to refer what they believed to be higher repayment type friends?In addition to the possibility that referrers simply did not pay attention to the information, ourmodel suggests three reasons why the experiment may not generate selection. First, in our contextthe lender has a stringent loan approval system. If referrers think that credit worthiness and

10Einav et al. (2011) identify selection on moral hazard in health insurance markets under the assumption that moralhazard type is not correlated with risk type. In our setting this is the same as assuming that malleability is uncorelatedwith credit worthiness. Their setting does not allow for a comparison in which there is no incentive for moral hazard, andtheir assumption that moral hazard type is not correlated with risk type is essential to their identification of selection onrisk type. In their setting it would be difficult to envisage a comparison that directly isolated the impact of risk types,because they would have to observe people that chose high insurance but in fact received none.

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the probability of loan approval are highly correlated, they will have an incentive to refer creditworthy types in both ex-ante treatments. Second, operational requirements imposed by the lenderimplied that the incentive promised in the ex-ante approval and repayment groups had to bethe same cash amount. This implies that the net present value of referral is higher in the ex-ante approval group (the incentive arrives earlier and with higher probability). Our theoreticalmodel suggests that this may have induced greater search in the approval group and, to the extentthat the probability of approval is correlated with the probability of repayment, may have led toreferral of high credit worthiness types in the ex-ante approval group. Finally, if there is strongselection on malleability, and malleability is negatively correlated with credit worthiness, thenreferrers may referrer low credit worthy friends in the ex-ante repayment group. Alternativelymalleability concerns could simply swamp credit worthiness concerns.

We adduce three pieces of evidence to show that these problems are not of concern and ourestimates should be thought of as accurately identifying selection on repayment type and whetherpeers have more information than the lender (again, subject to sample size). First, we showthat referrers in the ex-ante repayment treatment substitute away from referring family towardreferring work colleagues. This provides clear evidence that the referrers were aware of andinfluence by the incentive.11 The observation further shows that repayment and approval typesare not too highly correlated in the referrers mind - if they were, the referrer would refer the sameperson in each of the ex-ante treatment groups. Finally, under the assumption that work matesare more expensive to refer – either because it requires more search or because there are familialobligation to refer family given that the referee receives R40 – substitution toward work matesshows that the larger incentive in the ex-ante approval group did not loom large enough to leadto referral of higher cost types in the ex-ante approval group.12

Second, we show that the probability of making a referral is not affected by the ex-ante treat-ment assignment. This again suggests that the difference in the net present value of the incentivedoes not loom large. Third, we show that we cannot reject that the enforcement effect is the samewhen we compare across those in the ex-ante repayment incentive and those in the ex-ante ap-proval incentive, although the standard errors are large. We, therefore, cannot reject that thereis no selection on malleability, and that our selection estimates are true estimates of the extent ofreferrer knowledge. These three tests are essential to showing that the experiment does indeedgenerate an attempt at selection, and that we should, therefore, interpret our measure of screeningas a measure of the extent of knowledge held by the referrer. Similar data needs to be collected inother settings that implement measurements experiments along these lines.

The remainder of the paper is structured as follows. Section 3 introduces Opportunity and theSouth African microloan market. Section 3 provides details of the experiment. Section 4 outlinesa simple model of the referrer’s decision process, highlighting the conditions under which our

11This can be thought of as a basic manipulation check.12Our interpretation of work mates as higher cost is borne out by the recent paper of Beaman and Magruder (2009)

which shows a similar selection effect in the context of a labor market experiment. Their experiment also documentspositive selection effects, which would only occur if work mates are indeed more costly to refer.

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experiment separately identifies enforcement and selection. Section 5 provides some summarystatistics and discusses the integrity of the randomization. Section 6 provides our main results.Section 7 discusses a few alternative explanations of the data and section 8 concludes.

2 Market and Lender Overview

3 The Experiment

From February 2008 through July 2009, Opportunity offered each individual approved for a loanthe opportunity to participate in its new “Refer-A-Friend”program. Individuals could participatein the program only once. Referrers received a referral card, which they could give to a friend (thereferred). The referred earned R40 ($US5) if she brought in the card and was approved for a loan.The referrer could earn R100 ($US12)13 for referring someone who was subsequently approvedfor and/or repaid a loan, depending on the referrer’s incentive contract.

Opportunity first randomly assigned referrers to one of two ex-ante incentive contracts, corre-sponding to two different referral cards. Referrers given an ex-ante approval incentive would bepaid only if the referred was approved for a loan. Referrers given the ex-ante repayment incentivewould be paid only if the referred successfully repaid a loan.14 Figure 1 shows examples of thereferral cards, the top card was given to referrers in the ex-ante approval group and the bottomcard to those in the ex-ante repayment group.

Among the set of referrers whose referred friends were approved for a loan, Opportunityrandomly selected half to be surprised with an ex-post incentive change. Among referrers whohad been given the ex-ante approval incentive, half were assigned to receive an additional ex-postrepayment incentive. Opportunity phoned referrers in this group and told them that, in additionto the R100 approval bonus, they would receive an additional R100 if the referred repaid the loan.The other half of referrers who had been given the approval incentive ex-ante were contacted byOpportunity and reminded to pick up their R100 bonus. (Opportunity did not provide any newinformation on the incentive contract to these referrers, but we wanted referrers in both ex-postarms to receive a phone call from Opportunity in case the personalized contact from the lenderhad some effect.)

Among referrers who had been given the ex-ante repayment incentive, half of the referrerswere assigned to have the ex-post repayment incentive removed. Opportunity phoned referrersin this group, told them that they would be paid R100 now, instead of conditional on loan re-payment, and explained that this was the extent of the referrer’s bonus eligibility (e.g., that thereferrer would not receive an additional R100 if the loan was repaid). The other half of referrerswho had been given the repayment incentive ex-ante were assigned to continue with an ex-post

13The bonus for the referrer was initially R60 but was changed to R100 in July 2008 at the request of the lender. Theinclusion of this as a control makes no difference in any of our results.

14Successful repayment was defined as having no money owing on the date of maturity of the loan, or successfullyrolling over the loan.

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Figure 2: Referral Cards

If the friend is approved for a loan

If the friend successfully repays a loan

repayment incentive. Opportunity phoned these referrers with a reminder that they would re-ceive a bonus if the loan was repaid.

Figure 1 summarizes the randomization and the incentives that the referrers face. Intuitively,any effect of peer screening can be identified by comparing the arms with and without an ex-ante repayment incentive, holding constant the ex-post incentive. Similarly, any effect of peerenforcement can be identified by comparing the arms with and without an ex-post repaymentincentive, holding constant the ex-ante incentive.

4 Identifying Whether Referrers Have Information

In this section we discuss identification. Identifying enforcement effects using the ex-post ran-domization is straightforward, so we focus on a more difficult problem - clarifying the conditions

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under which our experiment allows us to answer the question: “do peers have useful informationabout their friends that is not currently used by the lender in its screening process?” To facilitatethe discussion we consider a stylized model of the referral and enforcement decision. Within thecontext of this model, we provide a definition of what it means for peers to have information thatis not used by the lender and argue that, we can use data collected as part of the experiment todetermine whether peers have information.

4.1 The Referral Decision

A market consists of N potential loan takers, each of whom is characterised by three parameters:

1. θ ∈ {θL, θH}: a repayment type;

2. γ ∈ (0, 1): the probability that the individual is approved for a loan; and

3. λ ∈ (0, λ]: the net cost of recruiting the individual to the referral scheme, including all socialand search costs and/or benefits, but excluding the referral bonus.

The parameters are drawn from a distribution F that admits a strictly positive marginal densityfor both γ and λ, and we denote the realisation for individual i, (θi, γi, λi). Each referrer j knowsa subset Nj of the total set of potential borrowers and the timing of the referral decision is asfollows:

1. The referrer j chooses a referee i ∈ Nj and pays a cost λij;

2. The referrer is approved for a loan with probability γij;

3. The referrer applies social pressure e to encourage repayment; and

4. The loan is repaid with probability f (θij, e), where

(a) f is increasing in both arguments, concave in e and lies between 0 and 1; and

(b) f (θ, 0) = θ.15

We restrict discussion to binary repayment types because it allows for a more concrete and easyto follow discussion a richer type space would be unlikely to alter the main results.

The referral decision depends on what the referrer believes about the parameters (θ, γ, λ). Weassume that λ is known to the referrer, and that she receives a signal (θ, γ), which she uses to formbeliefs about a potential referee’s type. We restrict our discussion to binary signals, so θ ∈ {θL, θH}with the interpretation that j believes i to be more likely to be a high type if θij = θH than ifθij = θL. We denote fl(e) to be the perceived probability of repayment when the referrer receives

15This is merely a normalisation.

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signal θl and puts in effort level is e, and (with some abuse of notation) we let the perceivedprobability of approval equal γ when the signal is γ.16

In making the referral decision, a referrer takes into account the possibility that she will exertpressure on the referee to repay the loan. We, therefore consider the decision backward, firstanalysing the effort decision and then returning to the referral decision.

Consider first the effort decision. If the referrer is in the ex-ante approval treatment she knowsshe will exert no effort. If the referrer is in the ex-ante repayment treatment she predicts choosingher level of effort to solve

maxe

{BR fi(e)− c(e)

}where BR is the bonus payment in the repayment treatment and c is a strictly convex functionthat captures the cost of effort. We denote the unique maximiser e∗(θl) ≡ e∗l for l ∈ {L, H}. Fora borrower of type (θ, γ) perceived to be of type (θ, γ) the repayment probability is f (θ, e∗(θ)).Depending on the structure of f , it may be the case that conditional on effort spent on socialpressure, high types actually have lower repayment rates. This means a comparison of repaymentrates in the presence of enforcement decisions may not reveal whether referrers have accurateinformation. We will discuss this point, and how it affects identification in the next subsection.

Now consider the referral decision. Given the effort decision discussed above, referrer j in theex-ante approval group chooses who to refer by solving

Uj(A) ≡ maxi∈Nj

{γiBA − λi

}where BA is the bonus paid in approval treatment. Because the bonus in the ex-ante approvaltreatment is expected to arrive earlier in time (immediately after approval) BA ≥ BR. In theex-ante repayment group referrer j solves

Uj(R) ≡ maxi∈Nj

{γi

(BR fi(e∗i )− c(e∗i )

)− λi

}.

Finally, a referrer j makes a referral in the ex-ante repayment treatment if Uj(R) > 0 and in theapproval treatment if Uj(A) > 0.

4.2 Identifying Whether Referrers Have Information

Our aim is to understand whether the set of referrers have information about the repayment typeof their friends. We say that referrers have information if

E(θ|θH) ≡ E(θ|θ = θH) > E(θ|θ = θL) ≡ E(θ|θL), (RHI)

16Formally fl(e) = p(θl) f (θH , e) + (1− p(θl)) f (θL, e) where p(·) maps from signals to posterior beliefs. γ is similarlydefined and our notational choice can be thought of as a restriction on the space of signals and the probability with whichthey are received.

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where the expectations is taken with respect to the population distribution F. This is equivalentto saying the the signal is informative. In our context it is important to know whether RHI holdsbecause a lender may wish to extract information from a peer and, at a later date, offer a contractthat does not offer any peer enforcement incentive, instead relying on the previous peer selection.As discussed above, a simple comparison of repayment rates in the presence of enforcement maynot be informative about whether information has been revealed.

Under some assumptions our experiment allows us to identify whether RHI holds. DenoteθA

j to be the perceived repayment type of referrer j in the ex-ante approval treatment and θRj

the equivalent for the ex-ante repayment treatment. Because parameter values will vary acrossreferrers j we can define a probability that the individual referred in each treatment is a high type,Pr(θA = θH) and Pr(θR = θH). With this notation, the expected difference in repayment ratesacross ex-ante treatments conditional on being in the ex-post approval treatment is

D(A) ≡ Pr(θR = θH)E(θ|θH)+Pr(θR = θL)E(θ|θL)−

Pr(θA =θH)E(θ|θH) + Pr(θA = θL)E(θ|θL).(1)

Consequently, if the experiment induces selection so that

Pr(θR = θH) > Pr(θA = θH), (SELECTION)

D(A) will be greater than zero if and only if RHI holds. As a consequence, our experimentallows us to determine whether the refer has information if it induces SELECTION to hold. Theremainder of this section argues that SELECTION does hold in our experiment, and that this canbe determined empirically.17

Because there are only two repayment types it is without loss of generality to consider thecase in which the referrer has only two friends, one high repayment type friend and one lowrepayment type friend – these can be considered the friends with the highest probability of be-ing approved. Denote the approval probability of the high repayment type friend γH and theapproval probability of the low repayment type friend γL. Similarly λH and λL denote the netreferral benefit for the two friends. Under this restriction, the high type is referred in the ex-anteapproval group if

BA[γH − γL] ≥ λH − λL. (2)

In the ex-ante repayment group the high type is referred if

BR[γH( fH(e∗H)− c(e∗H))− γL( fL(e∗L)− c(e∗L))] ≥ λH − λL. (3)

17Our experiment also allows us to measure D(R) – the differences in repayment rates across ex-ante treatment groupsconditional on being in the ex-post repayment treatment. However, given (4.1) it will not necessarily be the case thate∗(θR) = e∗(θA), as a consequence D(R) does not present an apples to apples comparison and cannot be used to determinewhether RHI holds in our population. The measure D(R) is, however, useful for other purposes as discussed below. Thefact that D(A) measures a situation with no enforcement effort allows for a clean identification of the role played byinformation. This is somewhat unique to peer settings such as this one and the labor market experiment studied inBeaman and Magruder (2009). In other settings such as Karlan and Zinman (2009) there is no equivalent.

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SELECTION holds if (2) is less likely to hold in the population than (3) or

BA[γH − γL] < λH − λL < BR[γH( fH(e∗H)− c(e∗H))− γL( fL(e∗L)− c(e∗L))] (4)

for more than half of the population of referrers.A sufficient condition for (4) to hold is that there are more high cost people referred in the

ex-ante repayment treatments (i.e. λR > λA) and that high cost types (λH) are indeed perceivedto be high repayment types (θH). Our strategy is to show that we do indeed observe more highcost types in the ex-ante repayment treatment, and that the two plausible stories under which wewould observe negative selection (high cost types being low repayment types) do not hold in ourdata.

We show below that those in the repayment treatment substitute away from referring familymembers toward referring work colleagues. We believe that it is reasonable to assume that workcolleagues are more costly to refer than family members, both because of the actual cost of con-tacting work collegues and because the referrer may have a direct obligation to refer family mem-bers. This assumption also gains support in the recent paper of Beaman and Magruder (2012).They conduct a similar experiment in a context of job referrals. They show evidence that thosein the equivalent of our repayment treatment also substitute toward referring work colleaguesaway from family. In their context this also involves an increase in work ability and suggests thatwork colleagues are in fact higher cost and higher “quality” in their setting. This fact in the dataprovides clear evidence that our incentive induces selection, in the sense that the experimentaltreatment induces a change in behavior. Even if one does not believe that family members arecheaper to refer, the fact that we demonstrate selection rules out the possibility that γ is so highlycorrelated with θ that households simply refer high repayment types in both treatments. The factthat we observe selection also rules out the possibility that referrers have less that two friends (i.e.Nj < 2 ∀j) which would rule out the possibility of observing selection.

To show that there is no negative selection, we consider two potential reasons that (4) wouldnot hold, and provide evidence against these conditions. First, it may be the case that

fH(e∗H)− c(e∗H) < fL(e∗L)− c(e∗L). (5)

Or that the net benefit of referring a high repayment type is less than the net benefit of referringa low repayment type. This would be a problem because it would induce negative selection. Itis a priori ambiguous whether e∗ is increasing or decreasing in θ. There seem to be several viewsthat one could take. One intuition suggests that there is much less scope for social pressure onthose who are already diligently repaying and as a consequence we might suppose that e∗H < e∗L(i.e. high types are less manipulable or susceptible to social pressure). Social pressure might evenbe counterproductive if high repayment types are intrinsically motivated and external pressurecrowds out intrinsic motivation (e.g. Gneezy and Rustichini 2000, Benabou and Tirole 2003 &Besley and Ghatak 2005). If this is the case, we might see that fH(e∗H)− c(e∗H) < fL(e∗L)− c(e∗L).

13

A second intuition, however, suggests that high types will be those that are easiest to motivate;e.g., they already care the most about diligently repaying and hence will also care most abouthow they are viewed by their peers. If this is the case we might have e∗H > e∗L which would implyfH(e∗H) > fL(e∗L).

Our experiment allows us to test whether (5) holds. Because BR ≤ BA, if (5) holds then weaklymore high repayment types will be referred in the ex-ante approval treatment and the differencein repayment rates induced by the ex-ante incentive will be larger for the low repayment typesthan the high high repayment types: fH(e∗H)− fH(0) < fL(e∗L)− fL(0). As a consequence, if weassume that the referrer knows f as a function of e (5) implies that D(A) > D(R) and that D(A) <

0 where D(A) is as defined in equation equation 1 and D(R) is the difference in repayment acrossthe ex-post treatment groups conditional on being in the repayment group ex-ante (discussed infootnote 17). As both D(A) and D(R) can be estimated in our experiment we can test whetherthere is this kind of negative selection. As we show below, with the caveat that our estimates arenoisy, we cannot reject that D(A) = 0 and that D(A) = D(R).

The above observation also raises the interesting point that conditional on (5) not holding, ourexperiment allows for the identification of the difference in repayment rates that is due solely toinformation. This occurs because we can clearly state that those in the ex-post approval treatmenthave no incentive to enforce the loan. This means that comparing across ex-ante treatments con-ditional on being in the ex-post approval treatments holds effort constant. In contrast, comparingacross ex-ante treatments conditional on being in the ex-post repayment treatment does not holdconstant enforcement effort and conflates selection and enforcement. Other two stage experi-ments such as Karlan and Zinman (2010) cannot make such a clean separation because there is notreatment that completely removes moral hazard in their setup.

Another reason (4) might not hold is because BR ≤ BA. Therefore, referrers in the ex-anteapproval group may have a greater incentive to refer high cost (i.e. high λ) referees. To the extentthat λ is correlated with θ this may lead to referral of higher repayment types in the ex-anteapproval treatment. For example a referrer in the ex-ante approval group may be motivated tosearch hard for a high γ high λ referee in order to reap the large reward BA. This may incidentallyinduce higher θ types to be referred in the ex-ante approval group. If this were the case then,conditional on λi > 0 for all i ∈ N we should observe that more people are referred in the ex-anteapproval group. We provide evidence below that this is not the case.

5 Data

5.1 Summary Statistics

Table 1 provides a summary of the characteristics of Opportunity borrowers over the period inwhich the experiment was run.

14

Table 1: Demographic Variables of all Borrowers During Experiment

Mean Median Std Dev

Female 0.418 - 0.493

Age 37.789 36.000 10.785

High School Education 0.637 - 0.481

Disposable Income 1753 1265 1703

Requested Amount 5049 3000 6615

Requested Term 10.743 9 6.265(Months)N 4383

Disposable income is income remaining after rent, debt repayments and recurring obligations. An individual has a highschool education if they have matriculated or gone on to tertiary education.

5.2 Integrity of the Randomization

Opportunity handed out 4408 referral cards to borrowers approved for new loans during thestudy period. Table 2 presents regressions of treatment assignment on a range of backgroundcharacteristics of the potential referrers. If the randomization is valid, we would expect baselinecharacteristics to be uncorrelated with treatment. In all cases an F-test of the restriction that thecoefficients are jointly zero fails to reject at the usual significance levels. Further, most individualcoefficients are not statistically different from zero and the total number of significant coefficientsis in line with what we would expect to see by chance. Below we also show that our results arerobust to including controls for referrer baseline characteristics.

Of the 4408 cards that were handed out, 430 were returned and 245 of these referred clientswere approved for a loan. The surprise nature of the second randomization (i.e. the changein ex-post incentives) provides another opportunity to check the integrity of the experimentalimplementation. Because the second-stage assignments were not known to potential referrers ex-ante (nor to Opportunity staff members delivering referral cards), baseline characteristics of thosereferred and approved for a loan should not differ within the ex-ante treatment groups.18 To testfor balance we run regressions similar to those presented in Table 2 where the outcome variableis being assigned to the ex-post repayment incentive. The first two columns of Table 3 shows theresults of the regressions. Within the group given the ex-ante approval incentive, the F-test shows

18Comparison across the ex-ante incentive groups are, however, endogenous. That is, we cannot compare characteristicsof those in the ex-ante approval groups to those in the ex-ante repayment groups as part of the experiment aims to generatedifference in these characteristics. We can run similar regressions on those who were referred not conditioning on beingapproved. The results are similar.

15

Table 2: Testing The Balance of Referrer Characteristics Across Treatments: OLS

Ex-Ante Incentive

Ex-Post Incentive Approval Repayment Approval Repayment

Female -0.006 0.008 0.005 -0.008(0.014) (0.014) (0.014) (0.014)

Age 0.000 -0.001 0.000 0.000(0.001) (0.001) (0.001) (0.001)

High School Education -0.027 0.027 -0.007 0.008(0.023) (0.023) (0.023) (0.023)

Salary Earner -0.004 0.022 -0.016 -0.003(0.016) (0.016) (0.016) (0.016)

Disposable Income -0.003 -0.006 0.010* -0.001(Thousands of Rand) (0.004) (0.004) (0.004) (0.004)*Application Score 0.000 0.000 0.000 0.000

(0.000) (0.000) (0.000) (0.000)ITC Score 0.000 0.000 0.000 0.000

(0.000) (0.000) (0.000) (0.000)ITC Score Missing 0.072 0.039 -0.058 -0.053

(0.109) (0.109) (0.109) (0.110)Requested Amount -0.001 0.004* -0.004* 0.000(Thousands of Rand) (0.002) (0.002) (0.002) (0.002)* *Requested Term 0.002 -0.004* 0.002 0.000(Months) (0.002) (0.002) (0.002) (0.002)*Government Worker 0.005 -0.002 0.022 -0.025

(0.031) (0.031) (0.032) (0.032)Cleaner/Builder/Miner 0.010 -0.006 0.007 -0.011

(0.031) (0.031) (0.031) (0.031)Security/Mining/Transport 0.021 -0.004 0.020 -0.037

(0.033) (0.033) (0.033) (0.033)Retail Worker -0.002 0.008 0.003 -0.009

(0.031) (0.031) (0.032) (0.032)IT/Financial Woker 0.010 -0.025 0.014 0.001

(0.035) (0.035) (0.035) (0.035)Agriculture/Manufacturing 0.008 -0.005 0.027 -0.030

-0.029 -0.029 -0.029 -0.029Constant 0.189 0.224 0.273** 0.315*

(0.118) (0.118) (0.119) (0.120)F-test of joint significance 0.560 0.930 0.810 0.440p-value of F-test 0.916 0.533 0.679 0.971N 4408 4408 4408 4408

Approval Repayment

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Each column represents a separate OLS regression where the LHS variable is assignment to

the particular treatment. Education is a dummy variable taking on value 1 if the referrer has matriculated. Application score is an internal

credit score. ITC score is external credit score. Salary monthly is a dummy variable taking value 1 if the client receives his or her salary

monthly.

16

that the baseline coefficients do not significantly predict assignment to treatment in the joint test.Among the individual tests, only one of the sixteen variables is significant, which is about whatone would expect to happen by chance.

Within the group given the ex-ante repayment incentive, there appears to be more cause forconcern (Column 2). A higher application score (i.e., internal credit score) significantly predictsassignment to the ex-post approval group. Given that application score is a key measure of theobserved credit quality of the applicant, this is troubling. It turns out that Opportunity changedits application score in May 2009. Before this time, scores are out of 200, while after they are out of800. Only 12 referred clients from the ex-ante repayment group were approved for loans after thispoint and 9 were from the ex-post approval group. This is not out of line with what we wouldexpect from random arrival times, but does create a problem in testing orthogonality. Columns 3and 4 of Table 3 take two approaches. First, in Column 3 we leave out the application score. Withapplication score not included, the p-value for the F-test of joint significance rises to 0.326 from0.077 and we are more confident that the allocation is random. Second, in Column 4 we restrictthe sample to prior to May 2009. This restriction also implies that the baseline characteristics areno longer significantly predictive of assignment. We gain further confidence by considering theimpact of ITC score on assignment. The ITC score is an externally provided credit score and islikely to be another good predictor of credit worthiness and it is never predictive of treatmentstatus. Overall it seems that the randomization was succesful. Regardless, we show below thatour results are not sensitive to including these baseline characteristics as controls.19

6 Results

6.1 Who Refers and Who Gets Referred?

Overall around 10% of eligible clients made a referral. This is not correlated with the ex-anteincentive a regression of the referral rate on a dummy for ex-ante treatment gives a coefficientof −0.002 with a standard error of (0.04). As discussed above, this suggests that the higher netpresent value of the bonus in the ex-ante approval group did not loom large in referrer’s calcula-tions.

We also collected data on the relationship between referrers and referees. Specifically we askedthe referee “How do you know the person that gave you the voucher?” Most people answeredthat the referrer was a relative or work colleague. A small number answered religion. Table 4shows the impact of the selection incentive (being in the ex-ante repayment group) on the prob-ability of refereeing a relative or a work colleague. The table shows that the selection incentiveleads referrers to substitute away from relatives and those they know through church to theirwork colleagues – those with the selection incentive are 10% more likely to refer a relative. Asdiscussed above, this provides direct evidence that our experiment induced selection.

19We can only control for these differences when studying the enforcement question, when we consider selection, re-ferred characteristics are endogenous.

17

Table 3: Testing The Balance of Referred Characteristics Across Ex-Post Treatments. DependentVariables is Assignment to Ex-Post Repayment Incentive: OLS

App. Score Exlcuded

Before May 2009

Ex-Ante Incentive Approval Repayment Repayment Repayment

Female 0.041 0.098 0.088 0.147(0.113) (0.104) (0.107) (0.113)

Age 0.001 0.003 0.004 0.002(0.005) (0.005) (0.005) (0.006)

High School Education 0.131 0.022 -0.005 -0.008(0.148) (0.164) (0.169) (0.173)

Salary Earner 0.029 -0.117 -0.086 -0.106(0.110) (0.113) (0.116) (0.133)

Disposable Income 0.034 0.028 0.037 0.023(Thousands of Rand) (0.057) (0.059) (0.061) (0.069)Application Score 0.000 -0.001*** - 0.002

(0.000) (0.000) - (0.004)**ITC Score 0.002 0.000 0.000 0.000

(0.001) (0.001) (0.001) (0.001)ITC Score Missing 1.197 -0.116 -0.276 -0.077

(0.893) (0.895) (0.922) (0.935)Requested Amount 0.010 -0.027* -0.026 -0.020(Thousands of Rand) (0.011) (0.016) (0.016) (0.021)Requested Term -0.013 0.014 0.010 0.012(Months) (0.015) (0.017) (0.018) (0.019)Government Worker -0.389 0.103 0.023 0.115

(0.266) (0.257) (0.264) (0.273)Cleaner/Builder/Miner -0.094 0.098 0.028 0.027

(0.207) (0.211) (0.217) (0.225)Security/Mining/Transport -0.330 -0.321 -0.450* -0.355

(0.226) (0.251) (0.255) (0.275)Retail Worker -0.212 -0.105 -0.166 -0.129

(0.203) (0.220) (0.226) (0.231)IT/Financial Woker -0.570** 0.495 0.445 0.427

(0.279) (0.533) (0.550) (0.562)*Agriculture/Manufacturing -0.222 -0.168 -0.214 -0.199

-0.187 -0.222 -0.229 -0.234Constant -0.547 0.642 0.692 0.348

(0.923) (0.932) (0.962) (1.059)

F-test of joint significance 0.810 1.640 1.150 0.990p-value of F-test 0.669 0.077* 0.326 0.47812N 123 120 120 108

Whole Sample

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Each column represents a separate OLS regression where the LHS variable is assignment to

the particular treatment. Education is a dummy variable taking on value 1 if the referrer has matriculated. Application score is an internal

credit score. ITC score is external credit score. Salary monthly is a dummy variable taking value 1 if the client receives his or her salary

monthly.

18

Table 4: The Impact of Ex-Ante Treatment Group on Referred Characteristics

Dep Var. Relative Work

Selection Incentive -0.095 0.051(0.043) (0.046)

Mean 0.271 0.656

N 428 428

No Controls

Each column represents a separate OLS regression. Standard errors in parentheses.

6.2 Repayment Rates

We identify screening and enforcement rates by comparing the repayment performance of loansreferred by referrers facing different incentives. We have four different and complementary mea-sures of repayment performance. Each proxies for the costs a lender bears when borrowers don’trepay (on time), without needing to impose additional assumptions on what the lender’s coststructure actually is (since in our experience many lenders lack precise data on marginal costs ofcollections). First, we have an indicator variable, for all 245 referred clients, of whether or notthe borrower was charged penalty interest for paying late at any time during the course of theloan. Second, we measure whether the loan was fully repaid on the date of maturity for the 240loans that have reached maturity.20 Third, for those 240 loans we also calculate the proportion ofprincipal still owed at maturity date (this value is zero for loans repaid on time, and positive forloans in arrears). Fourth, Opportunity charges off loans deemed unrecoverable and has made achargeoff decision (yes or no) on all but one of the 240 loans that have reached maturity as of thiswriting.21

Each panel in Table 5 shows the mean of these four loan performance measures, organizedby treatment groups. It also shows the difference in means holding either the ex-ante or ex-postrepayment fixed. These differences are our key results.

The ”Difference” row in the first two columns of each panel in Table 4 shows an estimate ofthe enforcement effect that is created by a difference in the ex-post incentives. So altogether thetable provides eight estimates of the enforcement effect (two for each measure of default). Thepoint estimate for each of the eight differences is negative, suggesting that adding the ex-postrepayment incentive decreases the incidence of default. In each case the implied magnitude ofthe enforcement effect is large; e.g., an 11 percentage point reduction in chargeoff likelihood, on

20A loan that was rolled over was considered to be repaid.21The results do not change qualitatively if we arbitrarily assign this loan as being charged off or not.

19

Table 5: Key Outcome Variables: Mean Differences Across Treatment Groups

(a) Penalty Interest Charged by Lender (N=245)

Approval Repayment Diff

Approval0.389

(0.064)0.518

(0.069)0.129

(0.093)

Repayment0.258

(0.054)0.272

(0.055)0.015

(0.077)

Difference -0.132(0.083)

-0.246***(0.087)

0.114(0.122)

Ex-Ante Incentive

Ex-P

ost

Ince

ntiv

e

(b) Positive Balance Owing at Maturity (N=240)

Approval Repayment Diff

Approval0.206

(0.054)0.226

(0.058)0.019

(0.079)

Repayment0.095

(0.037)0.152

(0.044)0.056

(0.058)

Difference -0.111*(0.064)

-0.075(0.072)

0.036(0.098)

Ex-Ante Incentive

Ex-P

ost

Ince

ntiv

e

(c) Portion of Loan Value Owing at Maturity (N=240)

Approval Repayment Diff

Approval0.187

(0.054)0.257

(0.076)0.070

(0.091)

Repayment0.076

(0.039)0.109

(0.039)0.033

(0.055)

Difference -0.110*(0.066)

-0.147*(0.081)

0.037(0.108)

Ex-Ante Incentive

Ex-P

ost

Ince

ntiv

e

(d) Loan Charged off By Lender (N=239)

Approval Repayment Diff

Approval0.155

(0.048)0.188

(0.054)0.034

(0.072)

Repayment0.047

(0.027)0.092

(0.036)0.045

(0.045)

Difference -0.108**(0.054)

-0.096(0.063)

0.011(0.085)

Ex-Ante Incentive

Ex-P

ost

Ince

ntiv

e

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Penalty interest is charged by the lender if a borrower is late in making an expected payment.

A loan is charged off if the lender deems that there is no probability that it will be repaid. Standard errors in parentheses and p-values

in square brackets. p-values are for a χ2-test of the hypothesis that the difference in differences is equal to zero. Ex-Ante incentive is the

incentive that the referrer faced when choosing a friend to refer. Ex-Post incentive is the incentive that the referrer faced after the loan had

been approved. Approval implies the loan had to be approved in order to earn the bonus and repayment implies the loan had to be repaid

in order to earn the bonus.

20

a base of 16%. Five of the eight estimates are statistically significant from zero, despite our smallsample. In all, the results suggest that small referral incentives create social pressure that lead tolarge reductions in default.

The ”Diff” column in the first two rows of each panel in Table 4 shows an estimate of thescreening effect that is created by moving from the ex-ante approval incentive to the ex-ante re-payment incentive. The point estimate for each of the eight differences is statistically insignificantand positive. So there is no evidence that small referral incentives induce screening that reducesdefault.

The bottom-right cell in each panel of Table 4 estimates the difference-in-differences (DD)across the two different estimates of the referral incentive effects on default rates. Recall fromSection 4 that, of D(A) ≥ 0 and D(A) = D(R) we can rule out positive selection based on thefact that high types are less susceptible to pressure. A zero estimate of the DD indicates thatsusceptibility to pressure is uncorrelated with ex-ante repayment type. And indeed none of thefour estimates is significantly different than zero. It bears emphasizing, however, that these arevery imprecisely estimated zeros: each of the four confidence intervals includes economicallylarge correlations between susceptibility to social pressure and repayment type.

Under the assumption that malleability of susceptibility to social pressure is uncorrelated withrepayment type, we can estimate the enforcement and selection effects with greater precision withregressions that pool across all four treatment arms:

yi = α + β1en f orcei + β2selecti + εi

where yi is one of the four measures of default, en f orcei is an indicator taking on value 1 if client iwas referred by someone with the ex-post repayment incentive, and selecti is an indicator takingon value 1 if the client was referred by a referrer with the ex-ante repayment incentive. Resultsfrom this regression (without controls) are presented in Table 6. For each of the four outcomemeasures we see a large and statistically significant reduction in default associated with the en-forcement incentive, and a smaller and statistically insignificant increase in default coming fromthe selection incentive. These results sharpen the key inferences from the means comparisons inTable 4: there is a large enforcement effect, and no (or a perverse, as discussed below) selectioneffect.

Appendix A shows that these results are robust to various specifications that control for thebaseline characteristics of borrowers or referrers.

6.3 Size of the Enforcement Effect

The enforcement effects we see above are very strong, reducing default by between 9 and 19percentage points in Table 5. It is interesting to ask how the size of the effect compares to theimpact of an incentive given directly to the borrower – rather than to a peer. We have one bitof evidence from a similar context. Karlan and Zinman (2009) conducted a dynamic incentive

21

Table 6: Pooled Impact of Selection and Enforcement Treatments on Key Outcome Variables: OLSWithout Controls

Outcome Measure

Penalty Interest

Not Paid on Time

Portion Owing

Loan Charged

Off

Enforcement -0.188*** -0.094* -0.129** -0.100**(0.061) (0.049) (0.054) (0.042)

Selection 0.067 0.039 0.050 0.040(0.060) (0.047) (0.052) (0.041)

Constant 0.419*** 0.197*** 0.196*** 0.149***(0.054) (0.045) (0.046) (0.039)

N 245 240 240 239

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Penalty interest is charged by the lender if a borrower is late in making an expected payment.

A loan is charged off if the lender deems that there is no probability that it will be repaid. Standard errors in parentheses. Ex-Ante incentive

is the incentive that the referrer faced when choosing a friend to refer. Ex-Post incentive is the incentive that the referrer faced after the loan

had been approved. Approval implies the loan had to be approved in order to earn the bonus and repayment implies the loan had to be

repaid in order to earn the bonus.

22

experiment with a similar, although much larger, South African lender in 2004. That interventionis somewhat different in that the dynamic incentive did not come in the form of a cash bonus, butrather in the form of a reduced rate on a future loan. On average, the dynamic incentive reducedthe interest rate on a future loan by 3.85% and led to a roughly 2.5% point increase in likelihoodthat the current loan was paid on time. This result suggests that to have a similar impact as ourstudy, a direct incentive would need to be very large - in the order of a 12% reduction in theinterest rate (effectively making the interest rate on the next loan zero). This again suggets that atleast part of the enforcement effect in our experiment reflects social pressure, rather than simplythe transfer of cash from the referrer to the borrower.

7 Alternative Explanations

In this section we discuss alternative interpretations of the results.

7.1 Income Effects

In theory, the enforcement effect could be driven by side-payments from the referrer to referredthat produce an income effect on loan repayment. In practice this channel seems implausible,for several reasons. First, the bonus was not paid out until after the loan was repaid, and theborrowers in our sample are liquidity constrained (as evidence by the fact that they are borrowingat high rates). Second, even our smaller point estimates imply default reductions that seem toolarge (about R500 on the average loan) to be explained by a small increase in income (maximumR100). Third, as discussed above, the enforcement effects here are large in comparison to similarestimates when bonuses were paid directly to the borrower.

7.2 Signaling

The repayment rates in Table 5 consistently show that the highest default rates occur for thoseclients that were in the ex-ante repayment group and were moved to the ex-post approval group.In this treatment group, Opportunity phoned the referrer and told her that the bonus would nolonger be paid upon repayment. It is possible that this signaled that the lender was not reallyinterested in repayment. If this explanation is correct, then our estimate of selection conditionalon being in the ex-post approval group would be biased in favor of showing no screening, whileour estimate of enforcement conditional on the ex-ante repayment incentive would be biased infavor of finding an enforcement effect. There are three reasons why this should not be a concern.First, even if we ignore these two means of estimating the effects, the other comparisons supportthe conclusions of the paper. Second, as discussed above, it is never the case that the difference-in-differences is statistically different from zero, implying that these potentially biased estimatesof selection and enforcement are not statistically different from the unbiased ones. Third, andmost importantly, if the signaling story were correct we would anticipate that repayment rates

23

for the referrer would also be affected. The default rate of the “signaled”, minus the default rateof the “un-signaled” are −0.060 (p = 0.414), −0.030 (p = 0.473), −0.019 (p = 0.664) and −0.006(p = 0.895) for the four default measures (interest, balance owing, portion owing and charged-offrespectively) indicating that the data does not support the signaling story. If anything the pointestimates suggest that the “signaled” were better repayers.

7.3 Impatience

Referrers that were assigned to the ex-ante repayment incentive were promised a bonus thatwould not be paid until the referrer repaid their loans. One might therefore expect fewer re-ferrers to make a referral in this treatment group, and/or that those making referrals would bemore patient (and hence be more willing to and effective at enforcing loans). Either differencecould, in principle, create issues for the identification of screening effects. In practice, such issuesdo not loom large. First, the number of referred clients does not differ across the ex-ante treat-ment groups (99 in the ex-ante approval group v. 94 in the ex-ante repayment group p = 0.516).Second, if those referring clients in the ex-ante repayment group were more patient and this im-pacted on how much social pressure they placed on their referreds then we would expect to seeevidence for this in the size of the enforcement effect. As discussed above, there is no evidencefor this.

7.4 Interpretation of the Selection Effect

The interpretation of the screening finding is open to several caveats. First, South Africa has awell established credit scoring system, and our lender has extensive experience with its inter-nal scoring model as well. The extent to which our results would generalize to markets wherelenders rely more heavily on ”soft” information is uncertain. Second, we do find some evidenceconsistent with peers having information about credit worthiness: the lender’s approval rate forclients off-the-street is around 23%, but for clients referred through the Refer-A-Friend programthe approval rate is around 55%. This observation is consistent with two interpretations: i) peersknow which of their friends are creditworthy, but this information duplicates information alreadyheld by the lender; and ii) peers have correlated credit scores and, because the referrers were allapproved borrowers, their peers are more likely to be approved than an average client. These twopossibilities make it hard to give a causal interpretation to the correlation. Third, peers can onlybe useful in screening borrowers if they have multiple friends who need a loan. If this is not thecase then our results do not imply that peers have no information, but rather suggest that this isa market in which peer information is difficult to extract.

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8 Conclusions

We used a novel field experiment to separately assess whether peers have information about thecreditworthiness of their friends and/or can use social pressure to enforce loan repayment. Theaim of the paper is to show that the experiment successfully induces both selection and enforce-ment. The results clearly show enforcement and document that, in the context of South Africanconsumer loans, peers are extremely effective in enforcing payment. The results also suggestthat the experiment was successful in inducing selection – referrers given a selection incentivesubstituted away from referring relatives toward work colleagues. Further, we find no evidencethat our experiment induced a perverse selection incentive. In our setting, while the experimentinduces referrers to try to refer better qualified referrers we see no evidence that they were suc-cessful – our model allows us to interpret this as saying that we find no evidence that referrershave useful information about their friends. This finding must be taken with caution, however, asthe standard errors are large, and we cannot rule out that referrers hold economically importantinformation.

Our findings also have implications for the design of (micro) credit contracts. In particular,the strong enforcement effects suggest that a referral scheme may be a cost-effective comple-ment or substitutes for mechanisms – like group lending – that are designed to mitigate moralhazard/limited enforcement problems. The results also suggest that mechanisms that rely onselection effects are unlikely to be effective in the study location.

Our analysis was based on a novel “two-stage” randomization that follows the basic method-ology of Karlan and Zinman (2009). Unlike that experiment and others like it, our experimentallows for two different estimates of the selection effect. We show that in our setting this featureof the experiment allows us to cleanly identify selection effects even when enforcement effortsare correlated with the “type” that is selected. We hope that this analysis of identification will beuseful for the growing literature that uses multi-stage experiments (e.g. Cohen and Dupas 2010,Ashraf et al. 2010, Beaman and Magruder 2009 and Chassang et al. 2010) .

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Table A.1: Enforcement Effects. The Impact of Ex-Post Repayment Incentive Within Ex-AnteTreatment Group: OLS with Controls for Referrer Characteristics

(a) Ex-Ante Approval Incentive

Penalty Interest

Not Paid on Time

Portion Owing

Charged Off

Ex-Post Approval Left Out Left Out Left Out Left Out

-0.144 -0.188** -0.184** -0.166**(0.097) (0.084) (0.084) (0.068)

Mean in Ex-post

approval

0.389(0.064)

0.206(0.054)

0.186(0.054)

0.155(0.047)

Controls All All All All

N 125 121 121 121

Ex-Post Repayment

(b) Ex-Ante Repayment Incentive

Penalty Interest

Not Paid on Time

Portion Owing

Charged Off

Ex-Post Approval Left Out Left Out Left Out Left Out

-0.208* -0.115 -0.157* -0.128*(0.107) (0.084) (0.091) (0.076)

Mean in Ex-post

approval

0.519(0.069)

0.226(0.058)

0.256(0.076)

0.189(0.054)

Controls All All All All

N 120 117 117 117

Ex-Post Repayment

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Penalty interest is charged by the lender if a borrower is late in making an expected payment.

A loan is charged off if the lender deems that there is no probability that it will be repaid. Standard errors in parentheses. Ex-Ante incentive

is the incentive that the referrer faced when choosing a friend to refer. Ex-Post incentive is the incentive that the referrer faced after the

loan had been approved. Approval implies the loan had to be approved in order to earn the bonus and repayment implies the loan had

to be repaid in order to earn the bonus. Controls: Female, Age, Disposable Income, Salary Occurrence, Education, Application Score, ITC

Score, Job Type, Requested Loan Amount, Requested Term, Branch, Application Month, Application year. All controls are for referrer

characteristics. Categorical variables are entered as fixed effects.

A Robustness to Controls

We now check whether the results are robust to adding controls. We start by estimating theenforcement or screening effect separately using equations of the form:

yi = αi + βTi + γXi + εi, (6)

where yi is again a measure of default, Ti is a dummy variable which takes on value 1 if i is“treated”, and Xi is a set of controls for either referrer or borrower baseline characteristics (thesesets of characteristics are highly collinear). When estimating the enforcement effect here, Ti = 1if the referrer was given the ex-post repayment incentive. We condition on the ex-ante incentiveby running regressions separately for the samples that received the ex-ante approval incentive(Tables A.1 and A.2, Panel (a)) or the ex-ante repayment incentive (Panel (b)). When controllingfor the referred’s application score we include a dummy variable for whether the client came inafter the change in application score procedure and also interact that term with the applicationscore. Tables A.1 and A.2 show that adding controls does not alter the coefficients appreciably.

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Table A.2: Enforcement Effects. The Impact of Ex-Post Repayment Incentive Within Ex-AnteTreatment Group: OLS with Controls for Referred Characteristics

(a) Ex-Ante Approval Incentive

Penalty Interest

Not Paid on Time

Portion Owing

Charged Off

Ex-Post Approval Left Out Left Out Left Out Left Out

-0.100** -0.127** -0.120** -0.115**(0.034) (0.045) (0.039) (0.046)

Mean in Ex-post

approval

0.389(0.064)

0.206(0.054)

0.186(0.054)

0.155(0.047)

Controls All All All All

N 125 121 121 121

Ex-Post Repayment

(b) Ex-Ante Repayment Incentive

Penalty Interest

Not Paid on Time

Portion Owing

Charged Off

Ex-Post Approval Left Out Left Out Left Out Left Out

-0.312** -0.072* -0.066 -0.098*(0.095) (0.033) (0.040) (0.046)

Mean in Ex-post

approval

0.519(0.069)

0.226(0.058)

0.256(0.076)

0.189(0.054)

Controls All All All All

N 120 119 119 118

Ex-Post Repayment

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Penalty interest is charged by the lender if a borrower is late in making an expected payment.

A loan is charged off if the lender deems that there is no probability that it will be repaid. Standard errors in parentheses. Ex-Ante incentive

is the incentive that the referrer faced when choosing a friend to refer. Ex-Post incentive is the incentive that the referrer faced after the

loan had been approved. Approval implies the loan had to be approved in order to earn the bonus and repayment implies the loan had

to be repaid in order to earn the bonus. Controls: Female, Age, Disposable Income, Salary Occurrence, Education, Application Score,

Application Score Post May 2009, ITC Score, Job Type, Requested Loan Amount, Requested Term, Branch, Application Month, Application

year. All controls are for referrer characteristics. Categorical variables are entered as fixed effects.

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Table A.3: Selection Effects. The Impact of Ex-Ante Repayment Incentive Within Ex-Post Treat-ment Group: OLS with Controls

(a) Ex-Post Approval Incentive

Penalty Interest

Not Paid on Time

Portion Owing

Charged Off

Ex-Ante Approval Left Out Left Out Left Out Left Out

0.046 0.046 0.035 0.027(0.041) (0.035) (0.041) (0.031)

Mean in Ex-Ante

Approval

0.389(0.064)

0.206(0.054)

0.186(0.054)

0.155(0.047)

Controls All All All All

N 113 111 111 111

Ex-Ante Repayment

(b) Ex-Post Repayment Incentive

Penalty Interest

Not Paid on Time

Portion Owing

Charged Off

Ex-Ante Approval Left Out Left Out Left Out Left Out

0.007 0.009 0.018 0.028 (0.100) (0.080) (0.075) (0.063)

Mean in Ex-Ante

Approval

0.258(0.054)

0.095(0.037)

0.076(0.039)

0.047(0.027)

Controls All All All All

N 132 129 129 128

Ex-Ante Repayment

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Penalty interest is charged by the lender if a borrower is late in making an expected payment.

A loan is charged off if the lender deems that there is no probability that it will be repaid. Standard errors in parentheses. Ex-Ante incentive

is the incentive that the referrer faced when choosing a friend to refer. Ex-Post incentive is the incentive that the referrer faced after the

loan had been approved. Approval implies the loan had to be approved in order to earn the bonus and repayment implies the loan had

to be repaid in order to earn the bonus. Controls: Female, Age, Disposable Income, Salary Occurrence, Education, Application Score, Job

Type, Requested Loan Amount, Requested Term, Branch, Application Month, Application year. All controls are for referrer characteristics.

Categorical variables are entered as fixed effects.

To test for selection effects we repeat the above exercise with Ti being an indicator for whetherthe referrer was given an ex-ante repayment incentive. The results are reported in Table A.3.In Panel (a) we restrict the sample to those given the ex-post approval incentive and in Panel(b) we restrict the sample to those given the ex-post repayment incentive. For these regressionswe control for referrer characteristics as the referred characteristics are endogenous. Again, theresults are robust to including controls.

Finally, we again pool the data and assume that the enforcement and selection effects areindependent of each other. That is we run the regression

yi = α + β1en f orcei + β2selecti + β3Xi + εi

where Xi is a set of controls. In this case we can only control for referrer characteristics as onceagain the referred characteristics are endogenous. Table A.4 contains the results, which do notdiffer significantly from those reported in Table 6 without controls.

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Table A.4: Pooled Impact of Selection and Enforcement Treatments on Key Outcome Variables:OLS With Controls (same as Table 6 but with controls)

Outcome Measure

Penalty Interest

Not Paid on Time

Portion Owing

Loan Charged

Off

Enforcement -0.168*** -0.117** -0.130** -0.109**(0.065) (0.055) (0.054) (0.047)

Selection -0.009 0.021 0.018 0.032(0.074) (0.061) (0.062) (0.053)

Mean in Left Out

0.389(0.064)

0.206(0.054)

0.186(0.054)

0.155(0.047)

Controls All All All All

N 245 240 240 239

∗∗∗ ⇒ p < 0.01, ∗∗ ⇒ p < 0.05, ∗ ⇒ p < 0.1. Penalty interest is charged by the lender if a borrower is late in making an expected payment.

A loan is charged off if the lender deems that there is no probability that it will be repaid. Standard errors in parentheses. Ex-Ante incentive

is the incentive that the referrer faced when choosing a friend to refer. Ex-Post incentive is the incentive that the referrer faced after the

loan had been approved. Approval implies the loan had to be approved in order to earn the bonus and repayment implies the loan had

to be repaid in order to earn the bonus. Controls: Female, Age, Disposable Income, Salary Occurrence, Education, Application Score, ITC

score, Job Type, Requested Loan Amount, Requested Term, Branch, Application Month, Application year. All controls are for referrer

characteristics. Categorical variables are entered as fixed effects.

32