ISSN: 2038-7296POLIS Working Papers

[Online]

Dipartimento di Politiche Pubbliche e Scelte Collettive – POLISDepartment of Public Policy and Public Choice – POLIS

POLIS Working Papers n. 180

February 2011

Microcredit and poverty.An overview of the principal statistical

methods used to measure the program net impacts

Cristina Elisa Orso

UNIVERSITA’ DEL PIEMONTE ORIENTALE “Amedeo Avogadro” ALESSANDRIA

Periodico mensile on-line "POLIS Working Papers" - Iscrizione n.591 del 12/05/2006 - Tribunale di Alessandria

Microcredit and Poverty. Anoverview of the principal statisticalmethods used to measure theprogram net impacts.

Cristina Elisa Orso�

Abstract

The purpose of this paper is to examine di¤erent economet-ric approaches aiming to evaluate the impact of microcredit onpoverty. Starting with a brief description of microcredit and themost common kinds of statistical biases connected to these stud-ies, I describe the principal characteristics of Non-Randomizedand Randomized approaches, in order to highlight strengths andweaknesses concerning the application of such methodologies.JEL-Classi�cation: C54, C58.Keywords: Microcredit, poverty, program impact, random-

ized approach, non-randomized approach.

�Ph.D. Student in "Economic Policy", Department of Economic and Social Sci-ences, Catholic University, Piacenza. E-mail: cristina.orso@unicatt.it

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1. IntroductionScienti�c testing of the net impact of microcredit is very di¢ cult.

It is possible to identify a speci�c question which represents thecore of every serious impact study: if we �nd out that people whohave obtained loans are doing better than those who haven�t, doesit necessarily mean that receiving loans caused the positive change?

In other words, the problem is to understand how outcomes havechanged with the program compared to what would have happenedwithout the program implementation.

The most important challenge, in this particular context, has beento determine a control group for comparison; it is very hard toidentify a group of people who are like the program participantsin all relevant features apart from not having received funds. Thecritical issue to evaluate how micro�nance works is the measure-ment of the net e¤ects caused by the programs.

As outlined by Armendàriz, Morduch (2010), the �rst contribu-tions of microcredit impact literature mainly concerned non-experimentalmethods. In this context, researchers use treatment and con-trol groups, but do not randomly assign subjects to the groups.The critical point in such studies is to establish causality relation-ships. Moreover, biases from omitted variables, non-random pro-gram placement, client selection and self selection, and attritionlead to important estimation problems (Karlan, 2001).

Some kinds of biases can be reduced by using longitudinal data.The e¤ects of non-random participation and non-random programplacement, under speci�c assumptions, can be mitigated by theimplementation of this strategy. But if there are unobservable vari-ables that change over time, attributes hard to measure such asentrepreneurial organization and business skills are probably cor-related with participation status. The most popular longitudinalstudies have been sponsored by USAID in the second part of 1990s.Researchers investigated net impacts on members of three di¤erentinstitutions: a microlender organization operating in the informalsector (SEWA) located in Ahmedabad (India), an ACCION In-ternational a¢ liate (Mibanco) situated in Peru and the ZambukoTrust in Zimbabwe. The sample households were observed a �rsttime to collect baseline data, and then, after two years, they wereresurveyed (Armendàriz, Morduch, 2010).

Some empirical work is based on household surveys from the WorldBank and the Bangladesh Institute of Development Studies in

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Bangladesh. The studies that exercise the most in�uence on theresearch community are Pitt and Khander (1998) and Khander(2005). As regards PK approach, they use cross-section data (fromthe three seasonal rounds in 1991/1992), while Khander takes intoaccount the panel dimension of the data set (he also uses the 1999round) in order to strengthen identi�cation. To follow, many otherstudies are based on this data set. We report, for instance, Khan-der (1996, 2000), Pitt et al. (1999), McKernan (2002), Pitt andKhander (2002), Pitt et al. (2003), Menon (2005), and Pitt, Khan-der and Cartwright (2006).1

Concerning experimental approach, randomized controlled trials(RCTs) , when done correctly, can really provide credible andtransparent estimates in di¢ cult contexts. Such approach consistsof giving loans to a subgroup randomly drawn from the population( for instance through a random algorithm to select people from alist), while the other subgroup, also randomly selected, will not ob-tain any funds.Using randomized approach, the di¤erence in termsof average outcome between the two distinct groups represents agood estimate of the program�s average impact. Under determinateassumptions, the result can be interpreted as the causal impact ofmicrocredit introduction.2

However, we must notice that it is an average impact; therefore,if half of the participants gains by 100 percent while the otherhalf loses by 100 percent, the average impact will be zero. In asimilar context, zero is a clean estimate of the average impact, butit doesn�t give us any relevant information about an individual�sperformance.

In order to obtain credible estimates, it is important that neitheragreement to participate in the experiment nor the tendency todrop out are systematically related to outcomes of interest.

Randomization approaches also have limits: few published exper-imental studies of micro�nance have been able to highlight short-term results only.

Banerjee et al.(2009) and Karlan and Zinman (2009) looked at mi-crocredit participants over a short period of time ( 12-18 months).They didn�t �nd any kind of improvement in household incomeor consumption, but both the studies showed some other bene�ts.

1For a more complete literature review, see Armendàriz, Morduch, 2010.2Because of RCTs implementation, loans represent the only ex-ante di¤erence

between the treatment and the control groups.

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The former concerns a randomized evaluation on the community-level impact of the introduction of new branches of a local micro�-nance bank. The baseline sample was randomly selected from ur-ban Hyderabad (India) for the opening of newmicro�nance branches.

Before new institutions opened, 69 percent of the households had atleast one outstanding loan from informal channels (moneylenders,family, friends). The authors found that the new branches settle-ment caused, in the interested areas, more new business openings,higher purchases of durable goods and relevant pro�ts in existingbusiness activities. However, it�s important to note that the maine¤ects concern target households starting new businesses, and theauthors can�t tell if the funds are actually invested in businessactivities or not.

Interestingly, Dupas and Robinson (2009) conducted a randomized�eld experiment in Kenya that found short-term welfare improve-ment regarding micro-savings, not microcredit.

They gave interest-free savings accounts in a local micro�nanceinstitution to a random sample of small entrepreneurs; these ac-counts did not pay interest and charged withdrawal fees, but theyrepresented the only opportunity for formal savings in the area.

The results suggested wide variation in the intensity of formal ac-count usage. Some microentrepreneurs did not accept the pro-posal, and many accepted without using the account e¤ectively;roughly 50 percent of those with accounts used them only rarely,and only a small minority used them frequently.

Clients of this service increased their investment and daily expendi-tures for women, but there was no evidence in terms of men impact.However, this study presents a few shortcomings: �rst, the randomsample is small (185 microentrepreneurs) and only few clients usedthe account frequently. Moreover, the target area of experimentwas limited to a single site and to a single micro�nance bank .

Karlan and Zinman (2008) conducted a randomized experiment inSouth Africa. The authors asked loan o¢ cers of a local lender torevalue and accept applicants for a microloan from a set who wereinitially refused but who got just below the cutt-o¤.

Many applicants who were reconsidered (but not all) showed in-come improvements and a more positive outlook on the future.Despite of a micro-entrepreneur set rejected and not reconsidered,they registered a higher level of stress and depression.

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The results of this study can�t generalize to other micro�nancecontexts, because the loans were consumer loans, not typically usedfor investments in business activities. In addition, applicants werenot very poor, and interest rates were higher than those appliedby typical micro�nance institutions (Rosenberg, 2010).

The remainder of this paper is organized as follows. The nextsection provides a brief description of microcredit and its princi-pal objectives, among which poverty alleviation. Section 3 gives asketchy outline of the problems arising from reverse causation andselection bias in order to discuss about the econometric method-ologies to use. Section 4 and section 5 respectively describe thetwo distinct empirical approaches, examining the results reachedin both �elds on the basis of recent literature. Section 6 com-pares randomized and non-randomized strategies. The last sectionconcludes with a discussion of the principal impact issues.

2. De�nition and aims of MicrocreditAccording to its basic de�nition, microcredit involves small loansto poor people for self employment projects that produce income,allowing them to care for themselves and their families.3 Theseindividuals, also called "unbankable", lack any kind of economiccollateral and a veri�able (and valuable) credit history to o¤er atraditional bank. Hence, they cannot meet the basic quali�cationsrequired to access formal credit. Microcredit can be considered a�eld of micro�nance, which embraces the provision of a wider rangeof �nancial services designed for the very poor. As highlighted byArmendariz, Morduch (2010), recently the terms microcredit andmicro�nance have often been used interchangeably even if theyshow some remarkable di¤erences. The original focus on microcre-dit mainly concerned poverty reduction and social change, and themost important institutions involved were NGOs. Then, the shifttomicro�nance arose from the growing need of poor households fora broader range of �nancial services (like savings) and not exclu-sively credit for entrepreneurial activities. As a result, this lexicaltransition has produced an orientation change, toward less poorpeople and toward a di¤erent kinds of organizations, commerciallyoriented and with strong �nancial regulations.

The termmicrocredit is often used in distinct contexts (rural credit,agricultural credit, consumer credit, etc.) with di¤erent implica-tions. In order to clarify the target and the speci�c objectives of

3http://w.w.w.microcreditsummit.org

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the programmes, we introduce a broader classi�cation to identifythe various categories.

On the basis of Yunus taxonomy4, it is possible to identify �vedi¤erent kinds of microcredit:

- Traditional informal microcredit (moneylender�s credit, pawnshops, loans from friends and relatives, consumer credit in infor-mal markets). Amongst those of that sector local moneylenders arean important source of credit to those borrowers usually refusedby most �nancial institutions because of their particular economicconditions. Low income and lack of collateral and stable employ-ment do not make borrowers creditworthy in the eyes of traditionalbanks. Moneylenders are better at serving clients neglected by theformal sector because they have a considerable market knowledgeand lower transaction costs. At the same time, they can easilymonitor borrower behaviour because of their proximity to the clientand reliable information about his or her status. Poor people turnto moneylenders mainly for consumer loans or to cope with emer-gencies like health problems or to pay for high outlay connectedwith education, wedding, funerals, and so on. Hence this sourceof credit cannot be considered a valid engine of inclusion and localgrowth.

- Microcredit based on traditional informal groups (tontine, ROSCA).Tontine can be compared to our life insurance. The basic schemeis simple. Each participant contributes a sum of money to the ton-tine and, then, he receives an annual dividend on his investment.When each participant dies, his or her share is reallocated amongthe surviving subscribers, until only one investor survives. ROSCA(Rotating Savings and Credit Association) consists of a group of in-dividuals who agree to meet for a speci�c period of time in order tosave and borrow money from a common "pot", usually allocated toone member of the group (who changes each period). Both kindsof microcredit pursue partially di¤erent objectives compared tomodern microcredit. The aim of tontine concerns insurance, whileROSCAs �nance consumer credit (Armendàriz-Morduch, 2010).

- Microcredit through traditional banks, generally specialised inspeci�c investment sectors (agricultural credit, livestock credit,�sheries credit, handloom credit, etc.).

- Cooperative microcredit and rural credit through specialised banks.

4http://www.grameen-info.org

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- Modern microcredit (Grameen credit, bank-ONGs partnershipbased microcredit and consumer microcredit). Small loans typi-cally designed for low-income clients who traditionally lack accessto commercial banking for several reasons (absence of collateral,informal employment, unveri�able credit history, high transactioncosts). This kind of credit allows poor people to start new en-trepreneurial activities, expand existing businesses, to cope withshocks due to adverse climatic conditions and illness, and smoothout consumption.

Concerning the last category of microcredit, three models for lend-ing have become globally popular: village banking, solidarity groups,and individual lending. The choice of lending technology relies onthe speci�c characteristics and needs of the target areas.

The village banking approach is most similar to the old cooperativecredit movement. This method was innovated by FINCA Interna-tional founder, John Hatch. A village bank is an informal self-helpsupport group of 20-30 participants ( predominantly women). The�rst loan comes from an institution like MFI or NGO, then follow-ing deposits come from individual savings amounts in group funds.For example, if the �rst loan is $ 50 and the participant saves inthe same period $ 10, the second loan will be equal to $ 60. Thelength of the loan cycle is 4-6 months5. SHGs (self-help groups)have dominated the micro�nance landscape especially in India.These involve small groups of 10-20 members that collect savingsfrom their participants and, at the same time, provide them withloans. The members are jointly and severally liable for the fundsobtained within the group itself (Nair, 2005).

Solidarity groups is a lending mechanism which allows a group ofpeople to provide collateral through a group repayment pledge6.Usuallyborrower groups are made up of three to seven members, most com-monly �ve7, and the patterns of disbursements and repayments is

5For detailed information, see:http://en.wikipedia.org/wiki/Village_Banking6http://www.accion.org/ Group_Lending7Five is the right size of a Grameen group. Grameen Bank (or Rural Bank)

was started by Muhammad Yunus, a Professor of the University of Chittagong(Bangladesh) in 1976. The bank mainly targeted rural women for its credit pro-grammes. It introduced group lending strategy to make credit available to the poor,usually denied by commercial loans because of the lack of physical collateral. Theincome-generation also aims to empower the women and increases their participa-tion in household decisions. For more details about its "mission" and history, seeArmendàriz, Morduch, 2010, chapter 4.

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regimented. According to the Grameen model, payments start im-mediately after disbursement every week. In practice, the �rst twoparticipants take their loans and begin with repayment, then twomore, and �nally the �fth. The eligibility to further and largeramounts of funds is subject to the repayment of all group loans.Each borrower is responsible for the repayment of all the otherloans within the group (joint liability). The advantages of thismethodology concern lenders and customers. First, it is conve-nient for villagers because the bank comes to them (as in the casesof ROSCAs and local moneylenders), avoiding logistic and admin-istrative problems. At the same time, for the lender, transactioncosts connected to loan disbursement are considerably reduced.Although this methods boasts some evident strengths, the higherlikelihood of group failure in the event of a single default, the hugetraining costs and the greater �nancial responsibility for others ina group have to be taken into consideration when looking into itsimplementation (Armendàriz, Morduch, 2010).

The case of individual lending substantially di¤ers from previousapproaches. Typically, microcredit is associated with group struc-tures (solidarity groups or village banks). Whilst the �rst twolending models serve the poorest, individual lending serves lesspoor clients. This targeting choice arises from the high costs ofunderwriting new loans, monitoring behaviour and repayment ofdisbursed funds, and enforcing repayment process. Group lend-ing strategies, as mentioned above, shift much of the responsibil-ity onto borrowers, while lending to individuals involves (for theMFI) managing these costs directly. Interestingly, however, somemicrocredit institutions do not o¤er group but individual loans.BDB (Bank Dagang Bali) and BRI (Bank Rakyat Indonesia), twoIndonesian private banks, are revealing examples of individual mi-cro�nance8. As in conventional lending, loan o¢ cers take collateraland collect information from credit bureaus, require pledges of ti-tle to land or to other property. Sometimes, the individual lendingis a part of a larger "credit plus" program, where other particu-lar kinds of services (such as skill development, education, health,etc.) are provided.

To sum up, it is possible to highlight some general key objectivesof the microcredit programmes:

(a) to provide small loans to poor people at lower cost than infor-mal sources;

8For more detailed information, see Armendàriz, Morduch, 2010.

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(b) to avoid exploitation of the poor due to the growth of informalcredit channels;

(c) to reach the "unbankable" that cannot be �nanced by tradi-tional banks (because of the lack of collateral);

(d) to empower women both within the household (as decisionmakers) and in society (through active economic and political par-ticipation);

(e) to improve employment opportunities;

(f) to reduce poverty, increase growth and improve the living con-ditions on sustainable perspectives.

As regards the last point, microcredit is gaining importance asan e¤ective tool of poverty alleviation. Impact evaluations aimto investigate the role of credit access in terms of poverty reduc-tion. Although some interesting research9 analyzes the e¤ects ofmicrocredit programmes through a multidimensional poverty per-spective10, �nancial outcomes remain the core matter in many rel-evant impact studies. The lack of reliable data and the selectionproblems connected with empirical evaluations represent a seriouscomplication to estimate microcredit consequences.

3. Econometric impact evaluations: selection bias and causal-ityMicrocredit and the other micro�nance services can a¤ect individ-uals and households in many di¤erent ways. The �rst question

9Karlan, Zinman (2010) conducted an interesting study using an experimentalapproach. They measure the impact of microcredit programmes (in Manila) also interms of subjective well-being using indicators such as life satisfaction, job satisfac-tion, decision making power, optimism, etc. In addition, the authors investigated thetreatment e¤ects on di¤erent kinds of human capital.As mentioned in the introduction, Karlan and Zinman (2008) created another inter-

esting experiment aiming to estimate impact e¤ects of microcredit in South Africa.In addition to �nancial impact measures (such as income and consumption), theyconsider particular types of indices concerning health aspects (physical and mentalhealth index) and decision- making process, optimism, and position in the commu-nity socio-economic ladder (this information comes from subjective perceptions ofsample households).

10Multidimensional poverty involves a group of deprivations that cannot be ade-quately expressed as income insu¢ ciency. It refers to speci�c composite measures,such as the Human Poverty Index, that accounts for well-being indicators (like adecent standard of living, a long and healthy life, knowledge). For more details, seeTsui, 2002.

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that researchers have to ask is the following: what are we tryingto measure?

Concerning the impact of microcredit, we distinguish between twodi¤erent e¤ects:

(a) an income e¤ect, that makes households wealthier and pushesup consumption levels (it can also increase the demand forchildren, health, children�s education, spare time);

(b) a substitution e¤ect, which may counterbalance the incomee¤ect. In fact, with increased female employment rates, hoursspent raising o¤spring can be costlier in terms of foregoneincome, driving birth levels down.

But increasing income and consumption are not the only metric ofjudgement of microcredit impact.

As argued in a interesting book, Portfolios of the poor: How theWorld�s Poor live on $2 a day (Collins, Morduch, Rutherford, andRuthven, 2009), the poor tend to use credit and savings not onlyin order to smooth consumption, but also to cope with emergen-cies like health problems and pay for expensive services such aseducation, weddings, or funerals.

A lot of studies have looked at the experience of people who haveobtained microloans.

In order to have a clean estimate of evaluating impacts, the statis-tical problem is to separate out the causal role of microcredit pro-gram. In other words, it is necessary to gauge microcredit e¤ectseliminating the various reverse causation and selection biases.

As regards causality, researchers have to answer fundamental ques-tions. For example, if they note that wealthier households havelarger loans, they have to ask if the loans enrich the households ordo richer households merely have less di¢ culty in accessing credit,without a substantial increase in their productivity (Armendàriz,Morduch, 2010).

The challenge has been to identify an appropriate control groupfor comparison; we have to ask if changements as new business,new saving accounts, further education for children, etc. are due tothe program implementation or would have happened also withoutmicrocredit introduction.

We can summarize the e¤ect produced by a speci�c treatment (T )on a characteristic Y ( in order to understand whether and in

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what size the treatment may be considered a determinant factorof Y ) as follows11:

� = E(Y 1i =Ti = 1)� E(Y 0i =Ti = 0)12 (1)

In this context, the causal e¤ect is measured as the di¤erence be-tween the outcome that would be observed if unit i received thetreatment (E(Y 1i =Ti = 1) ), and the outcome of receiving no treat-ment of any kind (E(Y 0i =Ti = 0)).

Econometric methods attempting to estimate how much of thedistinct outcomes between treatment and control groups attribut-able to the program are a crucial tool in microcredit interventions,especially in non-experimental settings. The question that everyevaluation seeks to solve is how would partecipants have done inabsence of intervention. As well argued in Holland (1986), the fun-damental problem of causal inference concerns the impossibility ofevaluating, at the same time, treatment and no treatment, thatis T i = 1 and T i = 0; obviously, it is not possible observing theresults obtained on the same unit from the two di¤erent situations( E(Y 1i =Ti = 1) and E(Y

0i =Ti = 0)) in order to gauge the causal

e¤ect of T on Y.

Di¤erent counterfactual statistical estimation methodologies haveto be implemented on the basis of the speci�c evaluation context.

In particular, we imagine to have to measure the causal impactof microcredit on borrower income. The income level can be at-tributed to di¤erent kinds of sources: measurable attributes, forexample, like job, business, pension, age, education and experi-ence, that are generally available.

But another category of personal characteristics is hard to measure,for instance organizational ability, entrepreneurial skills, access tovaluable social networks. In this latter category, we include eco-nomic shocks, and other types of casual events that could a¤ecthousehold outcomes (Armendàriz, Morduch, 2010).

In addition, a further set of attributes may be useful in order toestimate microcredit impact, such as village size, or the existenceof scale economies related to speci�c production (actually, this kindof information is measurable but not gathered in surveys).

11See Du�o, Glennetster, and Kremer (2007)12where "�" represents the measure of the impact, E (Y1i /T i = 1) is the expected

value of the outcome variable observed after treatment on target units, while E( Y0i/T i = 0) is the expected value after program implementation on control group.

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Estimating microcredit impact implies separating out its role fromthe roles of all these di¤erent attributes.

Bank o¢ cers work hard to screen potential ranges of customers,and calculate the optimal locations for new branches; loans arethought to attract the most gifted individuals, who choose to parte-cipate or not in a microcredit program on the basis of personal andstrategic reasons (in particular, on the basis of perceived returns).

If target clients are wealthier and more productive than the non-treated group, it could be attributed to the strategic placement ofthe intervention, not to the active role of the micro�nance institu-tion in making these conditions. Hence, a high correlation betweenmicrocredit participation and, for example, the variables age andentrepreneurial ability is very probable.

In this context, if investigators manage measurable attributes (likeage), there are simple strategies in order to control for age-relatedissues, but when there are typical unmeasurable attributes, such asentrepreneurial ability researchers have to be cautious in makingcomparisons between ex-ante and ex-post situations. The e¤ect ofbeing a good microentrepreneur could incorrectly be interpretedas an impact of program access (Armendàriz, Morduch, 2010).

The counterfactual estimation (and, at the same time, the im-pact estimation) can be a¤ected by relevant problems, indicatingas threats to validity (Bartik and Bingham, 1995). Concerningimpact evaluations, the essential problem is the risk that the com-parison between the target and the control group might be contam-inated by factors which inhibit the untreated units from simulatingthe without-intervention situation (selection bias).

The problemwith comparing microcredit participants to non-participantsis that participants are self-selected and therefore not comparableto the non-participants. Many microcredit clients already haveinitial advantages respect to their neighbors.

In other words, program target units may have systematic di¤er-ences compared to the control group units, and these di¤erencescould cause a biased evaluation of the intervention results.

Formally, if we consider equation (1) as a de�nition of programimpact, and we subtract and add the term E(Y 0

i =Ti = 1) , weobtain

� = E(Y 1i =Ti = 1)�E(Y 0i =Ti = 1)�E(Y 0i =Ti = 0)+E(Y 0i =Ti = 1)� = E(Y 1i �Y 0i =Ti = 1)+E(Y 0i =Ti = 1)�E(Y 0i =Ti = 0) (2)

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The term E(Y 1i �Y 0i =Ti = 1) is the treatment e¤ect; the other termE(Y 0i =Ti = 1)�E(Y 0i =Ti = 0) represents the measure of selectionbias. It captures the di¤erence in potential untreated outcomes be-tween the target and the control groups. Treated units may havehad di¤erent results on average even if they had not been treated.The bias can move in two distinct directions: if, for instance, pro-gram participants are more motivated in seeking goals, have high-level entrepreneurial skills, or live in a richer geographic area, theyare more likely to achieve good results in terms of outcomes. Inthis case, E(Y 0i =Ti = 1) could be larger than E(Y

0i =Ti = 0) . On

the other hand, if the treatment implementation arises in partic-ularly disadvantged communities, with an higher rate of poverty,the term E(Y 0i =Ti = 1) would be smaller than E(Y 0i =Ti = 0).The crucial point is that in addition to any kind of treatment e¤ectthere may be systematic di¤erences between participants and nonparticipants (Du�o, Glennerster, Kremer, 2007).

Given that the term E(Y 0i =Ti = 1) represents the expected out-come for a borrower who received a loan, if he had not receivedthe loan, such term is not directly observable and we don�t as-sess the size (and the sign) of the selection bias. Many empiri-cal papers aim to identify in what cases selection bias does notexist or �nd strategies to correct for it (Armendàriz, Morduch,2010).

4. Non-randomized approach4.1 The estimation strategy

The main contributions of recent literature use innovative researchdesigns to overcome selection bias problems.

Following Coleman�s study (1999), we initially analyse a standardempirical speci�cation concerning the evaluation of program im-pacts in the micro�nance framework.

We start from the following speci�cation:

Bij = Hij�B + Lj�B + �ij; (3)

Yij = Hij�Y + Lj�Y +Bij�Y + �ij (4)

where Bij represents the amount borrowed from the village bankby household i in village j, Hij is a vector of household attributes,Lj is a vector of village characteristics and Yij is an outcome onwhich measuring the impact. The parameters �B; �B; �Y ; �Y ; �Yhave to be estimated during the analysis. The error terms �ij and

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�ij represent unmeasured household and village attributes that de-termine microcredit participation and outcomes, respectively. Theparameter �Y measures the causal impact of a microcredit pro-gram on the outcome Yij.

A crucial assumption in order to obtain unbiased econometric es-timation of the parameters is that the error terms �ij and �ij areuncorrelated. If this assumption is violated, the estimate of theparameter of interest (�Y ) will be biased. This kind of correla-tion can arise from (a) self-selection into the village bank and (b)nonrandom program placement.

Concerning the �rst source of correlation, we consider a sampleof households selected only from communities with a local bank.Some households will receive loans, while others will not partici-pate in a microcredit program (on the basis of speci�c eligibilitycriteria). In this context, a correlation between �ij and �ij is al-most certain; for example, if the more promising households areselected to be borrowers , the unmeasured "entrepreneurial abil-ity"might a¤ect both the choice to become a program participantand the impact estimation of the outcomes.

As regards the second source of correlation, we imagine to have an-other common kind of sample made up of households from a villagewith a local bank and randomly drawn households from communi-ties without any village bank. If the placement of the local bank isnot random, it is more likely that �ij and �ij are correlated acrossdi¤erent villages. To illustrate this situation, consider a simpleexample: we suppose that an NGOs has to decide where placinga village bank, on the basis of its own criteria. Presumably, theinstitution will choose more entrepreneurial or better organizedcommunities, with a higher level of income, then the terms �ij and�ij will be correlated.

Mo¢ tt (1991) proposes three standard procedures used in the caseof correlation between �ij and �ij . The �rst concerns the instru-mental variables approach. The identifying instruments might bedeterminants of participating in the microcredit program, but notdeterminants of the impact measure13.

The second strategy regards the introduction of panel data, in or-der to take into account the pretreatment systematic di¤erences inoutcome variables. But collecting a panel dataset is often di¢ cultand costly.

13This will be covered in more detail later.

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Finally, the third method suggested by Mo¢ tt concerns assumingan error distribution (usually a normal distribution) of the outcomevariable in absence of any kind of treatment. Then, the impactof the micro�nance intervention can be de�ned by measuring thedeviations from normality of the variable of interest within thetreated units. This procedure involves three relevant problems:

(i) In many contexts, researchers haven�t su¢ cient information onwhich to base assumptions about the error distribution;

(ii) The impact estimation is highly sensitive to the initial assump-tions about the error distribution;

(iii) If analysts use, for instance, a censored regression (Tobitmodel), the identi�cation of the impact e¤ects is sometimes im-possible14.

14The Tobit model is appropriate when the dependent variable is censored at someupper or lower bound because of the way the data are collected (Tobin, 1958, Mad-dala, 1983). If we decide to censor at a lower bound, the empirical speci�cation willbe:Y�ij = Xij� + �ij (1)Yij= Y�ij if Y�ij > 0 (2)Yij=0 if Y�ij 6 0 (3)where Y�ij is an unobserved continuous latent variable, Yij is the observed variable,

Xij represents the vector of the independent variables, �ij is the error term and �is a vector of coe¢ cients. In addition, we assume that the error term is uncorre-lated with the vector Xij and is independently and identically distributed. We cangeneralize the model by introducing a known nonzero constant in equation (2) and(3), in substitution of the threshold zero. Variations of the censoring point acrossobservations may happen (Winship, D.Mare, 1992).OLS estimation of the �rst equation involves a selection bias problem. In fact, for

the set of information Yij > 0 , the above model implies:Yij = Xij� + E

��ij j Y �ij > 0

�+�ij

= Xij� +E[�ij j �ij > �Xij�] + �ij : (4)�ij represents the di¤erence between �ij and E

��ij j Y �ij > 0

�and is uncorrelated

with both terms. We note that E[�ij j �ij > �Xij�] in equation (4) is a function of�Xij� . The less the rate of censoring (that is �Xij� ), the greater is the conditionalexpected value of the error term �ij . In this context, the OLS regression estimatesare biased and inconsistent because of the negative correlation between �Xij� and�ij . It is possible to construct a similar equation to the (4) for observations forwhich Yij = 0 , generating a parallel analysis, but the inclusion of observation forwhich Yij = 0 leads to analogous inconveniences. Starting from the analysis ofequation (4), Heckman (1979) shows how selection bias may be thought of as anomitted variable bias. Speci�cally, the term E

��ij j Y �ij > 0

�can be interpreted as

an omitted variable correlated with Xij and that a¤ects the outcome. Hence, biasedand inconsistent OLS estimates of the vector coe¢ cients (�) hinge on its omission(Winship, D.Mare, 1992).

15

4.2 The Coleman alternative speci�cation

Coleman (1999) introduces a new approach consisting of usinginformation on future clients before the microcredit program isstarted. The author exploits a particular way a microcredit in-tervention was implemented in Northeast Thailand and suggestsan interesting way to address selection bias. The author gath-ered data on 445 households in fourteen communities. Of these,only eight had local banks beginning their activity at the start of1995 .The other six did not, but local village banks will be set upa year later. The "control" village bank households would have,presumably, the same unobservable characteristics as the "treat-ment" group of village bank members who had already receivedthe loans. Moreover, members and non-members of control andtreatment villages were surveyed.

Taking into account this survey design, Coleman(1999) estimatesthe following regression equation15:

Yij = Hij�Y + Lj�Y +Mij + Tij� + �ij (5)

This kind of approach allows a re�nement of the di¤erence in di¤er-ence method16. In particular, the dummy variables are introducedto control for membership status and location of the intervention.Speci�cally, Mij represents a dummy variable equal to 1 if house-hold i in village j self-selects into the microcredit program, and0 otherwise. The term Tij is another dummy variable equal toone if a self-selected member has already bene�ted from the creditinterventions, and 0 otherwise. In this speci�cation, the variables

15The author replaces equations (3) and (4) by an unique impact equation.16Di¤erence-in-di¤erence designs use pre-intervention di¤erences in outcomes be-

tween treatment and comparison group for control for unobserved heterogeneity be-tween the groups, when data are available both before and after the intervention.Consider YT1 the potential outcome in the case of treatment (YC1 corresponds tothe case of no treatment) in period 1, after the program implementation. Then, wedenote by Y T0 the potential outcome if the subject is treated ( Y C0 if the subjectis not treated) in period 0, before the program occurs.Subjects belong to group T or group C, and the T group is treated in period 1

and untreated in period 0. The control group (C) is never treated. Formally, thedi¤erence-in-di¤erence estimator is:DD=

hE�Y T1 j T

�� E

�Y C0 j T

�i�hE�Y C1 j C

�� E

�Y C0 j C

�iUnder the assumption that

hE�Y C1 j T

�� E

�Y C0 j T

�i=h

E�Y C1 j C

�� E

�Y C0 j T

�i; this estimator provides an unbiased estimation

of the program impact (Du�o et al. 2007).

16

of most interest are Mij and Tij. Coleman suggests that Mij canbe interpreted as a proxy for the unobservable attributes, whichleads subjects to self-select into the local bank. In other words,Mij captures the unobserved variables that caused the correlationbetween �ij and �ij across households. The variable Tij repre-sents the number of months that the loans of the village bank wereavailable to members who have self-selected, which is exogenousto the household. Following Coleman (1999), we argue that Mij

controls for selection bias in order to obtain a consistent estimateof the causal treatment impact described by � , the coe¢ cient ofTij.

Coleman�s �ndings suggest that average treatment e¤ects werenot signi�cantly di¤erent from zero after checking for endogenousmember selection and microcredit program placement. In addi-tion, the author expands the estimation frame to distinguish be-tween impacts on "rank-and-�le members" and members of thelocal bank committee (who are, usually, wealthier); the resultsshow that most program impacts were not statistically signi�cantfor rank-and-�le members, while there were some relevant impactsfor the committee members in terms of wealth accumulation.

However, the study needs to be put into the larger �nancial out-look. Thai villagers are relatively wealthier than, for example,Bangladeshi villagers, and have an easier access to credit, fromdi¤erent sources. In this analysis, the village banks� loans maybe too small to produce relevant average di¤erences in the welfareof households. Coleman recognizes that one reason that wealth-ier borrowers may have performed consistent impacts was becausethey could manage larger loans.

4.3 Quasi experimental designs: Bangladesh studies

As mentioned above, a di¤erent approach to overcome statisticalproblems may be searching for an instrumental variable for mi-crocredit program participation. This strategy allows analysts toaddress some kinds of omitted variable bias, reverse causality andproblems arising frommeasurement error17. In practice, the instru-mental variables method consists in �nding an additional variableor set of variables that gives an explanation for levels of creditreceived, but that has no correlation with the error term in theregression framework. Then, the proxy variable formed on thebasis of the instrumental variable approach can be use to extract

17For a more detailed discussion about instrumental variables strategy see Greene,2008, Part III.

17

the causal impact of credit access. To �nd appropriate instru-mental variables for microcredit is complex. But when we havewithin-village variation in program access the basis of the eval-uation methodology can be the eligibility rules (this is the ap-proach using in some important studies of micro�nance impact inBangladesh).

The most-famous studies about microcredit impacts on householdsare based on a survey �elded in Bangladesh in the 1990s.

Pitt and Khander (1998) develop a framework for estimating im-pact e¤ects using the �rst round of data (1991-1992 cross-section).They analyze surveys of 1,798 households in 89 villages randomlydrawn within 29 upazillas18 of Bangladesh. The starting pointis that the observations concerning the three programs evaluated(Grameen Bank, BRAC, and the state-run Rural DevelopmentBoards (RD-12)) all answer the same eligibility rule19. To focusthe attention on the poorest, all the three program formally de-�ned eligibility rule in terms of land ownership: households havingover half an acre of land are not allowed to borrow.

Following PK estimation set-up, the crucial feature of the estima-tion problem is that the credit variables are potentially endogenousand censored. Moreover, outcomes of interest as labour supplyand girl�s school enrolment are censored or binary. To estimateimpact parameters, PK use a limited-information maximum like-lihood (LIML20) framework, that takes into account instrumentalvariables and handles censoring. According to the kind of out-come, the model will be as continuos and unbounded (householdconsumption), Tobit (female and male labour supply per month,female non-land assets), or Probit (school enrolment of boys orgirls).

The �rst model speci�cation concerns the introduction of the creditchoice variables denoting if females and males in a household can

18The districts of Bangladesh are divided into subdistricts called upazillas.(http://en.wikipedia.org/wiki/Upazilas_of_Bangladesh).19In this study, the lending model was solidarity group. Some of these groups were

all-male and more were all-female (none was mixed).20The LIML estimator is based on a single equation under the assumption of nor-

mally distributed disturbances. It has the same asymptotic distribution as the 2SLSestimator. The advantage of the LIML estimator is its invariance to the normaliza-tion of the equation (see Greene, 2008, pp. 375-376 for the analytical demonstration).In particular, Davidson and MacKinnon (2004) show that LIML can be used withsuccess when the sample size is reduced and the number of overidentifying restrictionsis large.

18

borrow. Therefore, we have

cf = pfe

cm = pme:

Let pm and pm dummy variables denote if microcredit group ofmen or women are e¤ectively operating in a speci�c village, while eis a dummy that explains whether a household meets the eligibilitycriteria of the micro�nance programs. Let y0 denote the outcome.Then, the model choice (Tobit or Probit) relies on the kind ofoutcome y0. But since we restrict our attention on household con-sumption, we will assume outcome is continuous and unbounded.

According to PK approach and subsequent contribution of theRoodman-Morduch study, we consider the following problem:

y0 = yfm0 + x0�0 + �0y�f = x0�f + "f if cf = 1

y�m = x0�m + �m if cm = 1 (6)

yf = 1�y�f � C

� y�f

ym = 1 fy�m � Cg � y�m(�0; �f ; �m) 0 � N (0;�) :where yf and ym are the total borrowings of all women and all menhousehold members. Let yfm =(yf1; yf2; yf3; ym1; ym2; ym3) 0denotesthe six credit variables disaggregated by program and gender; xis a vector of exogenous controls, C represents the credit censor-ing level, � is a 3�3 positive de�nite symmetric matrix, and 1fgindicates a dummy variable.

The above econometric model presents some unusual features. First,as suggested by Roodman and Morduch (2009), "Super�cially,there appear to be no excluded instruments. Meanwhile, the creditequations�samples are restricted, which means that the number ofequations in the model varies by observation."21 Second, the out-come equation contains six di¤erent endogenous credit variablesbut in the model there are only two instrumental equations ( for y�fand y�m ). Apart from these unusual features, the key assumptionbehind the model is similar to a traditional two-stage instrumen-tal variable set-up. Speci�cally, they estimate the following twoequations by using LIML set-up:

y�f = cfx0�f + C + �f21See also Wilde (2000) for a more advanced discussion.

19

y�m = cmx0�m + C + �m (7)

In this speci�c setting, PK e¤ectively instrument for the borrowingvariable creating interactions between the credit choice dummiesand the exogenous variables included in the model. The PK ex-ogenous variables are: age, sex, education of the household head,other household characteristics, a set of village characteristics andindividual characteristics ( in the case of regression on individual-level data). In addition, the authors included also the constantterms, cf and cm , which are instruments themselves.

The PK models for distinct outcomes have several characteristics.First, they are conditional (i.e., it means that their speci�cs, suchas number of equations, vary by observation, being conditionalon the data). Second, they are recursive in the sense that thespeci�cations contain plain stages and do not model any kind ofsimultaneous causation. Moreover, as argued in Roodman (2009),the observed yf and ym appear in the equation (y0); this impliesthat they are also fully observed. Finally, the models combineequations that show di¤erent types of censoring (mixed process)22.

An important issue in this model concerns spherical errors. Sinceheteroskedasticity can make Tobit-type models inconsistent, thecritical point is how much the previous assumption can be relaxed.In PK�s carefully study homoskedasticity is implicitly assumed.Speci�cally, the authors assume identically but not independentlydistributed errors. Starting from assumptions on cf and cm, theidenti�cation framework is based on the exogeneity (after condi-tioning on controls) of this constant terms. In other words, thefactors driving credit choice (i.e., the formation of credit groupsby village and gender, and the eventual eligibility of individualhouseholds) must be exogenous. PK�s approach does not suggestvalid arguments in support of the exogeneity of the �rst factor. Asregards the second (landholdings), they argue:

"Market turnover of land is well known to be low in South Asia.The absence of an active land market is the rationale given for thetreatment of landownership as an exogenous regressor in almost allthe empirical work on household behaviour in South Asia"23

But this seems to describe a case in which landholdings is externalto the model and not exogenous (Heckman, 2000). The exogeneitynotion is di¤erent: it requires that landholdings are related to

22For more details, see Roodman (2009).23From Pitt and Khander (1998), p.970.

20

outcomes only through microcredit after linearly conditioning oncontrols24.

Concerning the two PK identifying assumptions , Morduch (1998)remarks relevant questions. First, PK acknowledge that unob-served factors might in�uence both group formation and outcomes,generating endogeneity. Their strategy consists of including villagedummies to control for any factors at the community-level. TheMorduch�s criticism is about sub-village e¤ects (i.e., the villagee¤ects are not �xed within villages). For instance, we imagine alocal community in which eligible households are not very poor.Then, in a similar context, group formation might be more likelyand outcomes systematically better. In his following study, Pitt(1999) introduces interaction terms between landholdings and allthe x variables to PK�s instrument framework to strengthen their�ndings. Second, in the PK data land markets are active and thereexists substantial endogenous mistargeting. In other words, 203 ofthe 905 borrowing households in the 1991-92 sample owned morethan 0.5 acres before the microcredit intervention. Microlenderswere not following the eligibility criteria strictly so that some of theover-half-acre households that received the loans may have beenmet with an alternative eligibility rule (as discussed in PK (1998),footnote 16: "The quasi-experimental identi�cation strategy usedhere is an example of the regression discontinuity design"). Pitt(1999) replies to Morduch�s criticisms pointing out that identi�-cation with LIML does not require the eligibility rule be perfectlyrespected but it merely drives an exogenous component of variationin borrowing.

With regard to impact results, PK found that "annual householdconsumption expenditure increases 18 taka for every 100 addi-tional taka borrowed by women...compared to 11 taka for men."In addition, they found that lending to female reduces the useof contraception and has a positive impact on schooling of boys(as regards Grameen Bank and RD-12, while women participationonly in Grameen Bank has a positive e¤ect on schooling of girls).

24According to Merriam-Webster�s dictionary, exogenous means caused by factorsor an agent from outside the organism or system. But the consistency of IV estimatorimplies that the instrument be orthogonal to the error term, which is not involvedby the Merriam-Webster de�nition (Leamer, 1985). Heckmann (2000) suggests theterm external for the Merriam-Webster de�nition. Its use concerns variables whosevalues are not set or caused by the variables in the model. Therefore, it is morecorrect keeping exogenous for the orthogonality condition that is required to obtainconsistent estimation in IV context.

21

These �ndings reinforce two fundamental concepts about microcre-dit: �rst, its reliability as instrument to alleviate poverty, secondthe important role of women credit.

We now focus our attention on Morduch�s study (1998). He usesan estimation strategy analogous to PK�s, but simpler and less ef-�cient. As a �rst step, he performs simple di¤erence-in-di¤erenceestimates, then adds controls. Despite PK�s study, Morduch �ndsno sharp evidence for strong impacts of microcredit on householdconsumption. However, he �nds some evidence that microcredithelps households to diversify income �ows so that consumptionvolatility is less pronounced across seasons. Moreover, the resultshinge on the assumption that the village dummies totally captureall critical aspects about the communities that might a¤ect themicrolender�s decisions concerning the program placement. In thisanalysis the village dummy variables only control for unobserv-able attributes that in�uence all households in a village identicallyand linearly25. In addition, Morduch �nds weaker evidence thathouseholds with credit access tend to manage actively not onlytheir spending, but also their labour income. He �nally concludes(without any direct evidence) that the ability to smooth incomeover the year drives smoother within-year consumption levels.

The above empirical contributions arise from the analysis of the�rst round of data (1991-1992)26. But exhaustive impact studiesusing a single cross-section requires some important assumptions.These studies are based on intensive use of statistical methodsto overcome the limitations of the data set. There are relevantquestions about the validity of the critical assumptions that holdup the statistical framework (Roodman and Morduch, 2009).

Khander (2005) points out that the availability of panel data helpsto eliminate one potential source of bias in the PK and Morduchcross-section studies. This source concerns unobserved but �xedattributes simultaneously in�uencing microcredit borrowing andother outcomes of interest. In his study, Khander analyzes threedi¤erent outcomes: household food consumption, non-food con-

25This aspect will be strongly criticized by Roodman and Morduch (2009).26Concerning the process of data collection, during the years 1991 and 1992 the

World Bank and the Bangladesh Institute of Development Studies surveyed nearly1,800 households in 87 villages in Bangladesh. Of these, 15 were not served by mi-crolenders. Then, in 1998 and 1999, researchers returned to analyse the same sample.The only change is that all villages were served by micro�nance services. Becauseof the attrition, 1,638 were the households interviewed in both rounds (Armendàriz,Morduch, 2010).

22

sumption and total consumption. Despite PK, he includes house-holds owing more than 5 acres.

Following Khander�s carefully study, we now examine in detail thepoverty e¤ects of microcredit intervention. In his analysis, theauthor distinguishes between moderately poor and extremely poor(as argued in Khander, 1998, he de�nes moderate poverty as house-hold consumption level below 5,270 taka/person/year and extremepoverty as 80% of that, 3,330 taka/person/year)27.

Table 1 contains data fromBangladesh context in Khander(2005).

We can note, from this survey, that in program villages microcre-dit participants had relevant declines in poverty rates (in termsof moderate poverty). Concerning the voice "All program partic-ipants", we can see a decrease from a rate of about 90 percentin the �rst period to about 70 percent in the second round ofdata, approximately a 20 percentage point decline. But for el-igible households that did not participate in credit programmes(in the period 1991/92) the falling in terms of poverty rate was19.2 percentage points, as nontarget nonparticipants (19 percent).At this point, the question is: did microcredit intervention playa role in this process? Pessimists may answer that the declineof average poverty incidence for program participants might havehappened even without intervention. On the other hand, optimiststhink that the net impact of programmes have been substantial,involving also nonparticipants. In other words, they argue thatthe spillover e¤ect could explain the general improvement in areaswith programs. Comparing the results for program areas to resultsfor villages without intervention in 1991/1992, we can note a sim-ilar trend: poverty rates decreased by around 19 to 20 percentagepoints (only target nonparticipants had a poverty reduction of 4.5percentage points).

In his conclusions, Khander argues that microcredit contributed toapproximately one third to one half of these poverty contractions.Speci�cally, Khander asserts that lending 100 taka to a femaleleads to a growth in household consumption by around 8 takaannually. Moreover, he suggests that the impact of micro�nanceintervention is stronger for extreme poverty than moderate poverty,and microcredit e¤ects are more relevant for women borrowingthan for men borrowing.

27This classi�cation is based on the poverty line criterion.

23

4.4 The Roodman-Morduch revisitation.

The Roodman-Morduch approach to PK�s analysis a¢ rms, as Mor-duch (1998), that the baseline assumptions used in the study donot hold. Morduch (1999) does not �nd evidence of consumptionimpacts in the 1991/1992 data and criticizes the identifying as-sumptions of the PK�s framework. On the other hand, he suggeststhat microcredit decreases consumption volatility. In their replica-tion, Roodman and Morduch (2009) use the same methods to thesame data as in PK. Applying two-stages least-squares (2SLS) re-gression, they contest the positive results obtained in the previousstudy. Concerning the PK �ndings, Roodman-Morduch achieveopposite (in sign) results. On the basis of speci�c tests , theyargue that instrumentation strategy is failing. Reverse or omitted-variable causation drives the �nal outcomes, and the endogenouslinks between credit and consumption varies by subsample ( i.e.,borrower sex). It can explain the di¤erences in terms of genderimpact. But they do not conclude that microcredit does not a¤ectthe lives of poor borrowers; rather, they suggest that the statisticalsetting is not due to the task.

Roodman and Morduch �ndings about Khander�s analysis reducethe con�dence that the key identifying assumptions for causal infer-ence e¤ectively hold in a similar context. In particular, they doubtthat the Khander�s assertion concerning the relevant impact of mi-crocredit services in reducing extreme poverty could arise from adirect estimation. The critical point is that the introduction ofthe panel framework does not seem to overcome the problem ofthe lack of clearly exogenous variations in the use of microcredit.The distinction between moderately poor and extremely poor con-ducted by the author is based on estimated baseline poverty levels.Then he compares changes in consumption (about the two kindsof poor households) using regression coe¢ cients that would havesense only if all the households have similar net impacts.

All the three studies (Pitt-Khander 1998, Morduch 1998, Khander2005) tend to reinforce the general positive idea about microcre-dit. According to PK (1998) and Khander (2005), microloans canreduce poverty, especially for women. In addition, Morduch (1998)suggests that small-size credits help households to attenuate con-sumption variability across the seasons. Roodman and Morduch(2009) do not contradict these considerations, but highlight theabsence of decisive statistical evidence in support of these studies.

24

5. Randomized approach5.1 Randomization as potential solution of selection bias: analyti-cal foundations.

As discussed in section 3, selection bias represents a relevant prob-lem in order to obtain a clean estimation of the microcredit pro-gram impact.

The aim, in this particular context, is to gauge the net e¤ect ofcredit access on the revenue of a borrower. The causal impact, thatis the term E(Y 1i � Y 0i =Ti = 1) , is not observable but as arguedin Du�o et. al. (2007) is "logically well de�ned".

Randomized experiments allow to manage selection bias problemsthrough a random assignment of the program to the treatment andcomparison groups.

How does this methodology function in practice?

First, a sample of N individuals, or households, is selected froma population of interest28; second, the initial sample is randomlydivided into two distinct subgroups: treatment and comparison orcontrol groups.

The target units are exposed to the "treatment" (i.e. they receivethe loan), while the non-target units aren�t. Then researchers ob-serve the outcome Y, and compared the results for both di¤erentsubgroups.

As argued in section 3, we can estimate the average program im-pact as follows:

� = E(Y 1i =Ti = 1)� E(Y 0i =Ti = 0) (8)

The advantage in adopting this approach is that the two groupsare expected to be identical before the microcredit program, be-cause of their random selection. The only di¤erence is due to theexposure of the treatment. This implies that the selection biasterm E(Y 0i =Ti = 1) � E(Y 0i =Ti = 0) is equal to zero.The term inquestion describes how both participant group and control groupwould have performed if nobody had had access to credit. More-over, if the outcomes of a subject are unrelated to the treatmentof the other individuals29, we obtain

28It�s important to highlight that the population of interest can�t be randomlydrawn from the whole population, but could be selected on the basis of observableattributes (Du�o et al. 2007).29See Angrist, Imbens, Rubin (1996)

25

E(Y 1i =Ti = 1)�E(Y 0i =Ti = 0) = E(Y 1i �Y 0i =Ti = 1) = E(Y 1i �Y oi )(9)

If randomization has been completed with success, experimentalapproaches can provide a valuable instrument in order to overcomeselection bias problems.

In the opposite case, we can meet with problems. For instance,the individuals that apply for loans successfully may have morebusiness ability, organizational skills and entrepreneurial experi-ence than subjects that don�t apply for a microcredit program.Besides, the choice of the location from a micro�nance institutionmay be addressed to the villages with good life and economic con-ditions respect to other more disadvantaged sites.

Many estimation problems concern the cases of "non-random" at-trition (the less promising clients are the �rst to drop out of theprogram) and contamination (for instance, a new competitor startshis �nancial activity during the study period).

Generally, the bias of impact estimation is upward. But thereare also particular forms of selection bias, such as contamination,which may lead to downward biases; performing a correct random-ization implying that E(Y 0i =Ti = 1) = E(Y

0i =Ti = 0):

30

5.2 Randomization in microcredit impact evaluations: sample-sizeand the power of experiments.

In general, two particular factors a¤ect the success of an exper-iment: statistical power and the role of spillovers (Armendàriz,Morduch, 2010).

Du�o et al. (2007) suggest the basic principles of power calcu-lation31, starting from a simple regression frame. The estimateof the average impact is the OLS coe¢ cient of � in the followingregression:

Yi = �+ �T + �i (10)

Following Bloom�s (1995) approach, we assume that only a possibletreatment exists, and that a speci�c proportion P of the samplereceives the treatment in question. Since we suppose that each

30As much as discussed above depends on the properties of expectations of linearoperators (average impact).As argued in Armendàriz, Morduch (2010, p. 296): "But the basic set-up does not

permit us to say anything about the medians and very little about the distributionalfeatures of impacts. And we need to be careful in analyzing data on the impacts forparticular subgroups in a population."31See also Bloom (1995).

26

unit was randomly sampled from an identical population, the ob-servations can be considered to be identical independent distributed(i.i.d.), with variance �2:

Clearly, the variance of the OLS estimator of � , that is � , isdetermined by:

1P (1�P )

�2

N(11)

Now, we focus our attention on testing the hypothesis H0 , that isthe impact of the treatment is equal to zero against the alternativehypothesis, H1 , that it is not.

The signi�cance level related to a speci�c test describes the likeli-hood of rejecting the null hypothesis when it�s true.

Figure 1: Statistical Power

Figure 1 draws two distinct bell shaped curves: on the left thereis the distribution of � under the null hypothesis of absence ofimpact H0 = 0, on the right the distribution of � if the true e¤ectis e¤ectively �:

In the �rst speci�cation, If � falls to the right of the critical value,for a determinate level of signi�cance, the hypothesis H0 = 0 willbe rejected; formally, it is true if

j � j> ta � SE� (12)

where ta hinges on the signi�cance level and it derives from a stan-dard t-distribution.

In the second case, in order to evaluate the power of the test fora true impact size � we take into account the part of the areaunder this curve which is to the right of the critical level ta. Inother words, it corresponds to the probability of rejecting the nullhypothesis when it�s e¤ectively false.

27

The achievement of a power k implies the following condition:

� > (t1�k + ta)SE���

(13)32

Du�o et al. (2007) consider the issue of power as the "minimumdetectable e¤ect size" for a given statistical power (k), signi�cancelevel (a), sample size (N ), and set of individuals that belong tothe treatment group (P). It can be given by

MDE=(t1�k + ta) �q

1P (1�P )

q�2

N(14)33

where the term t1�k represents the level of statistical power, ta capturesthe con�dence level, P includes the portion of sample that receivedthe program, �2 is the variance of the impact and, �nally, N is thetotal size of the sample.

From equation (14), we note a trade-o¤ between statistical powerand sample size. In fact, when N increases, the minimum de-tectable e¤ect size decreases, and vice versa. Power calculationdescribes the linkage between impact size and sample size, withtypical statistical con�dence levels (5 percent, 10 percent, 20 per-cent). But in general the e¤ect size is not known before startingwith the intervention. Many di¤erent studies have developed po-tential solutions to overcome such problems: the �rst practicalapproach consists in making predictions on the basis of previousresearches, the second concerns the introduction of a small pilotstudy.34

Cohen (1988), for instance, express the impact size in terms ofstandard deviations from the mean of the outcome; he suggests, inhis analysis, that an impact of 0.2 standard deviation is negligible,0.5 is intermediate, and 0.8 is relevant. Clearly, these values areindicative and have to be considered in each speci�c context.

Equation (14) also provides useful advice concerning the divisionof the sample between treated and non-treated units. We assume,for example, that there is a single treatment, and the most relevantcost of the study is data collection. It follows that an equal distrib-ution between treatment and control group is an optimal allocation(in this case, the equation above is minimized at P=0.5).

But if program implementation is costly and the data are easilyavailable for both the groups ( the data collection process isn�t ex-

32The term t1�k is simply given by a t-table.33It refers to a single sided test. If we introduce a two-sided test, the term ta will

be substituted by ta=2:34For a more advanced discussion, see Du�o et al. (2007, pp 22-24).

28

pensive), the optimal division will require a larger control group.Speci�cally, in order to obtain the optimal proportion of treatedunits, equation (14) must be minimized under the budget con-straint as follows:

MinP

�(t1�k + ta) �

q1

P (1�P )

q�2

N

�(15)

sub Ncc +NPct � Bwhere N is the total sample size, cc represents the unit cost percomparison subject, and ct is the unit cost for treatment subject.From (10), we obtain the optimal allocation rule:

P1�P =

pccct

(16)

As argued in Du�o et al. (2007), "the ratio of subjects in thetreatment group to those in the comparison should be proportionalto the inverse of the square root of their costs."

The above setting can be applied to sample size calculations whenthere are multiple treatment.35

The level of randomization represents a crucial matter for the sam-ple size. Many experimental designs involve randomization overgroups rather than single individuals. For example, PROGRESA36

program used the village as the unit of randomization, even if sin-gle individual data were available for statistical evaluation.

In similar contexts, we have to consider that the error term maynot be independent across single individuals. If the program par-ticipants in a group have some attributes in common, informationabout single units will cause weak variations in the �nal resultcompared to the case of individual-level randomization. Since bor-rowers of the same group can be subject to common shocks, acorrelation between outcomes is very likely, and leads to a wronginterpretation of the program impact.37

The key issue is to compare the proportion of the outcome vari-ance coming from the group impact and the proportion comingfrom individual impact: if the �rst value is higher, also the sampleneeds to be bigger, or, alternatively, the e¤ective size necessary fordetection.

35See Bloom (1995).36PROGRESA (Programa de Educaciòn, Salud y Alimentaciòn) is an anti-poverty

program implemented in Mexico in the late 1990s (for more information, seehttp://www.ifpri.org/dataset/mexico-evaluation-progresa)37For an analytical treatment, see Bloom (2005)

29

One important di¢ culty encountered when we operate in the mi-cro�nance context is that some experimental designs only encour-age subjects to participate in a speci�c credit program (treatment)so that "eligible" people can accept or refuse the invitation. At thesame time, people in the control group may take up the treatmenteven if they are not directly encouraged (Armendàriz, Morduch,2010).

Ashraf, Karlan, and Yin (2006) encouraged a randomly selectedgroup of people to sign up a new savings account. In this frame-work, the element of randomness was the invitation; this impliesthat the e¤ects of the program must be evaluated comparing in-vited and non-invited subjects. Clearly, it follows that not allinvited individuals accepted the proposal. Since the impact mea-sured at the invitation level is reduced, a bigger sample size isrequired.

Finally, a strati�cation (or block) of the sample can be introducedin order to improve estimate precision. Stratifying involves divid-ing the sample into subgroups that have similar values of particularobservable characteristics. Then, the randomization is conductedfor each single block (subgroup) separately.

While the randomization procedure ensures that treatment andcomparison groups will be similar in terms of expectation, strati�-cation process is used in order to ensure that the assignment to aspeci�c group (treatment or control group) is random in practice,along observable dimensions of the strati�cation.

A strati�ed design allows us to gauge the impact of the programfor each subgroups separately using statistical methods. Since eachblock tends to be more homogeneous compared to the entire sam-ple, a little change in the outcome levels can be found out withthe same sample size. The relevant consequence is that a smallertotal sample is needed38.

5.3 Spillover e¤ects

Experimental designs can make externalities such that non treatedindividuals are a¤ected by the intervention. Moreover, there arespillovers also when an individual transfers from the treatmentgroup to the comparison group, or vice-versa.

Following Du�o et al. (2007), we consider a simple case in which amicrocredit program is randomly attributed across a population of

38For a more advanced discussion, see Imbens, King, and Ridder (2006).

30

individuals. The estimate of the intervention is � = E(Y 1i =Ti =1) � E(Y 0i =Ti = 0); if we interpret this di¤erence as the impactof the treatment, "the potential outcomes for each individual areindependent of his treatment status, as well as the treatment groupstatus of any other individual.39"

If the previous condition is violated, the term E(Y 0i =Ti = 0)40 in

the sample does not correspond to E(Y 0i =Ti = 0) in the popula-tion, because the sample contains at the same time treated andnon treated units. This implies that the potential outcome foreach subject and the intention-to-treat estimate (�) hinge on theentire set of allocations to participants and non participants onthe program. If we assume, for instance, that the externalities onuntarget individuals are positive, the estimate of the term � willbe smaller than it would have been in absence of externalities.

If the spillover e¤ects become relevant in the impact study, re-searchers can design experiments ad hoc, in order to identify theirsize and power41.

In the micro�nance framework, spillovers can happen when, forexample, a target individual receiving funds divides part of themoney with a friend of the comparison group, or when a micro-credit client participating in business training program shares thenew knowledge with another borrower who wasn�t selected for thetraining activity.

Externalities a¤ect the experimental design at distinct levels. Indi-vidual switching between groups is not a random process, and theidenti�cation of the program e¤ects depends on the randomnessof the treatment assignment. Therefore, if an individual switchesfrom treatment to comparison group, a problem of selection biasin the impact estimation reappears. As regards spillovers due tosharing bene�ts concerning only the treated status, it may reduce(or enlarge) the observable e¤ects of the program implementation.

39This is the standard unit treatment value assumption (SUTVA): we assume thatthe potential outcomes for each individual are unrelated to the participation statusof other subjects (Angrist, Imbens, and Rubin, 1996).40We estimate the average treatment impact as the di¤erence in empirical means

of Y between the two distinct groups as follows� = E(Y 1i =Ti = 1)� E(Y 0i =Ti = 0)where the term E describes the sample average. Hence, as the sample size grows,

the previous di¤erence tends to� = E(Y 1i =Ti = 1)� E(Y 0i =Ti = 0)(Du�o et. al., 2007).41For a more advanced discussion, see Du�o et. al. (2007), pp. 56-58.

31

In similar contexts, a bigger sample is needed. Another potentialsolution concerns randomizing at the group level rather than theindividual level.

When a micro�nance istitution lends funds to a group of individu-als (group lending strategy), spillover e¤ects can a¤ect the impactestimation. Since this procedure involves a random assignment ofthe status of program participation within the group, it is likelythat resentment, confusion and distrust emerge from the groupmembers and produce biased impact evaluations.

5.4 Hawthorne and John Henry e¤ects

Another interesting aspect involving impact evaluations is thatthe evaluation itself may lead to changes in treatment and controlgroups behaviour.

Speci�cally, behaviour changes among the target units are calledHawthorne E¤ects42, while behaviour changes among the untargetunits are called John Henry e¤ects43.

In microcredit programs, the treated units might appreciate re-ceiving the loan and be aware of being observed, which may leadthem to modify their behaviour during the experiment. On theother hand, the control units may alter their behaviour becauseof their resentment towards the program participants, and decideto compete with those receiving the loan (for instance, workingharder in order to show their abilities) or on the contrary, slacko¤.

One way to disentangle these e¤ects from the program impacts issuggested by Du�o and Hanna (2006)44. The authors continuedto monitor the e¤ects of the program implementation after theduration of the experiment. If the results obtained in absence ofany kind of experiment are similar to the outcomes at the beginningof the evaluation period, the results are not a¤ected by Hawthornee¤ects.

42The term was coined by H. A. Landsberger (1950), when examining older ex-periments from the period 1924-1932 at the Hawthorne Works (a Western ElectricCompany in Chicago).During a study comissioned in order to evaluate the e¤ect of work conditions on

worker productivity, it was suggested that workers tend to increase their productiondue to the motivational e¤ect of being observed.(http://en.wikipedia.org/wiki/Hawthorne_e¤ect)43The term John Henry e¤ects comes from the story of John Henry trying to lay

railroad track faster than the machine (Du�o et. al., 2007).44For more information concerning the program, see the article "Monitoring Works:

Getting teachers to come to school" (Du�o, Hanna, 2006).

32

Experimental designs can also be created in order to disentangleHawthorne or John Henry e¤ects. For example, in Ashraf, Karlan,and Yin�s study (2006), the authors were concerned about the roleof the marketer visits (in the SEED program45) to the homes ofclients, emphasizing the importance of savings. They suggestedthat these kind of relationships may persuade individuals to im-prove their performances.

To overcome this inconvenience, they added a further treatmentgroup to which they o¤ered regular savings accounts. In otherwords, in addition to the clients assigned to the SEED program,a part of the comparison group was selected for the pure controlgroup, while the other part was assigned to a third group, called the"marketing treatment" group. The units of this group receive thesame marketing campaign as the SEED clients, with an exclusivedi¤erence: the marketing activity was limited to traditional savingsproducts of the micro�nance institution.

Comparing savings performances of the SEED�s participants withthe results of the "marketing treatment " clients, Ashraf et al.isolated the direct e¤ect produced by the SEED program from thee¤ect of the marketing activity.

5.5 Randomization limits

A �rst limit of a randomized approach arises from the estimate ofan average impact of the intervention. It o¤ers little informationabout the distribution of the e¤ects, and nothing concerning themedian impact. One method to improve the learning process aboutthe distribution of impacts can be strati�cation.

As discussed above, the introduction of impact estimations for sub-groups (from the start of the experiment) may help avoid relevantrisks, such as "data mining" and the �nding of spurious results.The implementation of a strati�cation method, both in random-ized and non-randomized approaches, allows us to specify in ad-vance which subgroups (for instance, men and women, richer andpoorer clients, young and aged people) and which hypotheses maybe signi�cant, thus restricting the analysis to these.

45The SEED is a commitment savings product (Save, Earn, Enjoy deposits) ac-count designed for a small rural bank in the Philippines. This kind of account requiresthat individuals undergo restrictions in withdrawing their funds until they reach agoal date, or that a given amount of money was deposited. (Ashraf, Karlan, andYin, 2006).

33

Another relevant limitation of randomized experiments concernsthe di¢ culty in generalising the �ndings to other settings, that aredi¤erent from the original one. In short, they can have a high inter-nal level of validity, but not an external one. Hence, analysts thatuse this approach have to replicate a speci�c experiment beforereaching general conclusions.

Non-randomized studies usually use data coming from large geo-graphical areas, with diversi�ed populations and their �ndings areapplicable to a wider range of di¤erent contexts. But often thesemethods are less e¢ cient in terms of internal validity.

Randomized experiments are designed carefully, and their imple-mentation is planned closely, but extension to a large scale canyield di¤erent results. Pilot studies46 can be used to evaluate if apolicy produces relevant impacts on a small scale, and then even-tually to procede with the implementation on a wide scale.

When a randomized experiment is implemented, the initial randomassignment of the treatment must be maintained during the entireperiod of analysis. The limits here are due to attrition and con-tamination. The �rst problem (attrition bias) is not predictableand can overestimate or underestimate the impact of intervention.Contamination may happen if, for example, a new micro�nance in-stitution starts working with a comparison group, giving �nancialservices to the people that do not receive any kind of treatment.

Finally, randomized approaches impose their logic on the selectionof program participants. This implies that not the entire popu-lation will receive the treatment, and the choice of who obtainsthe loan cannot be made based on fairness assumptions (such as"those who need it most"). Several nongovernment organizationsmay be unwilling to accept this statistical method. (Armendàriz,Morduch, 2010).

6. Experimental versus Non-experimental: a comparisonRecently, a growing amount of literature has tried to use random-ized experiments to validate non-experimental methods.

Lalonde (1986) suggests that many statistical procedures used inimpact evaluations did not lead to precise estimates and often thesedi¤er substantially from experimental results. Glazerman, Levy,

46Pilot study represents the phase before the program is scaled up. This is anoccasion for researchers to assess the e¤ectiveness of the program and a chance toimprove the experimental design. (Du�o et al., 2007)

34

and Myers (2003) compared experimental and non-experimentalapproaches in di¤erent �elds: welfare, job training and employ-ment service programs in the US. They found, by the examinationof twelve distinct design replication studies, that retrospective es-timators frequently lead to outcomes strongly di¤erent from ran-domized evaluation. In addition, the bias can be signi�cant47.

Interestingly, Cook, Shadish, and Wong (2006) compare random-ized and non-randomized studies, especially in educational set-tings. They note that the results coming from the two di¤erentapproaches are similar when analysts use a regression discontinuityor "interrupted time series" (as non-experimental strategy). Theauthors conclude that quasi-experimental designs (for instance re-gression discontinuity) might generate clean impact estimates as awell-done experimental evaluation.

Diaz and Hanna (2006) focus on PROGRESA, an anti-povertyprogram implemented in Mexico. Speci�cally, they compare esti-mates from an experimental design with those obtained by propen-sity score matching, and conclude that the second strategy can bevalid, when a consistent number of control variables is available.

Du�o, Kremer, and Robinson (2006) conducted an interesting studyin which they compared experimental and non-experimental esti-mates of peer e¤ects over fertilizer adoption in Kenya. They foundthat there is a correlation between an individual�s decision andthe decisions of other contacts, probably due to the sharing of thesame environment. In this context, randomization ensured exoge-nous variations in the likelihood that some members of a speci�cnetwork adopted the new technology. The study shows substan-tially di¤erent results from the non-experimental framework; inparticular, the authors highlight no evidence of learning e¤ect.

Comparative studies can be useful in order to assess the existenceand the size of biases in retrospective impact evaluations, providinga valuable guidance to address estimation problems.

Clearly, it is important that retrospective evaluations are con-ducted before the results of experimental approach are available, inorder to avoid selection of plausible comparison groups and meth-ods with the intention of matching experimental estimates (Du�oet al., 2007).

47For a more complete discussion, see Du�o et al. (2007).

35

7. Summary and ConclusionsIs microcredit really moving people out of poverty? This is thecrucial question that researchers are attempting to solve. But, asdiscussed above, completing reliable impact evaluations is oftendi¢ cult, as well as interpreting the results obtained.

Impact evaluations play a crucial role in allowing micro�nance in-stitutions to reliably assess the e¤ectiveness of their operationson poverty reduction and for investors to learn about the morepromising types of programmes to implement. But the lack ofvaluable studies explains the di¢ culty in evaluating interventionsin which di¤erent clients use �nancial services with several degreesof intensity and participation is voluntary.

To sum up, it is possible to highlight some important issues con-cerning the impact evaluations framework.

(i) Microlenders tend to carefully select communities and villages inwhich to o¤er their services, and target citizens to whom to lend.Therefore microcredit programmes can be implemented in thoseareas which have more business opportunities, or have good-levelinfrastructures (highways, markets, large towns). Such criteria toselect places for intervention lead to biased estimation of programimpact.

(ii) Self-selection of program participant represents another im-portant source of bias. Since it is probable that households withgreater entrepreneurial spirit and organizational skills are morelikely to join the microcredit program, this can produce biases inestimating the e¤ects of the program (speci�cally, when these kindsof unobservable attributes are correlated with obtaining credit).

(iii) The standard methods applied in microcredit impact evalua-tions tend to consider the intervention as a homogeneous process,that produces a steady in�uence on outcome variables like con-sumption, income or poverty. In practice, the causal process ismore complicated. For instance, there might be hidden relation-ships between the selected exogenous and endogenous variable, orexternalities, which may obscure the causation linkage.

Recently, a set of interesting impact evaluations have incorporatedexperimental designs into the program implementation to achievereliable estimates of the impact net e¤ects. In my opinion it rep-resents a possible strategy to follow, keeping in mind that bothapproaches have to be made with care.

36

If we focus our attention on the hundreds of millions of micro�-nance clients, they demonstrate how important microcredit is intheir lives by a behavioural mechanism called "voting with theirfeet". According to Rosenberg (2010), the micro�nance experi-ence in three decades shows that customers arrive without a needto advertise and repay loans with high reliability rates. The key in-centive to repay is the "borrowers�desire to keep access to a highlyvalued service" (Rosenberg, 2010, p. 4). It seems that target bor-rowers wish to preserve the microcredit access over time, in orderto cope with possible future shocks. Another observable aspectconcerns the willingness to pay high interest rates on the funds re-ceived, and accept trivial or no return on savings. In addition, mi-cro�nance customers usually return using micro-�nancial services,even in the presence of high desertion rates. The repeated usedoes not necessarily imply that these services provide bene�ts. Itis clearly possible that some borrowers will over-indebt themselves,producing a negative �nal outcome. But the high repayment ratesover the long term may justify the assertion that micro�nance isnot over-indebting great amounts of its users. Surely this presump-tion needs to be studied and tested by new research.

Finally, as suggested by Rosenberg (2010), an important advan-tage of microcredit introduction can be thought not as its net im-pact, but rather as its cost in term of subsidies. In other words,while social programs such as education and health care mightrequire consistent amounts of continued subsidies, microcredit, ifwell-implemented, can require relatively small initial subsidies thatallow such organizations to expand their business without any fur-ther kind of subsidy.

37

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41

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ope

rate

d in

Sou

th A

fric

a (C

apet

own,

Por

t Eliz

abet

h an

d D

urba

n ar

eas)

. The

sam

ple

conc

erns

mar

gina

l ap

plic

ants

, with

thre

e ch

arac

teris

tics:

ne

w, r

ejec

ted

but p

oten

tially

cre

ditw

orth

y (

787

appl

ican

ts).

- P

eopl

e ar

e no

t ver

y po

or. (

mar

gina

lly

reje

cted

app

lican

ts)

- In

tere

st r

ates

are

hig

her

than

thos

e ap

plie

d by

typi

cal m

icro

finan

ce

inst

itutio

ns. -

Onl

y co

nsum

er lo

ans.

- S

hort

-run

re

sults

(6-

12 m

onth

s)

Ash

raf,

Kar

lan,

Yin

(20

06)

- R

ando

miz

ed e

valu

atio

n. (

Mic

rosa

ving

s). -

SE

ED

* pr

ogra

m is

ran

dom

ly a

ssig

ned

abou

t 1.8

00 s

ubje

cts

to e

ither

rec

eive

a p

ropo

sal t

o op

en a

sav

ings

ac

coun

t (tr

eatm

etn

units

) or

not

(co

mpa

rison

uni

ts).

A

ran

dom

sub

set o

f 707

indi

vidu

als

rece

ived

the

prog

ram

offe

r, b

ut o

nly

202

acce

pted

the

prop

osal

an

d op

ened

the

acco

unt (

28,4

per

cent

).

Bas

elin

e ho

useh

old

surv

ey c

ondu

cted

by

the

auth

ors

of 1

.777

exi

stin

g or

form

er

clie

nts

of G

reen

Ban

k (r

ural

ban

k of

P

hilip

pine

s).

- M

icro

savi

ngs

impa

ct m

easu

red

at in

vita

tion

leve

l (no

t all

invi

ted-

subj

ects

acc

epte

d th

e of

fer

- 20

2 of

707

): th

is r

equi

res

a bi

gger

sam

ple

size

.

- H

igh

leve

l of s

tres

s an

d de

pres

sion

. -

Pos

itive

effe

cts

on jo

b re

tent

ion,

inco

me,

fo

od c

onsu

mpt

ion

qual

ity a

nd q

uant

ity,

hous

ehol

d de

cisi

on-m

akin

g co

ntro

l and

m

enta

l out

look

.

- r

ough

ly 5

% o

f hou

seho

lds

invo

lved

in th

e pr

ogra

m li

ft ou

t fro

m p

over

ty a

nnua

lly; -

le

ndin

g 10

0 ta

ka to

a fe

mal

e le

ads

to

addi

tiona

l con

sum

ptio

n of

18

taka

ann

ually

Pitt

, Kha

nder

(19

98)

-N

on r

ando

miz

ed e

valu

atio

n; -

Dou

ble

diffe

renc

e be

twee

n el

igib

le a

nd n

on-e

ligib

le h

ouse

hold

s an

d pr

ogra

m w

ith a

nd w

ithou

t mic

rocr

edit

inte

rven

tions

. -E

stim

atio

n pr

oces

s is

con

duct

ed s

epar

atel

y fo

r m

ale

and

fem

ale

clie

nts.

-B

angl

ades

h (G

ram

een,

BR

DB

*, B

RA

C);

-W

orld

Ban

k an

d B

angl

ades

h In

stitu

te o

f D

evel

opm

ent S

tudi

es s

urve

y (c

ross

-se

ctio

n, y

ears

199

1/19

92)

- E

ligib

ility

crit

eria

are

not

cle

arly

exo

geno

us

(Mic

rocr

edit

part

icip

atio

n is

res

tric

ted

to

"fun

ctio

nally

land

less

" -

hous

ehol

ds o

wni

ng

less

than

0.5

acr

e of

land

). -

No

evid

ence

of

cons

umpt

ion

impa

cts

(Mor

duch

, 199

8). -

Id

entif

ying

ass

umpt

ions

do

not h

old

(Mor

duch

, 19

98; R

oodm

an, M

ordu

ch, 2

009)

.

- P

ositi

ve im

pact

on

mic

rocr

edit

part

icip

atio

n on

wee

kly

expe

nditu

re p

er c

apita

, wom

en's

no

n-la

nd a

sset

s an

d w

omen

's la

bor

supp

ly. -

P

ositi

ve e

ffect

of f

emal

e pa

rtic

ipat

ion

in

Gra

mee

n B

ank

on s

choo

ling

of g

irls.

-

Mic

rocr

edit

inte

rven

tion

can

cont

ribut

e to

ch

ange

atti

tude

s an

d ge

nera

l cha

ract

eris

tics

of th

e vi

llage

s.

-N

on r

ando

miz

ed e

valu

atio

n; -

Dou

ble

diffe

renc

e be

twee

n el

igib

le a

nd in

elig

ible

hou

seho

lds

and

betw

een

prog

ram

and

non

pro

gram

com

mun

ities

.K

hand

er, S

. (19

98)

-B

angl

ades

h (G

ram

een,

BR

AC

);

-W

orld

Ban

k an

d B

angl

ades

h In

stitu

te o

f D

evel

opm

ent S

tudi

es s

urve

y (c

ross

-se

ctio

n, y

ears

199

1/19

92)

- E

ligib

ility

crit

eria

are

not

cle

arly

exo

geno

us

(Mic

rocr

edit

part

icip

atio

n is

res

tric

ted

to

"fun

ctio

nally

land

less

" -

hous

ehol

ds o

wni

ng

less

than

0.5

acr

e of

land

).

- N

o ev

iden

ce o

f pro

gram

impa

ct. V

illag

e ba

nk m

embe

rshi

p do

es n

ot im

pact

on

inco

me

varia

bles

.

Pitt

et a

l. (2

003)

- N

on r

ando

miz

ed e

valu

atio

n. -

Max

imum

like

lihoo

d es

timat

ion

cont

rolli

ng fo

r en

doge

neity

of i

ndiv

idua

l m

icro

cred

it pa

rtic

ipat

ion

and

of th

e pl

acem

ent o

f m

icro

finan

ce in

terv

entio

n. -

Impa

ct v

aria

bles

in th

e st

udy

are

heal

th s

tatu

s of

mal

e an

d fe

mal

e m

easu

red

thro

ugh

the

follo

win

g in

dica

tors

: arm

ci

rcum

fere

nce,

bod

y m

ass

inde

x an

d he

ight

-for

-age

.

- B

angl

ades

h (B

RA

C, B

RD

B, G

ram

een

Ban

k); P

anel

dat

a fr

om W

orld

Ban

k an

d B

angl

ades

h In

stitu

te o

f Dev

elop

men

t S

tudi

es (

year

s 19

91/1

992;

199

8/19

99).

- D

oubt

on

relia

bilit

y of

iden

tifyi

ng

assu

mpt

ions

.

- P

ositi

ve e

ffect

of f

emal

e cr

edit

on h

eigh

t-fo

r-ag

e an

d ar

m c

ircum

fere

nce

of b

oth

boys

an

d gi

rls. M

ale

cred

it do

es n

ot p

rodu

ce a

si

gnifi

cant

impa

ct o

n he

alth

chi

ldre

n m

easu

res.

Col

eman

(19

99)

- N

on r

ando

miz

ed e

valu

atio

n. -

Dou

ble

diffe

renc

e co

mpa

rison

bet

wee

n pa

rtic

ipan

ts a

nd N

on-

part

icip

ants

and

bet

wee

n vi

llage

s w

ith p

rogr

am a

nd

villa

ges

in w

hich

pro

gram

will

be

intr

oduc

ed la

ter.

- T

haila

nd (

villa

ge b

ank)

. - 4

45

hous

ehol

ds in

14

villa

ges:

8 w

ith v

illag

e ba

nks

that

sta

rted

thei

r ac

tivity

in 1

995,

th

e ot

her

6 an

yea

r la

ter.

- C

ontr

ol g

roup

mad

e up

of s

elf-

sele

ctin

g pa

rtic

ipan

ts in

vill

ages

iden

tifie

d fo

r la

ter

incl

usio

n in

the

prog

ram

. - G

ener

ally

, Tha

i-vi

llage

rs a

re w

ealth

ier

than

Ban

glad

eshi

-vi

llage

rs a

nd h

ave

easi

er a

cces

s to

cre

dit.

- T

he r

esul

ts c

anno

t be

exte

nded

to a

larg

e co

ntex

t.

- L

endi

ng 1

00 ta

ka to

a fe

mal

e le

ads

to

addi

tiona

l con

sum

ptio

n of

8 ta

ka a

nnua

lly. -

M

icro

cred

it co

ntrib

utes

to a

ppro

xim

atel

y on

e th

ird to

one

hal

f to

redu

ce p

over

ty. -

M

icro

cred

it ef

fect

s ar

e st

rong

er fo

r ex

trem

e po

vert

y.

Kha

nder

(20

05)

- N

on r

ando

miz

ed e

valu

atio

n. -

Fix

ed-e

ffect

s es

timat

or in

ord

er to

dro

p ou

t the

fixe

d (a

nd

unob

serv

able

) in

divi

dual

-spe

cific

and

vill

age

char

acte

ristic

s.

- B

angl

ades

h (B

RA

C, B

RD

B, G

ram

een

Ban

k); P

anel

dat

a fr

om W

orld

Ban

k an

d B

angl

ades

h In

stitu

te o

f Dev

elop

men

t S

tudi

es (

year

s 19

91/1

992;

199

8/19

99).

- K

ey id

entif

ying

ass

umpt

ions

for

caus

al

infe

renc

e do

not

hol

d (R

oodm

an, M

ordu

ch,

2009

). -

Intr

oduc

tion

of p

anel

dat

a do

es n

ot

solv

e th

e la

ck o

f cle

arly

exo

geno

us v

aria

tions

in

usi

ng m

icro

cred

it. -

Mic

rocr

edit

impa

ct in

re

duci

ng e

xtre

me

pove

rty

does

not

aris

e fr

om

dire

ct e

stim

atio

n (R

oodm

an, M

ordu

ch, 2

009)

.

Stu

dyM

etho

dolo

gica

l app

roac

hD

ata

Crit

ical

asp

ects

Res

ults

Sou

rce:

per

sona

l ela

bora

tion

on th

e ba

sis

of li

tera

ture

ref

erre

d to

.N

ote:

I al

so in

trod

uce

in th

is p

rosp

ect m

icro

savi

ngs

prog

ram

mes

. A g

reat

dea

l of m

icro

cred

it pr

ogra

mm

es in

clud

e, in

add

ition

to a

mer

e di

strib

utio

n of

the

loan

s, s

avin

gs s

ervi

ces.

*

BR

DB

cor

resp

onds

to B

angl

ades

h R

ural

Dev

elop

men

t Boa

rd, a

pub

lic s

ecto

r or

gani

zatio

n w

orki

ng fo

r ru

ral d

evel

opm

ent a

nd p

over

ty a

llevi

atio

n in

Ban

glad

esh.

(http

://w

ww

.brd

b.go

v.bd

).*

SE

ED

is a

ban

king

pro

duct

des

igne

d to

hel

p cl

ient

s sa

ve b

y bi

ndin

g th

eir

fund

s un

til th

ey r

each

ed a

spe

cific

sav

ings

pur

pose

.*

The

Len

der

in q

uest

ion

was

mer

ged

into

a la

rge

bank

hol

ding

com

pany

in 2

005;

it d

oes

not e

xist

as

a si

ngle

ent

ity. (

Kar

lan,

Zin

man

, 201

0).

- A

cces

s to

sav

ing

acco

unt h

ad a

pos

itive

im

pact

on

fem

ale

prod

uctiv

e in

vest

men

ts. -

In

crea

se in

inco

me

leve

ls fo

r fe

mal

e en

trep

rene

urs.

- H

igh

rate

of r

etur

n to

cap

ital

for

wom

en, r

ougl

y 5.

5% p

er m

onth

at t

he

med

ian.

Duf

lo e

t al.

(200

9)

- R

ando

miz

ed e

valu

atio

n. -

Ran

dom

sel

ectio

n of

52

of 1

04 s

imila

r po

or a

reas

as

loca

tion

for

new

br

anch

es o

f Spa

ndan

a (in

the

Indi

an c

ity o

f H

yder

abab

).

- S

pand

ana

(Ind

ia).

Bas

elin

e su

rvey

co

nduc

ted

in 2

005

(120

are

as a

nd 2

.800

ho

useh

olds

). S

ixte

en a

reas

wer

e dr

oppe

d fr

om th

e st

udy

befo

re

rand

omiz

atio

n (b

ecau

se o

f lar

ge

pres

ence

of m

igra

nt-w

orke

r ho

useh

olds

).

Hen

ce, o

nly

104

area

s w

ere

avai

labl

e fo

r th

e an

alys

is. -

Spa

ndan

a do

es n

ot

spec

ified

loan

pur

pose

.

- T

he p

oten

tial b

orro

wer

s in

sel

ecte

d ar

eas

are

poor

, but

not

"th

e po

ores

t of t

he p

oor"

. - S

hort

-ru

n re

sults

(15

-18

mon

ths)

.

- N

o im

pact

on

mea

sure

s of

hea

lth,

educ

atio

n an

d w

omen

's d

ecis

ion

mak

ing.

-

Hou

seho

lds

with

an

exis

ting

busi

ness

at

prog

ram

tim

e in

crea

se in

vest

men

t in

dura

ble

good

s; h

ouse

hold

s w

ith h

igh

prop

ensi

ty to

st

art n

ew a

ctiv

ity in

crea

se d

urab

le g

oods

sp

endi

ng, w

hile

thos

e w

ith lo

w p

rope

nsity

ris

e no

ndur

able

spe

ndin

g.

Dup

as, R

obin

son

(200

9)

- R

ando

miz

ed e

valu

atio

n (M

icro

savi

ngs,

Ken

ya).

-

Sam

pled

sub

ject

s w

ere

rand

omly

div

ided

into

tr

eatm

ent a

nd c

ontr

ol g

roup

s, s

trat

ified

by

gend

er/o

ccup

atio

n. T

hen

the

trea

ted

units

rec

eive

d a

prop

osal

to o

pen

a sa

ving

s ac

coun

t at n

o co

st,

whi

le th

e co

ntro

l uni

ts d

id n

ot b

enef

it fr

om a

ny

assi

stan

ce in

ope

ning

the

sam

e ac

coun

t.

- F

our

sour

ces

of d

ata:

1)

surv

ey

cond

ucte

d by

aut

hors

abo

ut b

asel

ine

char

acte

ristic

s of

par

ticip

ants

(ho

useh

old

com

posi

tion,

mar

ital s

tatu

s, h

ealth

, etc

.).

2) A

dmin

istr

ativ

e da

ta fr

om th

e vi

llage

ba

nk (

Bum

ala,

Ken

ya).

3)

Cog

nitiv

e ab

ility

mea

sure

s an

d tim

e an

d ris

k pr

efer

ence

s di

rect

ly e

licite

d fr

om

resp

onde

nts.

4)

Det

aile

d da

ta c

olle

cted

on

res

pond

ents

thro

ugh

daily

sel

f-re

port

ed lo

gboo

ks (

incl

udin

g in

form

atio

n ab

out i

ncom

e, e

xpen

ditu

re, h

ealth

, in

com

e sh

ocks

, etc

.).

- R

ando

m s

ampl

e is

sm

all (

185

mic

roen

trep

rene

urs)

. - T

arge

t are

a is

lim

ited

to

a si

ngle

site

and

to a

sin

gle

mic

rofin

ance

in

stitu

tion.

44

- T

reat

ed g

roup

tend

s to

shr

ink

thei

r bu

sine

sses

com

pare

d to

the

cont

rol g

roup

. -

No

evid

ence

that

incr

easi

ng a

cces

s to

cre

dit

impr

oves

sub

ject

ive

wel

l-bei

ng. -

Pos

itive

im

pact

of e

xpan

ding

cre

dit a

cces

s on

mal

e pr

ofits

. - M

ale

mic

roen

trep

rene

urs

use

incr

ease

d pr

ofits

to in

vest

in h

uman

cap

ital

of th

eir

kids

.

Kar

lan,

Zin

man

(20

10)

- R

ando

miz

ed e

valu

atio

n. -

Qua

ntita

tive

Cre

dit

scor

ing

is u

sed

to r

ando

miz

e th

e ap

prov

al d

ecis

ion

for

mar

gina

lly c

redi

twor

thy

appl

ican

ts.

- F

irst M

acro

Ban

k (P

hilip

pine

s, M

anila

) -

The

sam

ple

is m

ade

up o

f 1.6

01

mar

gina

lly c

redi

twor

thy

appl

ican

ts to

w

hich

1.2

72 w

ere

assi

gned

to th

e tr

eatm

ent g

roup

and

329

to th

e co

ntro

l gr

oup.

- P

eopl

e ar

e no

t ver

y po

or. U

sing

cre

dit

scor

ing

to r

ando

miz

e al

low

s to

mea

sure

onl

y tr

eatm

ent e

ffect

s on

the

mar

gina

lly

cred

itwor

thy.

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2011 n.180* Cristina Elisa Orso: Microcredit and poverty. An overview of the principal statistical methods used to measure the program net impacts

2011 n.179** Noemi Podestà e Alberto Chiari: La qualità dei processi deliberativi

2011 n.178** Stefano Procacci: Dalla Peace Resarch alla Scuola di Copenhagen. Sviluppi e trasformazioni di un programma di ricerca

2010 n.176** Fabio Longo and Jőrg Luther: Costituzioni di microstati europei: I casi di Cipro, Liechtenstein e Città del Vaticano

2010 n.175* Mikko Välimäki: Introducing Class Actions in Finland: an Example of Lawmaking without Economic Analysis

2010 n.174* Matteo Migheli: Do the Vietnamese support Doi Moi?

2010 n.173* Guido Ortona: Punishment and cooperation: the “old” theory

2010 n.172* Giovanni B. Ramello: Property rights and externalities: The uneasy case of knowledge

2010 n.171* Nadia Fiorino and Emma Galli: An analysis of the determinants of corruption: Evidence from the Italian regions

2010 n.170* Jacopo Costa and Roberto Ricciuti: State capacity, manufacturing and civil conflict

2010 n.169* Giovanni B. Ramello: Copyright & endogenous market structure: A glimpse from the journal-publishing market

2010 n.168* Mario Ferrero: The cult of martyrs

2010 n.167* Cinzia Di Novi: The indirect effect of fine particulate matter on health through individuals' life-style

2010 n.166* Donatella Porrini and Giovanni B. Ramello: Class action and financial markets: Insights from law and economics

2010 n.165** Corrado Malandrino: Il pensiero di Roberto Michels sull'oligarchia, la classe politica e il capo carismatico. Dal Corso di sociologia politica (1927) ai Nuovi studi sulla classe politica (1936)

2010 n.164ε Matteo Migheli: Gender at work: Productivity and incentives

2010 n.163Q Gian-Luigi Bulsei and Noemi Podestà (Eds): Imprese differenti. Le organizzazioni cooperative tra crisi economica e nuovo welfare

2010 n.162* Claudia Cusinello and Franco Amisano: Analysis for the implementation of a sustainable transport model in the eastern Piedmont county of Alessandria, Italy

2010 n.161* Roberto Ricciuti: Accumulazione del capitale e crescita economica tra Italia liberale e regime fascista

2010 n.160* Carla Marchese and Giovanni B. Ramello: In the beginning was the Word. Now is the Copyright

2010 n.159ε Peter Lewisch, Stefania Ottone and Ferruccio Ponzano: Free-riding on altruistic punishment? An experimental comparison of third-party-punishment in a stand-alone and in an in-group environment

2009 n.158* Rongili Biswas, Carla Marchese and Fabio Privileggi: Tax evasion in a principal-agent model with self-protection

2009 n.157* Alessandro Lanteri and Stefania Ottone: Economia ed etica negli esperimenti

2009 n.156* Cinzia Di Novi: Sample selection correction in panel data models when selectivity is due to two sources

2009 n.155* Michela Martinoia: European integration, labour market dynamics and migration flows