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Year 4

Figure 8.1

Sources of income for treatment and control groups.

Year 0

Year 0

C2 Year 4

C2 Year 4

"microfinance impact" in the bold box. The impact is felt by a "typical" person who gains access to a microfinance program. We term this position T2, taken to be four years after the program started. Before access to the program, in year 0, this person's income is reflected by position T1. The difference between T2 and T1 is a useful place to start as it nets out the roles of those measured and unmeasured individual attributes that do not change over time, as well as location-related issues. But while the difference captures the microfinance impact, it also reflects broader economic and social changes that occur between year 0 and year 4 and that are independent of microfinance. It would thus be misleading to attribute the entirety of the T2 - T1 difference to the microfinance impact. The problem is that we cannot parse it without more information.

Identifying a control group is thus critical. Figure 8.1 shows a plausible control group from an area without access to microfinance. It would be very unlikely to find a population that was exactly identical to the "treatment" population. And we see here in this example, that base income levels start at a lower level for the control group. Thus, comparing the difference between T2 and C2 will help address biases due to the broadly felt economic and social changes, but it will not account for the differing base levels. Isolating the true microfinance impact requires comparing the difference T2 - T1 with the difference C2 - C1, which is a so-called difference-in-difference approach.

Given the setup in figure 8.1, the difference-in-difference approach is adequate to deliver accurate measures of microfinance impacts. But we have made an implicit assumption that we now need to put on the table. We have taken the impacts of personal attributes like age, education, and entrepreneurial ability to be unchanging over time. Thus, their effects net out when we look at T2 - T1 and C2 - C1. But in reality, these characteristics may change over time (perhaps a borrower gets more education or strengthens their social networks, for reasons unrelated to microfinance), or they may directly affect changes over time, so they do not net out as assumed. More capable entrepreneurs will likely have greater earnings growth, for example, and not just a higher base level of income. When the relevant variables are not measurable, the problem is mitigated by making sure that control groups are as comparable to treatment groups as possible.

To find comparable treatment groups, we need to consider who joins microfinance programs in the first place. Figure 8.2 gives a plausible scenario, where the focus is just on entrepreneurial ability. Participants tend to have more entrepreneurial ability and nonparticipants tend to have less. Participants thus have higher incomes—and potential for income growth—before the microfinance program even arrives. Comparing microfinance borrowers in a given village to their neighbors who decide not to participate is thus apt to run into problems. The former already has an advantage, reflected by the average income level IP, relative to their nonparticipating neighbors with average income level INP. As noted earlier, the concern is that unmeasured attributes such as entrepreneurial ability may affect both income growth and initial income levels.

So, imagine that we had access to data from another village that was identical to the one depicted in figure 8.2, except that the second village lacked a microfinance program. It would seem to provide a perfect



Nonparticipants tend to come

Unmeasured entrepreneurial ability

Nonparticipants tend to come from this range

Participants tend to come from this range

Figure 8.2

The hypothetical relationship between unmeasured entrepreneurial ability and income in a given village.

control group. But how should it be used? Figure 8.2 shows that comparing the income of participants in the treated village to the population average in the control village will also create problems since the former group is self-selected while the latter is not. The problem of course is that by definition there are no participants in the control village since it has no program yet.

Two solutions present themselves. The first solution is to change the question. We have been asking: What is the effect of microfinance participation? But instead we could ask: What is the effect of microfinance access—whether or not villagers ultimately end up participating? To answer this second question (which may well be more relevant from a policy standpoint), it is only necessary to compare outcomes for the entire population in the treatment village (or, more easily, a random sample drawn from the entire population) against a sample drawn from the control village. A second solution, used by Coleman (1999), is to try to identify future borrowers in the control villages and to compare the actual microfinance participants to the set of future participants. A third approach, that is common but problematic, involves comparing older borrowers in a given village to newer borrowers who are just joining the program. The main difficulty with this approach involves nonrandom attrition, an issue discussed in section 8.4.2.

8.4 Addressing the Selection Problem in Practice

In the following sections, we consider a series of related approaches to impact evaluation. The overview is not exhaustive and we do not aim to provide a full survey of impact surveys to date. Rather, we aim to point to key methodological issues and to gather several important results. The results to date are decidedly mixed, with some evidence of modest positive impacts of microfinance on income, expenditure, and related variables, while other studies find that positive impacts disappear once selection biases are addressed. There have been few serious impact evaluations of microfinance so far, though, so a collection of definitive results is still awaited. All the same, the existing studies provide useful insights and directions for future research.

8.4.1 Using Data on Prospective Clients in Northeast Thailand

A number of recent studies use novel research designs to address selection biases. One approach is to use information on borrowers before the microfinance program enters. Coleman (1999) and (2002) takes advantage of a particular way a microfinance program was implemented in Northeast Thailand, providing a unique way to address selection bias. He gathered data on 445 households in fourteen villages. Of these, eight had village banks operating at the start of 1995. The remaining six did not, but village banks would be set up one year later. Interestingly (and critically for the evaluation), at the beginning of 1995, field staff from the village bank programs organized households in these six villages into banks, allowing the households to self-select according to the village bank's standard procedures. But then the households were forced to wait one year before getting their first loans.

The unusual procedure on the part of the programs allows Coleman to analyze who joins and who does not before the village banks start running. Moreover, it allows him to estimate the following regression equation:

where the variable to be explained Yj is a household-level outcome— income or profit—for household i in village j. The regression approach allows a refinement of the difference-in-difference approach discussed in section 8.3. Here, "dummy variables" (i.e., variables that only take the values of zero or one) are used to control for location and participation status. Other variables control for factors like age and education.7 The variables Xij capture household characteristics (and a constant term); and Vj is a vector of village dummy variables that control for all fixed characteristics of the village. The two variables of most interest are Mij and Tj. The first is a "membership dummy variable" that equals one for both actual members of the village banks and those villagers who have opted into the programs (in the control villages) but who have not yet received loans. Coleman argues that Mij controls for selection bias so that S, the coefficient on Tj, is a consistent estimate of the causal treatment effect. In his application, the variable Tij is the number of months that village bank credit was available to (actual) members, which is exogenous to the household.

Controlling for selection makes an important difference. Coleman (1999) finds that average program impact was not significantly different from zero after controlling for endogenous member selection and program placement. When he extends the estimating framework to differentiate between impacts on "rank-and-file members" and members of the village bank committee (who tend to be wealthier and more powerful), he finds again that most impacts were not statistically significant for rank-and-file members, but there were some noted impacts for committee members, particularly on wealth accumulation.

Coleman cautions, though, that the results need to be put into the context of the larger financial landscape. Thailand is relatively wealthy (at least compared to Bangladesh), and villagers have access to credit from a range of sources—some at low interest rates from government-backed sources. Strikingly, survey households held over 500,000 baht in wealth on average and had over 30,000 baht of "low-interest" debt (excluding village bank debt). Thus, the village banks' loans of 1,500 to 7,500 baht may be too small to make a notable average difference in the welfare of households; in fact, complaints about small loan sizes prompted some women to leave the banks. Coleman argues that one reason that wealthier borrowers may have experienced larger impacts was because they could commandeer larger loans.

8.4.2 Attrition Bias: Problems When Using "New Borrowers" as a Control Group in Peru

A problem in trying to replicate Coleman's approach is that it's not often that a researcher comes upon programs that go through the trouble of organizing villagers but then delay credit disbursement for a period. So instead, researchers have tried to capture the flavor of the approach by comparing "old borrowers" to "new borrowers" within the same area. Typically this is done with cross-sectional data, yielding an approach that is simple and relatively inexpensive (and which does not require surveying nonborrowers). This procedure has been promoted by USAID through its AIMS project (more on this to come) and by other microfinance organizations (Karlan 2001).

Assuming that the characteristics of people who enter into programs are unchanging over time, the method should account for the fact that borrowers are not a random group of people. But assuming that the relevant characteristics are similar over time requires a leap of faith. Why didn't the new borrowers sign up earlier? Why were the older borrowers first in line? If their timing of entry was due to unobserv-able attributes such as ability, motivation, and entrepreneurship, the comparisons may do little to address selection biases—and could, in fact, exacerbate bias.

Karlan outlines two additional problems based on his experience evaluating village banks organized by FINCA Peru. Assume that the conditions of selection are constant over time so that the same kinds of people become clients today as who became clients five years ago. All seems well, but there are still two potential biases, both of which are most pronounced when assessing impacts using cross-sectional data. Both are also due to dropouts.

Dropouts are an ongoing microfinance reality. Sometimes borrowers leave because they are doing so well that they no longer need microfinance; but, more often, it is the borrowers in trouble who leave. Wright (2001) gives evidence that dropout rates are 25-60 percent per year in East Africa. In Bangladesh, Khandker (2003) estimates rates for three leading lenders of 3.5 percent per year between 1991 and 1992 and 1998 and 1999 (which is much smaller than the numbers cited by Wright, nonetheless, they can add up over time). Gonzalez-Vega et al. (1997, 34-35) provide parallel data for Bolivia. They investigate the fraction of people who ever borrowed from a given microlender that are still active borrowers at the time of their suvey (the end of 1995). The resulting proxy for retention rates shows that just half of BancoSol clients were still active. In rural areas, two-thirds of borrowers from PRODEM were still active, possibly reflecting the fact that there are fewer alternative lending sources in the countryside.

It is likely that these "older borrowers" (i.e., those who remain active) have the positive qualities of survivors, while "new borrowers" have yet to be tested. If the failures are more likely to drop out, comparing old to new borrowers will overestimate impacts. We suspect that this patten is most often the case, but, as suggested earlier, the prediction is not clear-cut. If it is mainly the successes that move on (leaving weaker clients in the pool), the sign of bias will be reversed, underestimating causal impacts.

The second problem is due to nonrandom attrition independent of actual impacts. If richer households are more likely to leave, the pool of borrowers' becomes poorer on average. Then it could look like microfinance borrowing depletes one's income, when in fact it may have no impact at all. Conversely, when lower-income households leave in greater numbers, impacts will be overstated.

Karlan argues for hunting down the dropouts and including them in the analysis along with the other older borrowers, though it may be costly. A cheaper improvement would be to (1) estimate predictors of dropout based on observable information on older borrowers; then (2) form a prediction of who among the new borrowers is likely to (later on) drop out; and (3) use the prediction to weigh the new borrower control group. The method is not perfect, though: In particular, dropouts who made their decision based in part on the size of impact are not addressed by the reweighing scheme.

8.4.3 Longitudinal Data: USAID AIMS Studies in India, Peru, and Zimbabwe

Some biases can be mitigated by using data collected at several points in time, allowing "before versus after" comparisons as described in section 8.3. Under certain conditions, the approach controls for both nonrandom participation and nonrandom program placement. But when those conditions are not met, the approach is subject to biases due to unobservable variables that change over time—hard-to-observe characteristics such as entrepreneurial spirit and access to markets that are likely to be correlated with borrowing status.8

The most ambitious longitudinal studies to date are those sponsored by USAID in the late 1990s, with the hope to demonstrate methods and generate benchmarks.9 Teams analyzed impacts on members of SEWA (a labor organization and microlender serving women in the informal sector in Ahmedabad, India), Mibanco (an ACCION International affiliate in Peru), and the Zambuko Trust in Zimbabwe. Baseline data was collected and then the same households were resurveyed two years later. Case studies were also conducted alongside the statistical analyses.

The teams selected clients randomly from lists provided by the programs. The trick was then to identify control groups. In India and Peru, the control group was a random sample drawn from nonparticipants in the same regions who met program eligibility criteria. In Zimbabwe, enumerators instead used a "random walk procedure" in which they set off in a given direction to find nonclient households for the control group. As Barnes, Keogh, and Nemarundwe (2001, 19) explain, "For example, when the client's business was in a residential area, from the front of the house the interviewer turned right, went to the first road intersection, turned right and walked to the third intersection and then turned left; from there the interviewer asked a series of questions to identify who met the criteria for inclusion in the study." The criteria used to match treatments and controls were gender, enterprise sector and geographic location, as well as additional criteria added by Zambuko Trust: "a) never received credit from a formal organization for their enterprise, b) be the sole or joint owner of an enterprise at least six months old, and c) not be employed elsewhere on a full-time basis" (Barnes, Keogh, and Nemarundwe 2001, 19).

The data have potential, and the researchers followed dropouts as best they could to avoid the attrition biases described earlier. With two years of data, the researchers could have analyzed impacts by investigating how changes in microfinance participation affect changes in outcomes. But, surprisingly, the AIMS researchers chose not to analyze variables converted to changes over time, which would have eliminated all biases due to omitted variables that do not change over time (i.e., to analyze differences-in-differences as described in section 8.3). The stated rationale is that the "differencing" procedure also eliminates the chance to analyze the roles of variables such as gender and enterprise sector that are also fixed through time, and so alternative methods (analysis of covariance) were used (Dunn 2002). In our view, the costs of that choice far outweigh the benefits.

To see the differencing method (i.e., the method not used), we can modify equation (8.1) to specify that the variables are measured in a given time period t:

As before, we are interested in estimating the value of S, but here it is the coefficient on the value of loans received. (The two variables, value of loans and length of membership, are typically very similar since loan sizes and length of time borrowing often move closely together.) The dependent variable, Y^, is a household-level outcome (income or profit) for household i in village j at time t. The variables Xj capture household characteristics at t (and a constant term), and Vj is a vector of village dummy variables that are assumed to be unchanging over time. The dummies will capture village-level features like distance to the closest major city, proximity to major transportation and markets, and the quality of local leadership. Similarly, we assume that the individual-specific variable Mj, the variable that captures nonrandom individual selection into the program, is also unchanging over time. It may reflect, for example, an individual's energy level, management ability, and business savvy. In this case, though, we do not assume that it is observable. Thus, there is a potential bias stemming from its omission when equation (8.2) is estimated.

The problem can be addressed by estimating in differences. Assume that we have the same variables collected in period t + 1:

where A indicates the difference in the variables between periods t and t + 1. Here, the village dummies drop out, as do the fixed (and unob-servable) individual-specific characteristics (which was the concern that prompted the AIMS researchers not to follow this method). The benefit, though, is considerable: A consistent estimate of the impact S can be obtained (which is the most important aim).10

It turns out that the omitted unobservables in equations like (8.2) do make a large difference, and not addressing them undermines the credibility of the AIMS impact studies. When Alexander (2001) returns to the AIMS Peru data and estimates the equations in differences (akin to equation 8.4), she finds that estimated impacts on enterprise profits fall. In fact when she controls for reverse causality by using an instrumental variables approach (more on this to follow), the estimated impacts shrink and are no longer statistically significant. Selection bias is clearly a major problem, but results might be different if the two surveys had been collected more than two years apart or if other instrument variables had been used. Below we address why finding instrumental variables continues to be a challenge.

Then, we can subtract equation (8.2) from (8.3) to obtain

8.4.4 Using a Quasi-Experiment to Construct Instrumental Variables: Bangladesh Studies

A different way of approaching the problems above would have been to search for an instrumental variable for microfinance participation. The instrumental variables method allows researchers to address problems posed by measurement error, reverse causality, and some omitted variable biases. The instrumental variables strategy involves finding an additional variable (or set of variables) that explains levels of credit received, but that has no direct relationships with the outcomes of interest (like profit or income). Then a proxy variable can be formed based on the instrumental variable, and it can be used to tease out the causal impact of credit access.

The interest rate is a potential instrumental variable—or simply "instrument"—since it can explain how much credit a borrower desires while not being a direct determinant of income in itself (that's testable, at least). The trouble is that interest rates seldom vary within a given program, and the statistical techniques are impossible without some variation. And, while it is true that interest rates vary when comparing clients of different institutions—both formal and informal—it is likely that the variation partly reflects unobserved attributes of the borrowers, undermining the use of interest rates as instruments. Lender characteristics are also candidates for instrumental variables. Similar to all other community-level variables, though, they will be wiped out when including village dummy variables in specifications when there is no variation in program access within a village. In short, the instrumental variables approach can be powerful, but finding convincing instrumental variables for credit has been frustrating.

But when there is within-village variation in program access, rules determining eligibility can be the basis of an evaluation strategy, an approach employed in a series of studies of microfinance in Bangladesh. Over the years 1991 and 1992, the World Bank-Bangladesh Institute of Development Studies surveyed nearly 1,800 households in eighty-seven villages in Bangladesh; most villages were served by microlenders but fifteen were not. In 1998 and 1999, teams were sent back to find the same households, but by then all of the villages were served by microlenders.11 After losing some households through attrition, 1,638 households were left that were interviewed in both rounds.

In a sign of the rapid spread of microfinance in Bangladesh, about one quarter of the sample included a microfinance customer within the household in 1991-1992, but by 1998-1999 the figure had jumped to about half.12 The jump makes program evaluation more difficult, but not impossible. To complicate matters, about 11 percent of customers were members of more than one microfinance institution in 1998-1999. Estimates from the 1991-1992 Cross Section The first round of data has, on its own, generated a series of papers; the most important results have been compiled in Khandker's (1998) Fighting Poverty with Microcredit. Completing impact studies with just a single cross-section requires ingenuity and some important assumptions, and the task was made more challenging by the desire to estimate impacts of borrowing by men and by women separately. The studies are sophisticated in their use of statistical methods to compensate for the fundamental limitations of the data set. One large limitation arises because the researchers were eager to generate results with the first wave of the data rather than waiting for the second. That the studies use heavier statistical artillery than other microfinance studies does not necessarily mean that they deliver results that are more reliable or rigorous than other studies. In fact, as we describe later, the studies are open to questions about the validity of the underlying assumptions that prop up the statistical framework.

On the face of it, it would seem impossible to get far with just a single cross-sectional data set and without a special setup like that of Coleman (1999). But the way that microlenders in Bangladesh implement their programs opens a door for researchers. To capture the basic insight, figure 8.3 shows two hypothetical villages, one with a program (the treatment village) and one without (the control village). The villages are separated into distinct groups based on their eligibility and participation status; we discuss how eligibility is determined shortly. The groups within the thick black lines are eligible to borrow (or, in the case of the control village, would be eligible). As a first step, researchers could compare the incomes and other outcomes of microfinance participants to nonparticipants just using data from the treatment village, but it is impossible to rule out selection biases of the sort described in section 8.3. It is also possible to use the control villages to compare participants from the treatment villages served by microfinance to the eligible households from the control villages, but even here there are potential selection biases since the participants are still a select group.

A more satisfactory approach is to compare eligible households (all households within the thick black lines) between the two villages. Here, the goal is to estimate the impact of microfinance access rather

Figure 8.3

Example of impact evaluation strategies using eligibility rules.

"Treatment village" (microlender present)

"Control village" (no microlender)

Figure 8.3

Example of impact evaluation strategies using eligibility rules.

than actual participation. The benefit is that a clean estimate of the average impact of access may be more useful than a biased estimate of the impact of participation. Moreover, if there are no spillovers from participants to nonparticipants, it is possible to recover a clean estimate of the impact of participation from the estimate of access (by simply dividing the latter by the fraction of households in the village that participate). The assumption that there are no spillovers is strong, though, and Khandker (2003) finds evidence against it.

The fault with the latter approach is that while selection biases at the household-level are addressed, it does not address biases stemming from nonrandom program placement. As mentioned earlier, villagers served by microlenders may seem to do poorly relative to control groups just because the microlender chooses to work in isolated, dis-advantaged villages. In other cases, villages may be doing better than average even without the microlender, so the bias would go in the other direction; estimated impacts would be too high.

A potential solution is at hand, though, provided by the particular way that the selected microlenders determine eligibility for program access. Pitt and Khandker (1998) develop a framework for estimating impacts using the 1991-1992 cross-section. The starting point is the observation that the three programs being studied—Grameen Bank, BRAC, and the state-run RD-12—all share the same eligibility rule. In order to keep focused on the poorest, the programs restrict their services to the "functionally landless"; this is implemented through a rule declaring that households owning over half an acre of land are not allowed to borrow. The individual programs place some additional restrictions, but the half-acre rule is the common criterion. So, in terms of figure 8.3, the functionally landless are encompassed by the thick black lines, and the noneligible lie outside. The fact that there are ineligible households within villages with programs means that there is another control group that can help alleviate concerns that the microlenders choose villages that are special in one way or another.

An improved estimation strategy—but not the one adopted by Pitt and Khandker—is to compare differences-in-differences as described in section 8.3. It involves comparing the outcomes of households with microfinance access to the outcomes of households that are ineligible, but living in treatment villages. The strategy then turns to the control villages where the ineligible are compared to those who "would be" eligible. Finally, those two comparisons are pitted against each other. The result tells us if households with access to microfinance are doing better than their ineligible neighbors, relative to the difference in outcomes between functionally landless households in control villages versus their ineligible neighbors.

One can do even better by implementing this strategy in a regression framework that also accounts for a broad range of household characteristics. In the regression framework, the difference-in-difference strategy would be implemented as

The idea is very similar to that of equation (8.1), but two important changes are made. First, Eij is a dummy variable that reflects whether or not a household is functionally landless and thus eligible to borrow from a microlender (whether or not there is in fact a microlender present in the village). The variable equals one if a household is within the thick black lines in either village in figure 8.1. The other important change is the variable (Tij ■ Eij), which is the product of Eij and a dummy variable that indicates whether or not the household is in a treatment village; it equals one only if the household is within the thick black lines in the village with a microlender. The coefficient on the dummy variable gives the average impact of credit access—after controlling for being functionally landless, living in a particular village, and having specific household characteristics.

Morduch (1998) takes the approach in equation (8.5) and finds no sharp evidence for strong impacts of microfinance on household consumption, but he finds some evidence that microfinance helps households diversify income streams so that consumption is less variable across seasons. The estimates, though, rely on the assumption that the village dummy variables perfectly capture all relevant aspects about the villages that would influence microlenders' location decisions. In this setting, though, the village-level dummies only control for unob-servables that affect all households in a village identically (and linearly). Nonrandom program placement thus remains an issue if, as is plausible, the functionally landless are noticeably different from their wealthier neighbors (noticeable to bank staff but not the econo-metrician), and if the programs take this into account when deciding where to locate. In that case, the dummy variable (Tj • Ej) could pick up the effects of those inherent differences, thus biasing estimated impacts.

Morduch (1998) also takes a closer look at the eligibility rule on which the strategy rests. As Pitt and Khandker (1998) point out, it is important that landholdings are exogenous to the household—that is, households are not, for example, selling land in order to become eligible to borrow. If that was the case, selection biases would creep back in—even when estimating using equation (8.5)—since unobservably promising borrowers would be taking special steps to switch their eligibility status. Pitt and Khandker cite the fact that in southern India in the 1980s, village land markets tended to be thin, and most land was acquired through inheritance. In that case, landholdings were exogenous to the household and unlikely (or at least much less likely) to be correlated with unobserved potential. But Bangladesh in the 1990s is not southern India in the 1980s, and land markets in the study area turn out to be fairly active—and this is evident upon closer inspection of the landholding module of the data set. On the other hand, Morduch (1998) finds no evidence that households are selling land in order to meet microfinance eligibility criteria. If anything, successful borrowers are buying land, and one explanation for Morduch's inability to find significant impacts on household consumption could be that funds were instead going to land (and other asset) purchases.

The reason that households are not selling land to gain access to microfinance raises another tricky issue. It turns out that the microlenders were not following the eligibility criteria strictly; so many households owning over a half an acre were nonetheless borrowing in 1991-1992. As a result, there was no reason to sell land to become eligible. Khandker (2003) acknowledges the problem and finds that 25 percent of borrowers were over the half-acre line in 1991-1992 and 31 percent were over in 1998-1999.13 Pitt (1999) follows up on the issue and suggests that households with more land have lower quality land, so they still may be impoverished, even if they are not (strictly speaking) functionally landless. But a problem remains: the eligible households in the control villages were surveyed on the basis of a strict interpretation of the half-acre rule, while the eligible households in the treatment villages include the mistargeted households. Morduch (1998) adjusts the samples in order to maintain comparability, and Pitt (1999) does robustness checks to show that the Pitt and Khandker (1998) results change little when mistargeting is taken into account.14

These issues should be borne in mind when turning to the Pitt and Khandker (1998) framework. We start by noting that equation (8.5) (which can be run using ordinary least squares) is closely related to the following instrumental variables approach estimate instead:

where Cj is the amount of credit received and Tj • Ej is employed as an instrumental variable.15 Estimating equation (8.6) using ordinary least squares would bring trouble since households who have received more and larger loans can be expected to be different in unobservable ways from those who have received fewer loans (leading to a variant of selection bias associated with loan size). The instrumental variables method addresses the problem and leads to a clean estimate of 8", the average impact of credit access (subject to the same caveats as village dummy variables noted earlier).

Before moving on to the method used by Pitt and Khandker (1998), note that the instrument Tj • Ej is a dummy variable that only reflects credit access. The estimate of 8" thus does not draw on variation in how much credit is received, it only depends on whether credit is received. The step taken by Pitt and Khandker is to expand to a larger set of instruments, in effect, by using Xj • Tj • Ej as instruments. The step yields as many instruments as there are X's. (The X's include education and various aspects of household demographics.) The move means that the estimate of d" takes advantage of variation in how much credit households receive.

An important identifying assumption is that the specification in equation (8.6) is correct so that education and demographics affect household outcomes in exactly the same way for the whole sample; otherwise, biases enter back in. In other words, it is assumed that there are no important nonlinear relationships in the ways that age, education, and the other variables influence outcomes of interest.16 Another critical identifying assumption stems from their use of a Tobit equation to explain credit demand in a first stage in which they are effectively creating the instrumental variables used in the final regressions. The Tobit provides a way to efficiently handle variables with many zero values (like credit); but it requires that, in the second stage estimation, all microfinance impacts are assumed to be identical across borrowers, an assumption that is often made out of necessity but that stretches plausbility here. It also implies (implausibly) that marginal and average impacts of credit are equal. Estimating using a simpler two-stage least squares method would lead to consistent estimates without requiring these assumptions, but the method is less efficient (i.e., coefficients would tend to have larger standard errors). By using the Tobit, the efficiency of the estimators is improved.

Pitt and Khandker take one more step to investigate credit received by men separately from credit received by women (motivated by the concerns raised in chapter 7). To do this, they take advantage of the fact that microlending groups are not mixed by gender in Bangladesh. In the eighty-seven villages surveyed in 1991-1992, ten had no female groups and twenty-two had no male groups (and forty had both, leaving fifteen villages with no groups). Identification in this case comes from comparing how the roles of age, education, and so forth for men with access to male groups compare to the roles for men without access. Similarly, for the characteristics of women with and without access.17

Pitt and Khandker's most cited result from the 1991-1992 cross-section is that household consumption increases by eighteen taka for every one hundred taka lent to a woman. For lending to men, the increase is just eleven taka for every one hundred taka lent. Men, according to the estimates, take more leisure when given the chance, explaining in part why household consumption rises less when they borrow. Nonland assets increase substantially when borrowing is by women, but not by men. Schooling of boys increases in general with borrowing, but schooling of girls only increases when women borrow from Grameen—but not when women borrow from the other programs. It cannot be ascertained from the estimates why loans to women have higher marginal impacts than loans to men. Pitt and Khandker interpret is as an indication of a lack of fungibility of capital and income within the household (which is plausible assuming that their basic result is correct). A very different interpretation is supported by the fact that loans to males tend to be larger so that the smaller relative impacts may be explained, at least in part, by the standard theory of declining marginal returns to capital. However, marginal returns would have to be very sharply diminishing, since loan sizes are in the same general ballpark.18

The 1991-1992 cross section has also been used to analyze noncredit program impacts, fertility and contraception choices, and impacts on seasonality and nutrition (for an overview, see Morduch 1999b). Khandker (1998) has used the basic impact numbers described earlier (imperfect as they be) to estimate broad impacts on poverty and to complete cost-benefit analyses (see chapter 9 for a more detailed discussion). The work is ambitious; but, as the previous discussion suggests, the underlying setup is far from perfect. The basic imperfections are not the fault of the researchers, but they do necessitate more structure, greater econometric sophistication, and a heavier load of assumptions than would otherwise be necessary. The second round of data collected in 1998-1999 provides hope that simpler methods may be able to deliver more robust, transparent results, but initial results are just being circulated as we write this book. Estimates from the Full Panel, 1991-1992 and 1998-1999

With the two rounds of data, Khandker (2003) estimates an equation along the lines of equation (8.4). As with the work on the cross section, he modifies the equation slightly, to allow for separate impacts when women borrow versus when men borrow. And in other specifications, he explores spillovers to nonborrowers who live in the same villages as borrowers. As noted earlier, the control villages from 1991 to 1992 all have programs by 1998-1999, so simple before and after comparisons in treatment versus control villages are not possible. In addition, the extent of mistargeting became more severe by the end of the 1990s.

The panel data allow us to see trends that help put the microfinance revolution in Bangladesh into perspective. Table 8.1 compiles data from Bangladesh in Khandker (2003). If we just look at the top panel of the

Table 8.1

Falling poverty in Bangladesh: Program participants versus nonparticipants

Table 8.1

Falling poverty in Bangladesh: Program participants versus nonparticipants

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