The authors are grateful to an anonymous referee for useful comments. We are also indebted to several individuals for their help with the field surveys, especially Afmad Efendi, Sabita Maharja, Subi Alwi, Risidianto, Tadianto Saputro, Alfan Vahad, and Dedy Aryanto. Opinions expressed in this paper are the sole responsibility of the authors and do not necessarily reflect those of the IDE-JETRO.
Indonesian microfinance is primarily operated by for-profit commercial banks, characterized by large-scale loans that require collateral. In 2003, the largest nongovernmental organization in the country introduced much smaller-scale loans without a collateral requirement. This scheme is commercialized but potentially more suited to the credit demands of the poor. Applying propensity score matching with the difference-in-difference method, this paper examines whether the emerging microcredit scheme has been successful in targeting and improving the welfare of the poor in the one year following loan disbursement. The results show that although collateral ownership is not an important determinant of participation, relatively wealthier families gain access to microcredit. The impact of microcredit on various household outcomes is generally statistically insignificant, except for sales of nonfarm enterprises for the nonpoor and schooling expenditures for the poor. This implies that the microcredit scheme under study might not have an immediate impact on poverty alleviation.
Poverty reduction has long been a primary political agenda in most developing countries. Indonesia is no exception. Over the past four decades, since the early days of the Soeharto regime, poverty reduction has been the central pillar of the national development plan. Since the second five-year development plan was launched in 1975, the three pillars of growth, equity, and stability have been explicitly recognized as the Development Trilogy, and various anti-poverty programs have been systematically implemented along with stimulation of economic growth. Coinciding with high levels of economic growth, the percentage of the poor fell remarkably from 40.1% in 1976 to 11.3% in 1996 (World Bank 2006). However, the Asian financial crisis of 1997 adversely affected Indonesian households as a whole, and the incidence of poverty jumped to 23.4% by 1999. Although the economy started to recover, the percentage of the poor was still relatively high at 17.8% in 2006 (World Bank 2006). Therefore, a major challenge for the incumbent Yudhoyono administration is to effectively reduce poverty.
One anti-poverty strategy pursued by successive governments of Indonesia has been the development of a microfinance industry. In fact, there have been numerous microfinance institutions (MFIs) serving different segments of society with different contract terms. Examples include commercial banks, state-owned pawnshops, secondary banks, cooperatives, nongovernmental organizations (NGOs), and informal moneylenders. In addition, the government has provided small cash transfers and credit under various development programs. Among those many institutions, for-profit state-owned and private commercial banks have played a dominant role, with little involvement by NGOs (Charitonenko and Afwan 2003). This is in sharp contrast to other microfinance pioneer countries such as Bangladesh and Bolivia, where NGOs play a vital role in providing microfinance (ProFI 2005). These NGOs generally make poverty reduction their primary goal, while commercial banks usually have profitability as their primary goal. Major characteristics of Indonesian commercialized microfinance include the following: (1) banks often charge relatively high interest rates to cover operational costs, (2) most require collateral to mitigate the default risks, and (3) most allow clients to borrow a relatively large amount of money to reduce transaction costs. As an example, the leading and most popular MFI in Indonesia, Bank Rakyat Indonesia (BRI), charges net annual effective interest rates of approximately 32%, requires collateral for loans and allows clients to borrow a maximum of Rp 50 million (Johnston and Morduch 2007).1 BRI has an excellent reputation in terms of number of clients, high repayment rates, and profitability.2 However, it is not evident that these microfinance services have reached the poorest of the poor who do not have sufficient collateral and/or who might require much smaller loans than banks would like to lend. Indeed, there is little solid evidence that BRI contributes in any significant way to improving the welfare of the poorest of the poor. Instead, some authors point out that BRI has served only the near poor and nonpoor households (Hulme and Mosley 1996; Armendáriz de Aghion and Morduch 2005).
Under such conditions, the largest NGO in the country, Yayasan Bina Swadaya (YBS), developed a regulated bank, Bank Perkreditan Rakyat (BPR), in the early part of this decade, and introduced a unique microcredit scheme for Indonesia. This program (hereafter BPR-YBS) is commercialized in that it seeks to make a profit and does not rely on government subsidies for operation. However, it is distinct from other commercial MFIs in that it explicitly seeks to help the poor move out of poverty.3 Therefore, no collateral is required in its credit scheme, and it provides clients with smaller loans at a competitive interest rate (30% per year), which are potentially more suited to the credit demands of the poor.4 Whether or not such a small-scale collateral-free microcredit scheme can really reach and improve the welfare of the poor is an important question to be addressed in this paper.
We will apply a rigorous evaluation technique to explore this question. The existing evaluation of Indonesian microcredit thus far has been mostly anecdotal, and little attempt has been made to control for potential bias in estimation.5 As is well known, the fundamental problem associated with program evaluation arises from the fact that outcomes of the same individuals with and without the program cannot be observed simultaneously. Therefore, differences in outcomes between actual participants and nonparticipants have been often viewed as a result of the impact of microcredit. Yet, because participants can self-select themselves into the program, and that program placement might not be random, participants and nonparticipants are likely to systematically differ in observable and unobservable characteristics (Kono and Takahashi 2010). Thus, in many cases, differences between participants and nonparticipants cannot be solely attributable to microcredit programs. The practical estimation problem is one of determining how to construct a relevant counterfactual outcome of participants had they not participated (and of nonparticipants had they participated) in order to mimic the comparison of same individuals with and without participation in the microcredit program.
In an attempt to mitigate potential bias, a growing body of the literature applies various methods to evaluate the impact of microcredit programs using different assumptions. However, few of these limited studies are free from criticism.6 For example, one series of studies has compared tenured participants to incoming participants who have applied for but not yet received loans from MFIs. The incoming participants are seen as a good comparison group because they are also self-selected into the program, presumably in the same way as tenured participants (see Barnes, Gaile, and Kibombo 2001; Dunn and Arbuckle 2002; Mosley 2001). Karlan (2001) and Alexander-Tedeschi and Karlan (2010) criticize this approach as flawed. They insist that tenured participants at the time of survey exclude ex-participants who have left the program. Hence, the difference between tenured participants and incoming participants not only reflects the impact of the microcredit program but also the difference in characteristics between the remaining participants and ex-participants, thus exaggerating the impact.
Pitt and Khandker (1998) focus on an exogenous eligibility criterion of MFIs in rural Bangladesh, where MFIs target households with less than half an acre of land. They use this discontinuity as an identification strategy and principally compare households just above and below this threshold. They assume that these two groups resemble each other except for exogenously determined eligibility for access to microcredit.7Morduch (1998) argues that this assumption is erroneous because such an eligibility criterion is often violated in practice. He proposes using a difference-in-difference (DID) approach, where the difference in eligible and ineligible households in program villages is compared with the same difference in nonprogram villages. This controls for unobservable fixed factors affecting “endogenous” eligibility and program placement. Chemin (2008), in contrast, proposes employing propensity score matching (PSM) because it does not rely on ambiguous discontinuity, and it can take into account selection on observable characteristics by comparing matched participants with nonparticipants who have no access to the program (such as those living in non-treated villages) and who would participate in the program if they had access.
To minimize estimation bias, we purposively collected data for same households in the Gresik District of Indonesia in 2007 and 2008. Data from 2007 are based on a period prior to the disbursement of BPR-YBS microcredit. Data from 2008 are based on the period one year after the disbursement of microcredit. Following Chemin (2008), we use PSM to account for selection on observables. Taking full advantage of the panel data, the DID method is also used to account for selection on time-invariant unobservables. As suggested by Heckman, Ichimura, and Todd (1997), a combination of PSM with DID is strongly expected to improve the accuracy of impact evaluation.
Using the PSM–DID method, the present paper investigates the impact of microcredit under BPR-YBS on the following: (1) household income, (2) profits and sales (revenues) of self-employed businesses, (3) savings and investment in assets such as durables and livestock, and (4) schooling and medical expenses as well as expenditure on female clothing. Expenditure on female clothing is included with the qualification that if women are more empowered through a microcredit program (as argued by, among others, Pitt and Khandker 1998; Pitt, Khandker, and Cartwright 2006), they might have greater bargaining power within the household, which in turn might lead to larger expenditures on items that only women can enjoy. Estimations are conducted separately for each outcome variable to identify the manner in which the positive impact of microfinance on household welfare, if any, could be realized. The impact of microfinance may be positive and significant for expenditure but not for income if obtained credit is used exclusively for expenditure. It might well be that the impact of microfinance is positive for investment but not for income if it takes time to reap returns on investments. Because there is no ex-ante presumption about the channel in which impact may be realized, we may leave it for an empirical question.
This paper makes two major contributions: (1) This study is one of the few attempts to rigorously assess the impact of microcredit in Indonesia. We believe that the dearth of academic evidence has hindered the understanding of appropriate microfinance design in Indonesia. (2) This study represents a novel application of the PSM–DID method to the analysis of microcredit. This approach could be used because data for both pre-treatment and post-treatment status were available, something still quite rare in the published microcredit literature.
The remaining part of this paper is structured as follows. Section II includes a brief introduction to basic issues of impact evaluation and an explanation of how PSM combined with DID functions to mitigate possible estimation bias. The program of BPR-YBS and study settings are explained in Section III. Data sources are introduced in Section IV along with descriptive statistics of sample households. Estimation results are then discussed in Section V. A summary of major empirical findings and conclusions are presented in Section VI.
A major purpose of this study is to estimate the mean impact of microcredit programs on households that actually participate in such programs. This is called the average treatment effect on the treated (ATT) in the evaluation literature, defined as:
where E(·) denotes an expectation operator, y1i is an outcome of interest of household i participating in microfinance, y0i is the outcome of the same household without participating in microfinance, and D is a treatment indicator equal to 1 if the household belongs to a treated group and 0 otherwise. The fundamental problem in estimating the above equation is that it is impossible to observe the outcome of participants had they not participated, (y0i|Di= 1). Therefore, a major challenge is to construct a suitable counterfactual from the pool of nonparticipants. As noted by Kono and Takahashi (2010), simply treating nonparticipants as the counterfactual and replacing (y0i|Di= 1) by (y0i|Di= 0) tends to result in serious bias represented by
The last term of the right-hand side of equation (2) indicates the magnitude of potential bias when E (y1i|Di= 1) −E (y0i|Di= 0) is simply treated as ATT.
In general, matching-based techniques create a missing counterfactual from the pool of nonparticipants comparable in a set of essential characteristics, x, to participants. A practical shortcoming of such a method is that if x is high-dimensional, and the number of characteristics in the match increases, it is difficult to find nonparticipants having exactly the same or sufficiently close x's as participants in all dimensions. However, Rosenbaum and Rubin (1983) show that matching on a single index that captures the propensity to participate conditional on x yields consistent estimates of the treatment effect in the same manner produced by matching on all x's. This is referred to as the PSM method. Let p(xi) denote the probability of participation given observable covariates x, i.e., Pr(Di= 1|xi) =p(xi).8 The validity of PSM rests on the following two assumptions.
The first is called “conditional independence.” That is, conditional on the probability of participation given observable covariates, an outcome of interest in the absence of treatment, y0i, and participation, Di, are independent such that (y0i?Di|p(xi)). This assumes that selection can be explained purely by observable characteristics. In other words, once all relevant observable characteristics arecontrolled, participation in the program is not correlated with the outcome without treatment.
The second is termed “common support.” That is, all treated households have a counterpart control group and households with the same x have a positive probability of being participants such that p(xi) < 1.
Satisfaction of “conditional independence” implies E (y0i|Di= 1, p(xi)) =E(y0i|Di= 0, p(xi)), and this effectively eliminates bias in equation (2) caused by the difference in observable characteristics between participants and nonparticipants. PSM entails the obvious disadvantage of a reduction in sample size because observations that are unmatched or outside common support are not used in the analysis. However, restricting the comparison to differences within carefully selected pairs might significantly improve the quality of impact evaluation. Moreover, estimating determinants of participation in microfinance is valuable in its own right in order to examine whether the microfinance scheme under study actually reaches the poorest of the poor.
Propensity scores are estimated with a probit model using pre-treatment observable characteristics as regressors, which is followed by creation of matched observations. It is well known that there are different matching algorithms, each with positive and negative attributes (Caliendo and Kopeinig 2008). Among available options, a caliper matching method without replacement is used in this research. This allows finding the counterfactual of participants from nonparticipants who lie within the predetermined tolerance level (caliper) and is closest in terms of propensity scores. The appropriate tolerance level is a priori undetermined (Smith and Todd 2005), but following the conventional practice, we set it at 0.01 in this research.
Although PSM is appropriate only if observable characteristics affect the selection process, there is a problem if unobservable characteristics affect participation and outcomes. In such a case, the DID method can mitigate the selection problem on unobservables to some degree. This provides a reason to combine PSM with DID.
Difference-in-difference yields a comparison of before–after estimates for participants and nonparticipants. Formally, DID in the regression form can be expressed as follows:
where yit is an outcome of interest of household i in year t, β's are parameters to be estimated, T is the time period (1 for post-treatment and 0 for the pre-treatment period), and e is an unobserved error term. In this specification, the parameter β2 captures the average impact of microcredit. Estimation bias clearly emerges if the error term is correlated with treatment status such that corr(eit, Di) ≠ 0. Yet, suppose that the error term e comprises a time-invariant component v and a meanzero time-varying component ε, that is, eit=vi+εit, and suppose further that the time-varying component is independent of participation (εit?Di) for all households i, and εit is not serially correlated (corr(εit, εit+1) = 0). Taking the first difference, the above equation can then be rewritten as
where Δ represents changes in corresponding variables over time. This equation clearly shows that the impact of time-invariant characteristics, vi, is effectively removed. Because Δεi is uncorrelated with Di by assumption, the estimator of β2 is unbiased. ATT then takes the following more general form:
Since the estimator of β2 is equivalent to [E(Δy1i|Di= 1) −E(Δy0i|Di= 0)], the last term of the right-hand side of equation (5) will represent estimation bias if E(Δy0i|Di= 1) ≠E(Δy0i|Di= 0). Therefore, the validity of DID rests on “parallel time drift,” where a change of outcome in the control group between post-treatment and pre-treatment periods is identical with such change in the treatment group when there is no treatment.
Note that under PSM–DID, the above assumption implies (Δy0i?Di|p(xi)), which is less restrictive than the “conditional independence” under standard PSM, (y0i?Di|p(xi)). This is because the effect of time-invariant unobservables is eliminated. If this “parallel time drift” assumption is satisfied, the first term of the right-hand side of equation (5) is equivalent to β2 in equation (4) and provides an unbiased estimate of ATT.
In sum, bias due to selection on observable characteristics is controlled by PSM, given (y0i?Di|p(xi)), and its combination with DID helps control for selection on time-invariant unobservable characteristics given (Δy0i?Di|p(xi)).
III. DESCRIPTION OF THE STUDY AREA AND PROGRAM
BPR-YBS started a microcredit program in 2003 in the Gresik District of East Java Province, Indonesia. This is one of seven branches in the country that provides a microcredit service under BPR-YBS. Among the seven branches operated by BPR-YBS in Indonesia, Gresik was chosen for this study because the present authors received information in 2007 that BPR-YBS planned to open a new branch in a new subdistrict within Gresik and sought new members living nearby. This was seen as a good opportunity to obtain data on pre-intervention and post-intervention periods, and to examine not only who participates in the program but also whether and to what extent microcredit has an impact, without due consideration of existing members. If there were existing members in areas under study, it would be reasonable to consider why these members participated earlier and what differences there might have been in impact between tenured members and new members. Identification of such differences, caused by different timing of decisions, is an interesting but formidable task, and is beyond the scope of the present study.
Gresik is north-west of Surabaya, the second largest city in Indonesia and the capital city of East Java Province. Road conditions are relatively favorable, so it takes approximately one hour to drive from Surabaya to Gresik. Due to this proximity to a large commercial area and such favorable road conditions, the manufacturing sector is relatively well developed in Gresik. In 2004, approximately 48% of gross domestic regional income was derived from manufacturing industries, followed by transportation and communication (19.9%) and agriculture (11.1%) (BPS Gresik 2006).
BPR-YBS adopted a microcredit model from the Association for Social Advancement (ASA) in Bangladesh, an NGO working in the field of poverty alleviation and empowerment of the poor, especially adult women. Following ASA, BPR-YBS aims to help the poor, especially women and their families, and targets female clients aged 18 years old and over.9 To attract poor households, collateral is not required for loan application. Once an application is accepted, the first loan size is required to be small and might range from Rp 0.5 million to Rp 1.5 million. These features are in sharp contrast to other commercial banks with microcredit operations in Indonesia. These banks usually require pledged collateral and allow clients to borrow up to Rp 50 million in the initial loan.10 This generally prevents the poor, who usually demand smaller loans without collateral, from using the services of such banks. In addition, BPR-YBS asks applicants to submit a simple application form indicating average household income, major income sources, the number of household members, and the purpose of loans. Based on information gathered, very rich households are excluded as customers.
While BPR-YBS does not explicitly monitor actual loan usage, it aims to smooth the running costs of microentrepreneurs rather than helping with start-up costs or in smoothing household consumption. Therefore, members of clients' households, either the client herself or other household members, are usually required to have some self-employed work prior to borrowing, even though this rule is not strictly enforced in practice.
The credit scheme under BPR-YBS involves individual lending without joint liability. However, to become BPR-YBS members, applicants must form or join a self-help group consisting of 10–30 women. Before borrowing, they must also attend weekly group meetings four times and make mandatory savings deposits. After four weeks, clients can receive loans. Weekly group meetings are held continuously after loan disbursement, and members must repay the loan and deposit mandatory savings weekly in these meetings. The length of repayment period is 50 weeks for all members and cannot be shortened. According to BPR-YBS officers, the collection of weekly repayment and savings in 50 weeks significantly reduces default risks in the absence of collateral. This is due to the following: (1) frequent meetings can form a habit of regular repayment, (2) members feel shame if they cannot properly repay in public at the group meeting, and (3) mandatory savings are like collateral because members are afraid that savings might be seized by BPR-YBS if there is default. Furthermore, if members are in default for any reason, they are no longer eligible for future loans. Therefore, as long as members have continuous credit needs, members make an effort to repay their current loan.
A. Sampling Design and Data Collection
Data used in the present study were collected by the present authors in Gresik in 2007 and 2008. As noted earlier, BPR-YBS expanded its geographical business area within Gresik in 2007. A presurvey was conducted in September 2007 to attain BPR-YBS collaboration and to determine a sampling strategy. The basic strategy was to collect pre-treatment and post-treatment conditions for: (1) participants in treated villages (hereafter participants or treatment group), (2) nonparticipants in the same treated villages (hereafter nonparticipants), and (3) nonparticipants in control villages where BPR-YBS did not provide any service during the observation periods (hereafter, control group).
Discussion with BPR-YBS officers revealed that at the time of the presurvey, general information on socioeconomic conditions and credit demand in ten villages in two subdistricts had already been collected, and BPR-YBS had decided to start operation in these areas. BPR-YBS officers indicated that they initially planned to use 100 customers in a pilot study and that actual loan disbursement for the 100 customers would start around the end of 2007 because the selection of 100 members would take time.
Based on that discussion, 100 participants chosen by BPR-YBS became the treatment group for this study. We also decided to select 100 nonparticipants randomly from the rest of population in the treated villages after the 100 participants had been determined. Selection criteria for control villages was that they be located in the same subdistricts as treatment villages and geographically close to the treatment villages, so that agro-climatic and social conditions would likely be similar. It was also important that villages where BPR-YBS would be willing to operate in the future be chosen to reduce estimation bias associated with program placement. Following the advice of BPR-YBS officers, three villages were selected for control villages satisfying the above criteria. 250 households were then randomly sampled from control villages and treated as the control group.
By November 2007, 100 households had signed up to become BPR-YBS customers but had not yet borrowed. Then, 100 nonparticipants living in the treated villages were randomly selected, and more detailed household surveys were conducted from December for: (1) 100 participants, (2) 100 nonparticipants, and (3) 250 subjects of the control group selected as above. The main objective of the 2007 survey was to obtain detailed baseline household information when all had not borrowed. The data included characteristics of household members, occupations, income, assets, and credit history. Immediately after the 2007 survey, 100 participants received loans from BPR-YBS.
One year after loans were disbursed to the treatment group, the 2008 survey was conducted to trace all households. For consistency, questionnaires were virtually the same as those used in 2007. Although it was desirable to maintain the sample size, 3 treatment households could not be traced in the follow-up survey due to outmigration. Of the remaining 97 participants, 5 households were found to have participated only in mandatory savings without taking out loans. Karlan (2001) and Alexander-Tedeschi (2008) note that excluding such dropouts from the credit scheme might potentially yield estimation bias if selection is not adequately adjusted for. Therefore, all 97 participants were defined as the treatment group in this study, with 5 households labeled as “dropouts.”
B. Descriptive Analysis
Table 1 shows basic household characteristics in 2007. Sample households are classified into three groups according to treatment status, and residential locations discussed above (participants or treatment group, nonparticipants, and control group). To focus on the characteristics of women who are eligible to participate in the microcredit, “eligible women” were defined as women over 18 years of age and either head of household or spouse, regardless of actual treatment status.
Table 1. Selected Household Characteristics in 2007
Participants in Treated Communities
Nonparticipants in Treated Communities
Other employment includes casual agricultural wage work and assistance for household nonfarm enterprise and farming without payment.
The average age of the eligible women was approximately 40 years for all groups. Average education was seven to eight years; this is less than the nine years required for lower-secondary graduation in the 6-3-3-4 educational system of Indonesia. It is notable that the average completed years of education for eligible women was highest for nonparticipants, followed by the control group; it was lowest for the treatment group. It may be that BPR-YBS microcredit attracts less educated women who have not had sufficient opportunities to obtain lucrative and stable employment in the labor market.
There is support for this conjecture in data related to occupational choice of eligible women. The table shows that such women are self-employed, regularly employed in public or private sectors, employed in other segments,11 or housewives. Approximately half of the treatment group were engaged in self-employed jobs; this percentage was well below 30% for nonparticipants and the control group. Nonparticipants and the control group were generally more likely to be engaged in regularly employed work in the public or private sectors.
The percentage of couples, defined as a still-married woman, was also lowest among participants. This might be due to the fact that women who are single having never married, or who are divorced or bereaved, have a greater demand for credit to expand self-employed businesses or to smooth consumption.
Characteristics of husbands, where eligible women were not single, were more or less similar across the three groups. The average age was approximately 43 years, and the average completed years of education was slightly greater than 8 years for all groups. Other household characteristics did not significantly differ, except for ownership of house and farmland. The average percentage of house ownership was approximately 94% for the treatment group, 93% among nonparticipants, and 86% for the control group. The average percentage of those who owned farmland was 33% for the control group, 27.1% for the treatment group, and 19% for nonparticipants.
These descriptive tables are suggestive, but determining factors of participation in BPR-YBS microcredit cannot be identified ceteris paribus. To examine this issue, we will perform regression analysis in the next section.
Before discussing the econometric framework, let us examine differential living standards and their dynamics across the three groups. Table 2 shows changes in per capita income, its composition, and poverty incidence between 2007 and 2008.12 Because there were several unusual observations, the top and bottom 1.5% of per capita income, changes in per capita income, and percentage changes in per capita income of households have been excluded from the analysis. Of the remaining 407 households, 89 households comprised the treatment group, 87 were nonparticipants, and the remainder were in the control group, as shown at the bottom of Table 2.
Table 2. Changes in Per Capita Income, Its Composition, and Poverty Incidence, 2007–8
Participants in Treated Communities
Nonparticipants in Treated Communities
Participants in Treated Communities
Nonparticipants in Treated Communities
Income per capita (Rp 1,000)
Composition of income (%):
Change in poverty status between 2007 and 2008 (%):
Number of observations
It is clear that the average per capita income of the treatment group was much higher than that of nonparticipants, even in 2007 when those participants had not yet started borrowing. It might be that better-off households voluntarily self-select into the program or that BPR-YBS tends to target better-off households within a village. The average per capita income of the treatment group was also higher than that of the control group. The fact that participants are wealthier than nonparticipants and those in the control group, even in the absence of credit, implies that BPR-YBS microcredit might not necessarily serve the poorer segment of society.
Income gaps between treatment and nonparticipant households as well as between treatment and control households further widened in 2008. Access to credit might improve living standards of the treatment group far above those of other groups.
Turning to income composition, a cursory glance at the table shows that employment is by far the most important source of income for all three groups, especially in 2007; approximately 70% of total household income was derived from employment in that year. However, this percentage dropped remarkably from 78% to 57% between 2007 and 2008 for the treatment group in favor of self-employed income. This suggests that dependency on self-employment greatly increased for participants during this period. Specifically, participant share of nonfarm self-employment income in total self-employment income significantly increased from 63% in 2007 to 74% in 2008.
The percentage of the poor, defined as households with less than half of the median per capita income of 407 restricted sample households,13 was 13.5% for participants. This was lower than that of nonparticipants or the control group in 2007. In 2008, the poverty incidence of participants was still lower than that of nonparticipants and the control group, even though gaps among the three groups slightly narrowed. According to the bottom part of Table 2, approximately 80% of participants never experienced poverty in 2007 or 2008, whereas only 61% of nonparticipants and 68% of those in the control group were never poor in these years. Together with observations of average per capita income, these results suggest that BPR-YBS microcredit does not necessarily reach the poorest of the poor. Rather, it seems that wealthier households are more likely to join the program.
V. ESTIMATION RESULTS
A. Participation in Microcredit Program
To determine who participates in BPR-YBS microcredit programs, a regression analysis is conducted using a probit model. The dependent variable is binary (1 if households join the program and 0 otherwise). There are three groups of independent variables. The first group includes: (1) eligible female characteristics such as age, education, and their squared terms; (2) a couple dummy equal to 1 if still married and 0 otherwise; (3) a set of occupation dummies including self-employment, government work, and private employment dummy (equal to 1 if the primary occupation of the eligible woman was the given occupation, and 0 otherwise); and (4) a birth dummy (equal to 1 if the potential client was born in the same community as the current community and 0 otherwise). The second group consists of household characteristics such as: (1) the number of dependents and working members defined as those aged between 15 and 65 years old and not enrolled in school at the time of the survey, (2) the average years of education of working members, (3) the share of male family members, and (4) the area of residential lots and farmland. The third set of independent variables includes village characteristics such as: (1) population density, and (2) a dummy for rural areas which took a value of 1 if the village was in a rural area and 0 otherwise. To avoid reverse causality, all variables were derived from the pre-treatment year 2007. Because the control group by definition could not participate, sample households were restricted to those in treatment villages.
The results of probit estimations are presented in Table 3.14 Model 1 is a benchmark equation including only eligible female characteristics as regressors; Model 2 adds the squared age and education terms to Model 1; Model 3 adds household characteristics to Model 2; and Model 4 adds village characteristics to Model 3. Qualitative implications are not significantly different across the four specifications. However, judged by a pseudo R2, Model 4 seems to have the highest explanatory power. Hence, the estimation result based on Model 4 is used in the interpretation.15
Table 3. Determinants of Participation in Microcredit Program
Note: 1. Absolute value of Z-statistics in parentheses.
2. Dependent variable =1 if participated, =0 otherwise.
***, **, and *
represent statistical significance at the 1%, 5%, and 10% level, respectively.
Holding other characteristics constant, eligible female age and its squared term individually did not have a significant impact on the decision to participate in a microcredit program. A joint significance test shows that the null hypothesis (that they are jointly not different from zero) could not be rejected at the 5% level. The coefficient of completed years of education of eligible women was positive and significant, whereas its squared term was negative and significant. This indicates an inverse-U-shaped relationship between education and probability of participation. Specifically, those women least educated and those women most educated tend not to receive BPR-YBS microcredit (conditional on other explanatory variables), whereas those with moderate educational levels tend to receive more.16 The couple dummy was negative and significant, implying that if a husband is active and generates sufficient income, demand for credit might become weaker.
Consistent with expectations, the self-employed business dummy was positive and significantly correlated with participation in the microcredit program. This might be partly because BPR-YBS generally targets those who already have some self-employed business and partly because those who run self-employed businesses are more likely to have greater credit demand for working capital and investment in business assets. It is interesting to observe that the government work dummy (which is 1 if the eligible woman works in the public sector) was also positive and significant. In Indonesia, it is common for public servants to have some side business to compensate for the relatively low salaries they make in the public sector. The positive coefficient of the government work dummy appears to be evidence of such side businesses.
For household characteristics, there were no statistically significant results for the number of dependents, the number of working members, or the share of male family members. The only exception was the average education of working members, which was positive and significant. This is probably because household members who are well endowed in terms of human capital help improve the productivity of self-employed jobs, which leads to greater demand for capital input. More importantly, neither area of residential lots nor area of farmland that could serve as collateral were significant determinants of participation in the microcredit program. This suggests that BPR-YBS credit actually does not screen out households who do not possess collateral of sufficient value. Other village characteristics, including population density and the rural dummy, were also not significantly correlated with the participation decision.
Overall, eligible female characteristics appear to be the most important determinants for joining BRP-YBS microcredit programs. Household and village characteristics, such as the number of household members and their gender composition, the ownership of a homestead and farmland, and the rural dummy, do not systematically affect whether or not a household may receive loans from BPR-YBS. The only exception is the average education of working members, which has a positive effect on participation.
B. Propensity Score Matching and Balancing Test
Using parameters obtained in Model 4, propensity scores (probability of participation) were computed for all households. The treatment group was matched with the control group that has the closest propensity score within a predetermined caliper (0.01). To impose common support conditions, observations in the treatment group with propensity scores higher than the maximum or lower than the minimum of the control group were dropped. Through this matching procedure, 85 pairs were successfully matched.
The distribution of propensity scores before and after matching is illustrated in Figure 1. The horizontal axis indicates the estimated propensity score, and the vertical axis indicates observed frequency with the graph being upside down for the control (untreated) group. The propensity score is more diverse before the match, but it is more concentrated and its distribution resembles between treatment and control groups after the match. We also perform a series of balancing tests on the differences in means based on t-statistics. These were calculated for each independent variable to investigate whether the matched control households had characteristics similar to the matched treatment households. If the difference between the matched treatment and control households was statistically insignificant, it could be safely claimed that there was no systematic difference between these two groups, at least in terms of observable characteristics. The results in Table 4 show that although several characteristics were statistically different between treatment and control households before matching, no variables were statistically different at the 1% level after matching. This, in turn, indicates that the matched pairs are sufficiently comparable in essential pre-treatment observable characteristics, which will enable more accurate estimates of the impact of microcredit programs.
Table 4. Results of Balancing Test
p > t
*** and **
represent statistical significance at the 1% and 5% level, respectively.
Having obtained matched pairs, ATT was estimated based on equation (4). Because there were five dropouts in the treatment group, a dropout dummy was constructed and added to equation (4). One critical limitation inherit in this analysis is that the length of time between the baseline and the follow-up surveys was too short, only one year. So, even if no impact were found, it cannot be strongly claimed that microcredit programs have no impact on outcomes, as this merely indicates that microcredit programs may have no impact after just one year (Karlan and Goldberg 2007). Because the time required to realize an impact might be different for different outcomes, it is better to test using several dependent variables. Still, care should be taken when interpretating the results.
Table 5 shows results of the average impact on the treated using PSM with DID. For comparison, results obtained through ordinary least squares (OLS) are presented.17 According to the OLS estimate, the increase in average per capita income during one year was higher for the treatment group by Rp 551,000 than for the control group. The corresponding estimate by PSM–DID indicates that the OLS estimate was biased upward, and the magnitude declines to Rp 441,000. Yet, neither OLS or PSM–DID results were statistically significant. Similar bias appears to arise for profits of self-employed business. However, average differences between treatment and control groups were again not statistically different from zero in both OLS and PSM–DID results.
Table 5. Average Impact of Microcredit Program
Outcome (Rp 10,000)
Ordinary Least Squares
Note: ATT = average treatment effect on the treated. PSM–DID = propensity score matching–difference-in-difference.
represents statistical significance at the 10% level.
The impact on per capita sales from self-employment business was underestimated by OLS.18 Although the magnitude of ATT is Rp 1.6 million using OLS, it increases to Rp 3.0 million and becomes statistically significant using PSM–DID. The same applies to per capita sales from nonfarm enterprises. According to the OLS estimate, the difference in growth of per capita nonfarm enterprise sales were, on average, statistically insignificant. However, the PSM–DID estimate indicated that the same difference was statistically significant, and that growth was larger for the treatment group by Rp 3.3 million than for the control group. In contrast, there was no significant difference in change in sales of farming/aquaculture between treatment and control groups.
Because neither profits of total self-employed business or nonfarm self-employed business were statistically different, as described above, the results indicate that microcredit contributes to expanding the scale of business in general and nonfarm business in particular, but this improvement does not result in increased profits within a year.19 This may be presumably because households can immediately increase the level of output through changing the level of input, but they cannot find the optimal input mix to raise profits within a short period of time.
Regarding the impact on asset values, there were no significant differences between treatment and control groups in savings, durables, or livestock using both OLS and PSM–DID estimates.20 Schooling expenditure was calculated in the following two ways: (1) schooling expenditure per actual attendant, and (2) expenditure per school-aged child who is between 6 and 22 years old. When the first definition was employed, both OLS and PSM–DID showed insignificant impact on schooling expenditure. When the second definition was employed, the OLS estimate showed a positive and significant effect on schooling expenditure. However, significance disappeared when PSM–DID was applied. The impact on medical expenditure per capita was also not statistically different from zero. The final outcome variable was the value of female clothing with the expectation that if women are more empowered through the microcredit program, they may have greater bargaining power within the household, and this will lead to larger expenditures on items only women can enjoy. Yet, our conjecture was not supported, as evidenced by the insignificant coefficient.
In sum, if the preferred estimation of the PSM–DID method is used, only sales of self-employed business show a positive and significant effect on the the treatment group. Given the statistical insignificance between treatment and control groups of the impact on total household income and profits of self-employed business, the results suggest that although microcredit programs might help to enlarge business size, they do not lead to an improvement of profits and, thereby, total household income within a year.
D. Heterogeneous Impact by Initial Poverty Status
Why does there seem to be little impact of microcredit programs on households?21 It might simply be that there is no impact of microcredit programs. However, another possibility is that observation intervals in this study were too short to realize the impact. In addition, impacts might be so heterogeneous that positive impacts cannot be observed on average. Indeed, Coleman (2006), in his study on village banks in Thailand, demonstrates that with a pooled sample, virtually no significant impact emerges. However, when the sample is divided into ordinary members and committee members of village banks who are relatively better-off, positive and significant impacts are found on various outcomes for the latter.
To explore the last possibility, the initial poor dummy, which takes the value 1 if the household is poor in 2007 and 0 otherwise, was added to equation (4) and placed in interaction with the dropout and treatment dummies. The modified specification can be expressed as follows:
where Drop is the dropout dummy, and P is the initial poor dummy explained above.22 The parameters of interest are β2 and β4. The former represents ATT for the nonpoor, and β2+β4 represents ATT for the poor. Alternatively, β4 represents the differential slope between the nonpoor and the poor. Therefore, if this parameter is statistically significant, it is evidence of heterogeneous impact from the microcredit program between the poor and the nonpoor.
The results in Table 6, however, reveal virtually no changes in impact on income and assets. Again, all coefficients for these outcome variables were not statistically different from zero. This indicates that participants in the microcredit program were not different from the control group in terms of changes in income and assets over time, regardless of their initial levels of wealth. The increase in sales of self-employed business was positive and significant for the nonpoor and significantly negative for the differential slope. The magnitude of the negative coefficient for the differential slope (Rp 5.4 million) outweighs the magnitude of the positive coefficient for the nonpoor (Rp 4.3 million). This implies that the net impact was negative if participants were poor. In other words, the benefit of enlarging the business size seen earlier was predominantly captured by wealthier households.
Table 6. Differential Impact of Microfinance Program by Initial Poverty Status
Outcome (Rp 10,000)
Differential Slope for the Poor
Note: ATT = average treatment effect on the treated.
represents statistical significance at the 5% level.
In contrast, the coefficients for both schooling expenditures per attendant and per school-aged child were positive and significant for the differential slope. This indicates that poor participants are more likely to increase their expenditures for schooling by a greater amount than their richer counterparts when they gain access to microcredit. This would reflect that whereas nonpoor households can provide sufficient education even in the absence of microcredit, poor households might find it difficult to do so without help of microcredit, due to binding credit constraints.
In contrast to the work of Coleman (2006), the insignificant impact of microcredit programs on various outcomes does not seem to be driven by the pool of observations, given that estimation results are mostly robust even when observations are decomposed into the poor and nonpoor. Microcredit programs under study appear to have no significant impact on household income, business profits, or asset accumulation within a year. The decomposition exercise does indicate that the impact of microcredit programs on expansion of business sales might not be captured by participant households as a whole but only by nonpoor households. By contrast, it was found that increases in child schooling expenditures due to microcredit is greater for the poor than the nonpoor. This might mean that there is hope that the vicious circle of poverty will be broken over the course of generations through investment in schooling. However, the lack of other impact on the poor shows that the microcredit program under study does not seem to immediately contribute to the alleviation of poverty in the short term (at least within one year). Perhaps more time is needed for the poor to learn by doing and thereby transform increased credit access into the expansion of business, increased profits, and increased household income.
Using panel data collected in 2007 and 2008, this paper examines whether a microfinance program operated by BPR-YBS in the Gresik District of Indonesia contributes to the reduction of poverty. The BPR-YBS scheme seems suitable to the poor in that, unlike most commercial banks in Indonesia, it does not require collateral and does offer small loans. From the descriptive analysis, however, we found that the average per capita income was higher and the poverty incidence was lower for participants even in the absence of credit. Probit analysis showed that characteristics of adult women were decisive determinants of participation in microcredit programs, and other household and village characteristics did not significantly affect a decision to participate. Importantly, areas of residential lots and farmland, which can be a proxy for the ability to put up collateral, had no impact on participation. These results together suggest that, although the collateral-free scheme might actually work, it is the relatively wealthier families that gain access to microcredit in reality.
Based on the parameters estimated by the probit model, propensity scores were calculated for all households and control households were matched with treatment households based on the propensity scores. Then, several outcome variables of the matched treatment households and control households were compared through the difference-in-difference method. The results showed that the impact on most outcomes, including household income and profits of self-employed business, was not statistically significant. Notable exceptions were sales of self-employed businesses in general and those of nonfarm enterprises in particular. On average, treatment households experienced a greater increase in volume of business sales than did of control households. This suggests that microcredit programs contribute to increased business size. Decomposition of the sample into the poor and nonpoor further revealed that such an enlargement of business occurred only for the nonpoor. In contrast, the poor benefited more from access to microcredit through increased investment in schooling for their children than the nonpoor.
Of course, there is great hope that the vicious circle of poverty will be broken over the course of generations through investment in schooling. However, given that the BPR-YBS microcredit program does not intensively target the poor, and given that poor participants do not benefit from access to microcredit to any great extent other than for investment in schooling, it seems reasonable to conclude that such a BPR-YBS microcredit program, although it introduces a unique, collateral-free, small-size scheme in the context of Indonesia, does not have an immediate impact on poverty alleviation, at least within one year.
We must note, however, that the BPR-YBS attempt has not been completely unsuccessful. In fact, small-scale loans without a collateral requirement from BPR-YBS have been shown to greatly increase overall credit access in survey regions (Tsukada, Higashikata, and Takahashi 2010). Households with a self-employed business were also found to prefer formal credit like that offered by BPR-YBS as a stable financial source rather than informal sources like moneylenders. Therefore, BPR-YBS might fill a niche for loan demand in the microfinance industry in Indonesia. There is also the possibility that several significant changes, including the composition of participants and benefit of credit, might emerge if the observation period is extended. Whether or not BPR-YBS can deliver greater benefits to participants and whether or not BPR-YBS will realize its full promise on a sustainable basis are major research agendas that should be explored in future studies.
One US dollar is equivalent to Rp 9,419 as of December 2007.
The number of clients is reported to be more than 30 million; this is the largest client base in the developing world. The repayment rate is as high as 98%, and more than 96% of BRI branches are profitable.
See Hamada (2010) for an overview of the microcredit industry and BPR's role in Indonesia.
Strictly speaking, Pitt and Khandker do not use observations just above and below the threshold, although the study can be considered an example of “regression discontinuity design” (Morduch 1998; Roodman and Morduch 2009). They use an intricate econometric technique called weighted exogenous sampling maximum likelihood-limited information maximum likelihood-fixed effects to derive the marginal impact.
In practice, one of the most important criteria for selecting covariates is that all factors explaining participation and outcomes be included in x (Smith and Todd 2005; Caliendo and Kopeinig 2008). The argument of p(·) is not necessarily a simple linear function of the covariates x and can include, for example, quadratics and interaction terms. Furthermore, the propensity score p(xi) can be estimated using fully nonparametric methods (Wooldridge 2002). Dehejia and Wahba (2002) propose including interaction or higher-order terms of x when a simple linear function fails to pass the balancing test. Following Chemin (2008), the present study included application of a simple linear function of covariates x with several quadratic terms (such as age and education) that are likely to explain participation, outcome, or both, and help pass the balancing test.
Marital status is not material as a criterion of membership. Therefore, members in the sample include the married, the divorced, and the widowed.
In Indonesia, microcredit is defined as any credit less than Rp 50 million.
Other employment includes casual agricultural wage work and assistance for household enterprise and farming without payment.
Because per capita income is a nominal value, the increase in income between 2007 and 2008 reflects inflation, other time trends, and the impact of microcredit. The annual inflation rate in 2008, measured by the consumer price index (CPI), was 11.1%. To control for changes in income and other variables due to inflation, all values were converted into the real term using CPI as a deflator (2007 base year) in the subsequent DID estimations.
The poverty line set by the central statistics office, Badan Pusat Statistik (BPS), was not used because the BPS poverty line is based on total expenditure (which is not in the data), and also because the 2008 poverty line has not yet been reported.
Three observations in nonparticipant households did not have any eligible participant who was a woman 18 years of age or older and either head of household or spouse. Therefore, the number of observations was reduced to 194.
We tried to include a squared term for working members' average education level as an additional regressor because the education level of eligible women had a nonlinear effect (as seen later). However, the squared term had no significant impact on participation, and because inclusion of the squared term failed to pass the balancing test, it was not used in the present study.
An inverse-U relationship between education and probability of participation might explain why there is a large change in magnitude of the coefficient for the “government work” variable between Models 1 and 2. If (as is likely the case) the average education level of those engaged in government work is high, omission of its quadratic term will lead to a large negative bias for the coefficient of “government work.”
For OLS, 407 restricted samples as defined in the previous section were used.
Underestimation of impact by OLS compared with PSM–DID is surprising. Further examination of the data shows that although the average increase in the sales of self-employed business for untreated households was positive, it becomes negative if observations are restricted to matched untreated households. This seems to be a major reason for underestimation of impact by OLS.
ATT was also estimated using total profits as well as total sales of self-employed business instead of their per capita values. Results indicate that microfinance has no significant impact on total profits, but it does have a positive and significant impact on total sales. This is consistent with findings in the main text.
The impact on business assets cannot be estimated because only four observations changed their business asset values over time.
The matched control group of BPR-YBS may potentially borrow credit from other sources, and this can reduce the impact of BPR-YBS microcredit due to contamination. However, a detailed examination of the data reveals that although many in the control group actually borrowed credit from other sources in 2007 and 2008, the average growth of their borrowing amount was negative between the periods. Because the DID method was used in the present study, contamination is probably not a major reason for the small impact of the BPR-YBS microcredit program.
It can be argued that the initial poor dummy should be included in equation (6) to capture the differential time drift between the poor and nonpoor. However, because there were few variations among the dropouts, the initial poor dummy was perfectly linearly related to other variables. Therefore, the initial poor dummy was dropped from the equation, and only the interaction term was used with other dummies.