metadata: authors: 0: author: Boonperm, Jirawan
1: author: Haughton,Jonathan
2: author: Khandker,Shahidur R.
count: Thailand
docna: 0: docna: Does the village fund matter in Thailand ?
docty: Policy Research Working Paper
theme: Micro, Small and Medium Enterprise support
majtheme: Financial and private sector development
subtopic: Conflict and Fragile States,Urban Housing and Land Settlements,City to City Alliances,Rural Microfinance and SMEs,National Urban Development Policies & Strategies,Regional Urban Development,Urban Economics,Urban Governance and Management,Urban Housing,Microfinance,Food Security,Municipal Management and Reform,Urban Economic Development,Urban Communities
teratopic: Macroeconomics and Economic Growth,Poverty Reduction,Finance and Financial Sector Development
abstracts: cdata!: This paper evaluates the impact of the
            Thailand Village and Urban Revolving Fund on household
            expenditure, income, and assets. The revolving fund was
            launched in 2001 when the Government of Thailand promised to
            provide a million baht (about $22,500) to every village and
            urban community in Thailand as working capital for
            locally-run rotating credit associations. The money  about
            $2 billion in total  was quickly disbursed to locally-run
            committees in almost all of Thailands 74,000 villages and
            more than 4,500 urban (including military) communities. By
            May 2005, the committees had lent a total of about $8
            billion, with an average loan of $466. Using data from the
            Thailand Socioeconomic Surveys of 2002 and 2004, each of
            which surveys almost 35,000 households, the authors find
            that the borrowers were disproportionately poor and
            agricultural. A propensity score matching model finds that
            Fund borrowing in 2004 was associated with, on average, 1.9
            percent more income, 3.3 percent more expenditure, and about
            5 percent more ownership of durable goods. These results are
            broadly consistent with the results from instrumental
            variables models (where the identifying instrument was the
            inverse of village size), which however show a smaller
            (marginal) effect. Households that borrowed both from the
            revolving fund and from the Bank of Agriculture and
            Agricultural Cooperatives gained substantially more in terms
            of higher income than those who borrowed from either one or
            the other or from neither.
geo_reg_key: 517191,517198
repnme: repnme: Does the village fund matter in Thailand ?
display_title: Does the village fund matter in Thailand
listing_relative_url: /research/2009/07/10846344/village-fund-matter-thailand
topicv3: Agriculture and Food Security m1326205 435,Microfinance m1327227 367,Urban Development m1327371 699,Land and Housing m1327648 817,Military m1505651 3036
publishtoextweb_dt: 2010-07-01T00:00:00Z
historic_topic: Macroeconomics and Economic Growth,Poverty Reduction,Finance and Financial Sector Development
no_of_pages: 36
author_keys: 0: author_key: 165913
1: author_key: 92956
model_extractions: WPS5011 Policy Research Working Paper 5011 Does the Village Fund Matter in Thailand?

_Jirawan Boonperm Jonathan Haughton Shahidur R. Khandker_ The World Bank Development Research Group Sustainable Rural and Urban Development Team July 2009
Policy Research Working Paper 5011

# **Abstract**

This paper evaluates the impact of the Thailand Village and Urban Revolving Fund on household expenditure, income, and assets. The revolving fund was launched in 2001 when the Government of Thailand promised to provide a million baht (about $22,500) to every village and urban community in Thailand as working capital for locally-run rotating credit associations. The money —about $2 billion in total—was quickly disbursed to locally-run committees in almost all of Thailand’s 74,000 villages and more than 4,500 urban (including military) communities. By May 2005, the committees had lent a total of about $8 billion, with an average loan of $466. Using data from the Thailand Socioeconomic Surveys of 2002 and 2004, each of which surveys almost 35,000 households, the authors find that the borrowers were disproportionately poor and agricultural. A propensity score matching model finds that Fund borrowing in 2004 was associated with, on average, 1.9 percent more income, 3.3 percent more expenditure, and about 5 percent more ownership of durable goods. These results are broadly consistent with the results from instrumental variables models (where the identifying instrument was the inverse of village size), which however show a smaller (marginal) effect. Households that borrowed both from the revolving fund and from the Bank of Agriculture and Agricultural Cooperatives gained substantially more in terms of higher income than those who borrowed from either one or the other or from neither.

This paper—a product of the Sustainable Rural and Urban Development Team, Development Research Group—is part of a larger effort in the department to understand the cost-effectiveness of rural financial institutions. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org. The author may be contacted at skhandker@ worldbank.org.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
# **Does the Village Fund Matter in Thailand?**

**Jirawan Boonperm** National Statistics Office of Thailand, Bangkok

## **Jonathan Haughton**

Suffolk University, Boston

## **Shahidur R. Khandker**

World Bank, Washington DC JEL codes: O16 G21 I38 Note: The authors listed above are in alphabetical order. They would like to thank Chalermkwun Chiemprachanarakorn and her colleagues at the Thai National Statistics Office for helping us work with the Thailand Socioeconomic Survey data, Sheila Buenafe for excellent research assistance and Xiaofei Xu for research support. We are deeply indebted to Kaspar Richter, who was instrumental in adding a special module on the Thailand Village Fund to the 2004 Socioeconomic Survey and arranging for a panel component for that survey. We benefited from comments received from Dean Karlan and Darlene Chisholm, and from participants at a seminar at Suffolk University at a presentation at NEUDC 2007. The views expressed in this paper are those of the authors, and not necessarily of the institutions with which they are affiliated.
# **1. Introduction**

In 2001, the government of Thailand launched the Thailand Village and Urban Revolving Fund (VRF) program, which aimed to provide a million baht (about $22,500) to every village and urban community in Thailand as working capital for locally-run rotating credit associations.<sup>1</sup> Thailand has almost 74,000 villages and over 4,500 urban (including military) communities, so the total injection of capital into the economy envisaged by the “million baht fund” amounted to 78 billion baht, equivalent to about $1.75 billion, making it the most ambitious of the estimated 120,000 microfinance initiatives anywhere in the world.2 The program was put into place rapidly. By the end of May 2005 the VRF committees had lent a total of 259 billion baht ($8.3 billion at the July 2007 exchange rate of Baht 31.23/$) to 17.8 million borrowers (some of whom borrowed more than once). This represents an average loan of $466. The total repayment of principal amounted to 168 billion baht, leaving outstanding principal of 91 billion baht.

In this paper we ask a narrowly focused question: Has the VRF had an impact on household incomes, spending, and asset accumulation, and, if so, how large are these effects? An answer to this question is necessary, but not sufficient, to help the Government of Thailand determine whether the program should be expanded or revised, and to help governments of other countries determine whether they should introduce or expand similar microcredit schemes. In order fully to address these policy issues, one would also need information on the costs of the program. A complete cost-benefit analysis of the Thailand Village Fund would be highly desirable, but goes beyond the scope of this paper.

The VRF represents a policy experiment on a grand scale, but it is not the only major source of household credit, even in rural areas. The Bank for Agriculture and Agricultural Cooperatives (BAAC) has an extensive network of rural lending. So it is appropriate to ask what additional role the VRF has played, an issue that we also address in this paper.

We summarize the relevant details of the VRF program in section 2, set out our general approach in section 3, describe the data employed in the impact evaluation in section 4, and in the subsequent sections explain the methodology and report the results of the impact evaluation using propensity score matching (section 5), instrumental variables (section 6), and panel data methods (section 7). The paper ends with a short set of conclusions in section 8.

> 1 The average exchange rate during 2001 was Bht44.51/$, which implies that a million baht are equivalent to $22,468. The exchange rate as of mid-July 2007 was Bht31.23/$, which would value a million baht at $32,020; this is the exchange rate that we use throughout the rest of the paper.

> 2 Estimated number of microfinance initiatives is from Kaboski and Townsend (2009), p.10.

_Village Fund, draft of June 29, 2009_ _Page 2 of 34_
# **2. The Thailand Village Revolving Fund**

The Thailand Village Revolving Fund became operational very rapidly. Inaugurated in 2001, Village and Urban Community Fund Committees (henceforth “Village Fund Committees”) had been formed in 92% of the villages and urban communities in Thailand by 2002, and much of the money had been disbursed. By May 2005, 99.1% of all villages had a Village Fund in operation and 77.5 billion baht, representing 98.3% of the originally scheduled amount, had been distributed to Village Fund Committees (Arevart 2005).

Although the initial working capital came from the central government, the Village Funds are locally run, and have some discretion in setting interest rates, maximum loan amounts, and the terms of loans; some require, or at least encourage, savings deposits as a condition for borrowing. The Village Fund Committees process loan applications; households borrow and repay with interest; and the money is lent out again. The Village Fund Committees do not handle money directly; this is done by a number of intermediaries, of which the most important are the Government Savings Bank (GSB), which operates mostly in urban areas, and the Bank for Agriculture and Agricultural Cooperatives (BAAC), which operates only in rural areas and semiurban communities.

There are five steps that must be taken in order for a Village Fund to become operational:

- (a).   The village first sets up a local committee to run the fund and to determine the lending criteria (interest rate, loan duration, maximum loan size, and objectives).

- (b)   The properly-established committee then opens an account at the BAAC (which has about 700 branches) or another "facilitator", and the government deposits a million baht into the account.

- (c)   The local Fund committee sifts through loan applications and determines who may borrow and under what conditions (interest rate, duration, etc.).

- (d)   The borrowers go to the BAAC (or other facilitator) to get access to the loans.  Each borrower must open an account – the minimum balance, if it is at the BAAC, is 100 baht – to which their loan is transferred.

- (e)   The borrower repays the loan with interest.  This requires him or her to visit a BAAC branch (or that of another facilitator); the borrower typically deposits the repayment directly into the village fund account. The BAAC provides a regular listing of transactions to each Village Fund.

A number of rules govern the establishment and operating procedures of the committee: three quarters of the adults in the village must be present at the meeting where it is established; the committee should have about 15 members, half of them women; while there is some discretion about the amount lent per loan, it should not generally exceed 20,000 baht and should never exceed 50,000 baht; the loans must charge a positive interest rate; and it is recommended that loans have at least two guarantors.

The government rates Village Funds on a variety of efficiency and “social” criteria; in any given year, those that are rated AAA are provided with a “bonus” of a further Bht100,000 to add to their working capital.

_Village Fund, draft of June 29, 2009_ _Page 3 of 34_
In addition, Village Funds can borrow an additional million baht (or sometimes just half a million baht, see below) from the BAAC or other facilitator. The size of this additional loan - i.e. half a million, or a million baht - is determined by the BAAC using its own (banker's) criteria. Only Village Funds that are ranked 1<sup>st</sup> class or 2<sup>nd</sup> class by BAAC may borrow a million baht; the others (3<sup>rd</sup> class) may only borrow half a million baht. The BAAC says that about 1% of these loans are overdue. The BAAC thus rates the managerial efficiency and potential of VRF Associations and may be intending gradually to withdraw from micro-lending by giving these village funds a space for competition to run village banks. The BAAC recognizes that Village Fund Committees generally have an informational advantage in determining who is a good candidate for a loan.<sup>3</sup> Some of the more dynamic Village Funds are trying to become rural banks, which would potentially lead to an efficiency gain in that it would allow money to move from one village to another.

# **3. Measuring the Impact of the Village Revolving Fund**

The injection of loanable funds due to the VRF was substantial, averaging 2.7% of annual income, or 7.1% of income for the 38% of households who borrowed. Because a million baht was available for every village, regardless of size, the importance of the VRF declined with village size: in the smallest tenth of villages, VRF loans represented 7.9% of income, but just 1.1% of income in the largest decile of villages (Table 1). What impact might one expect from such a sizeable one-time infusion of cash?

It is not self-evident that an injection of credit into a rural economy will have a measurable impact, or a positive impact. If financial markets operate well – information is cheap and readily available, there are no policy distortions – then households should already have access to as much credit as they can productively use, and they would mainly substitute VRF credit for other sources of credit. So for the VRF to have an impact on output, it must be predicated on the existence of market imperfections. As a general proposition, this is not unreasonable, as credit markets have well-known informational asymmetries that in turn can lead to the inefficient allocation of credit, excessive loan default, monopoly profits for well-informed lenders, and even credit market collapse (Bardhan and Udry 1999, p.91). The important point is that it cannot be assumed, a priori, that the VRF will necessarily have a major impact on household welfare.

According to the Socio-Economic Survey undertaken in 2004, 24% of respondent households said that they did not borrow from the VRF because they had no need for credit, and a further 25% said that they did not borrow from the VRF because they did not want to take on more debt. We have assumed that in the absence of general equilibrium effects, the introduction of the VRF credit cannot be expected to have an

> 3 This process, however, could potentially squeeze out some existing borrowers who may have less access to BAAC loans, and yet not be able to get VRF loans for one reason or another.  Moreover, some VRFs may be inefficient for the following reasons: (i) lending to unqualified borrowers; (ii) favoring committee members; (iii) extending loans that  are larger than the limit (e.g. 50,000 baht); (iv) not insisting on repayment; (v) charging a lower interest rate; and (vi) landing for longer-than-allowed periods.

_Village Fund, draft of June 29, 2009_ _Page 4 of 34_
impact on the incomes or spending patterns of these households; however, this is not an innocuous assumption, because the very availability of easier credit may reduce the incentive for precautionary (“buffer stock”) savings, and allow even non-borrowers to spend more than they otherwise would have.

Of those who did borrow, some may not have been credit-constrained, meaning that they had access to as much credit as they wanted, given the available price. They would then only have taken on VRF loans because they were cheaper. In part this would produce an income effect – substituting cheap for expensive credit – but the lower price of credit would also provide an incentive to borrow more overall. The effect could be large; one in six VRF borrowers said that they borrowed from another source to repay the VRF loan, and the average annual interest rate paid on those sources was 46.0%; given an average VRF interest rate of 6.0%, this represents a gain of 40%; given the mean loan size of 16,183 baht, the interest saving would be equivalent to 4.9% of an average borrowing household’s annual income. While this probably an upper bound on the cost savings from VRF borrowing, it is enough to allow non-interest consumption for borrowers to rise by at least 6.1%, with no change in household income.

Other VRF borrowers may have been credit-constrained, in the sense that they already wanted to borrow more at the available price of credit. Presumably existing lenders were reluctant to lend more due to prudential concerns, which in turn may have been justified, or may have resulted from asymmetric information. It is entirely possible that the village-level VRF would, in many cases, have better knowledge about the ability of village households to service loans than most outside lenders, and thus improve the efficiency with which credit is allocated.

We do not have direct evidence on whether VRF loans substituted for other credit, or supplemented other borrowing. Kaboski and Townsend (2009), based on a rural sample of 800 households, find evidence that in 2003, households took on VRF loans without reducing their other borrowing. This sits well with the view that many households are credit-constrained, but of course is not inconsistent with the case of nonconstrained households responding to lower borrowing costs.

Much microlending is seen as desirable because it allows households to invest more, and so raise their earnings, and certainly the VRF was originally viewed as a vehicle for promoting the development of non-farm enterprise. In this case the impact goes from loan to more investment to more income to more consumption. On the other hand, many households use credit for consumption purposes – to smooth consumer spending over the course of a year, or make a lumpy purchases (including durable goods), or increase consumer spending now relative to in the future. In this case one would observe an increase in consumer spending without a corresponding rise in income. Given that households are heterogeneous, and only some would borrow from the VRF for productive purposes, our presumption is that the VRF will have a stronger impact on consumption spending than on income.

Whether VRF loans were used for investment or for consumer spending, the effect is likely to be complicated by the fact that a number of credit schemes are already in place. In rural areas, the most _Village Fund, draft of June 29, 2009_ _Page 5 of 34_
important is the Bank for Agriculture and Agricultural Cooperatives (BAAC), which practices individual as well as group-based lending (mainly to support farming), mobilizes savings as part of financial intermediation, and is widely considered to be a successful rural finance institution (Yaron 1992, Fitchett 1999). Therefore it is legitimate to wonder whether the VRF has an added value to rural households that the BAAC could not provide – are they substitutes or complements? In other words, the relative effectiveness of both programs is an issue worth examining from the policy point of view, an issue to which we return in section 5.

In short, our main task is to measure the impact of the VRF program on three outcome variables of interest:

- **Expenditure per capita.** The measure of expenditure available is based on the Socioeconomic Surveys of 2002 and 2004, and includes 56 categories of expenditure (and home production), including the rental value of housing, but does not include the rental value of the household’s durable goods or vehicles (for lack of data).

- **Income per capita.** This measure includes 24 categories of income, and includes the rental value of housing (but not of durable goods).

- A number of measures of **household assets** , including whether the household has a washing machine, a VCR, or a motorized vehicle.  The SES-2004 did not collect information on the total value of household assets.

But now we are faced with a methodological problem: VRF borrowers do not represent a random sample of the households (or adults) surveyed in the Socioeconomic Survey of 2004 – among other things, they are poorer and more rural.

To get around the problem of non-random assignment, we are obliged to turn to a number of econometric techniques. These include propensity score matching (section 5) and instrumental variables (section 6), using data from the Thailand Socioeconomic Surveys of 2002 and 2004. These surveys also included a panel of rural households, which allows us to estimate the impact of the VRF using double differences, and instrumental variables with household fixed effects (section 7). But before discussing the impact evaluation techniques and results, some additional description of the data is in order.

# **4. The Data**

The data for the impact evaluation come from the Thailand Socioeconomic Surveys of 2002 and 2004. The 2004 survey interviewed 34,843 households (covering 116,444 people) throughout the country drawn from 2,044 municipal “blocks” and 1,596 villages in 808 districts. The data were collected in four rounds, spread throughout the year. The survey collected a wide variety of socio-economic data, including relatively detailed information on household income and expenditure. It used stratified random sampling with clustering; all the _Village Fund, draft of June 29, 2009_ _Page 6 of 34_
descriptive results presented in this paper apply the appropriate weights (unless otherwise indicated). The 2002 survey used substantially the same questionnaire and covered 34,785 households.

An interesting feature of these two surveys is that they include a panel of 5,755 rural households. An effort was made in 2004 to re-survey all 6,309 households that had been surveyed in rural areas in rounds 2 and 3 of the 2002 socioeconomic survey. This represents an annual attrition rate of 4.5%, which is relatively low. A comparison between panel households and those who dropped out of the panel found no appreciable differences in the relevant variables (in 2002), allaying concerns about attrition bias.

The summary statistics in Table 2 come from a special module that was included in the 2004 socioeconomic survey and that asked all adult members of households about their experience with the VRF. By 2004, a sixth of all adults had borrowed at least once from the VF, with higher proportions of borrowers among the poor (defined as those in the poorest quintile, as measured by expenditure per capita) and among those in rural areas; in this respect, VRF lending differs sharply from the older “village bank” programs in Northeast Thailand analyzed by Coleman (2002), where the bulk of the loans, and gains, accrued to the wealthier villagers. Adults in 38 percent of households had borrowed from the VRF by 2004.

Of those adults who did _not_ borrow, less than one percent had been refused a VRF loan, although a further 4% thought that they would be turned down. On the other hand, over a quarter of non-borrowing adults said they had no need to borrow, and almost a third said that they did not want to go into debt. Poor households were less likely to indicate that they did not need to borrow, but more likely to be fearful to going into debt.

The average amount borrowed in the most recent VRF loan was 16,183 baht (about $518), and this was only slightly less than the amount requested on average. The mean interest rate charged on VRF loans was 6.0 percent per year, but there was considerable variation, as Figure 1 shows: substantial numbers of Village Funds charged annual interest rates of 5, 3, or 12 percent. The interest rate paid by poor, or rural, borrowers was essentially the same, or perhaps slightly lower, than that paid by other adults.

Although the rhetoric surrounding the Village Revolving Fund program emphasized the importance of providing finance for processing and packaging, over half of all VRF borrowers said that they planned to use the money for relatively traditional agricultural purposes. This effect was even more marked among poor and rural borrowers. Borrowing is fungible, so this does not necessarily imply that spending on agricultural activities actually rose as a result of the implementation of the Village Fund program, but there is a dissonance between the reported uses of the borrowed funds and the original aspirations for the Fund.

_Village Fund, draft of June 29, 2009_ _Page 7 of 34_
<!-- Start of picture text --> 50<br>40<br>30<br>20<br>10<br>0<br>1 2 3 4 5 6 7 8 9 10 11 12 13 14 15<br>Interest rate for VRF borrowers (% p.a.)<br>% of total cases<br><!-- End of picture text --> Figure1. Interest Rates Charged by Village Funds, 2004 Source: Thailand Socio-Economic Survey 2004 Eight percent of VRF borrowers reported that they were overdue on repayments, and the proportions were similar for poor, and for rural, households. However, a sixth of those who obtained VRF credit in turn borrowed elsewhere in order to repay their VRF loan. The interest rates charged by those alternative sources of credit were high, averaging 46 percent (on an annualized basis).

Despite the challenges that some faced in repaying the VRF loans, seven out of ten borrowers said that their economic situation had “improved” as a result of the program and just 2 percent said that it had worsened. However, less than a third of borrowers said that the VRF system should be left unchanged; substantial numbers wanted the loan amounts to be larger (34% of respondents), longer (34%), cheaper (37%), or to be focused more on the poor (25%).

In 2004, women were slightly less likely than men to have borrowed from the Village Fund: 15.5% of adult women borrowed from the fund, compared to the overall average of 16.6%. Women asked for, and received, slightly smaller loans; paid a slightly higher interest rate; and were less likely to borrow to buy agricultural inputs or equipment. However, in most other respects, female borrowers are indistinguishable from male borrowers, as may be seen by comparing the first and last columns of numbers in Table 2.

A 2005 survey undertaken in the northeast of Thailand by the Thailand Development Research Institute (TDRI) found that about 40% of households had borrowed from the VRF, and among those who borrowed, slightly over 90% said they were satisfied with the process. There is, however, anecdotal evidence that in some cases the injection of credit has led villagers to borrow too much, leading to difficulties when the _Village Fund, draft of June 29, 2009_ _Page 8 of 34_
funds had to be repaid (Laohong 2006, Gearing 2001). There have also been reports of corruption in the administration of the VRF in some scores of villages.

The most rigorous study to date of the impact of the VRF uses data from the 2003 and earlier rounds of a panel of 960 households that Robert Townsend and his colleagues have been following for a number of years in four provinces of Thailand; 800 households were followed throughout 1997-2003, and this is the sample used in the study by Kaboski and Townsend (2009). Although the sample size is relatively small, the survey is rich in detail on household financial assets and transactions. Their most striking finding is that the proportion of household credit coming from “formal” sources (including the VRF) jumped from 37% in 2001 to 69% in 2002, and was accompanied by little reduction in the use of other credit; in other words, at least as of 2003, VRF credit supplemented rather than replaced existing sources of credit.

Although the VRF is widely used, and reported levels of satisfaction with it are high, this is no guarantee that it has had a measurable impact on the outcome variables of interest. Some critics have argued that many VRF borrowers view the money more as a grant than a loan, in which case it might be expected to lead to a one-time increase in per capita expenditure and the value of household durables, but not raise income. Defenders argue that the VRF has had an effect on productivity, raising income and, via higher income, boosting expenditures. Yet others argue that the main effect of the VRF has been to substitute for other sources of credit, with very little net impact on real output, spending, or welfare. To determine the truth in these arguments, a formal impact evaluation is required.

# **5. Propensity Score Matching**

Our first approach to measuring the impact of the VRF is by creating a quasi-experimental design that matches VRF borrowers with “otherwise identical” non-borrowers, and quantifies any difference in outcome variables between these two groups. Formally, let

- _Xi_ be a vector of pre-treatment covariates (such as age of head of household, location of household, and so on),

- _Yi0_ be the observed value of the outcome variable (such as expenditure) in the absence of the treatment,

- _Yi1_ be the observed value of the outcome variable for household _i_ if it has been treated (i.e. it has borrowed from the VRF), and

_Ti_ be the treatment (equal to 1 if the household is treated, to 0 otherwise).

We want to measure τ _i ≡ Yi1-Yi0,_ but this is impossible, because an individual is either in the treatment group (so be observe _Yi1)_ or the comparison group (so we observe _Yi0_ ), but never in both. If we are willing to assume that households are “assigned” randomly to the treatment group, once we have conditioned on the covariates, then by a proposition first established by Rubin (1977), the average treatment effect (τ|T=1) is

_Village Fund, draft of June 29, 2009_ _Page 9 of 34_
identified and is equal to τ|T=1,X averaged over the distribution of X|Ti=1. In other words, we can measure the average impact of the VRF by taking each borrower, finding an identical non-borrower (conditioned on the _X_ covariates), computing the difference in the outcome variable of interest, and taking its mean.

This procedure would only be straightforward if there were just a few covariates; in practice the problem is more tractable if we can create a summary measure of similarity in the form of a propensity score. Let p( _Xi_ ) be the probability that unit _i_ be assigned to the treatment group, and define _p_ ( _X i_ ) ≡ Pr( _Ti_ = 1 | _X i_ ) = _E_ ( _Ti_ | _X i_ ). (1)

In practice, this probability – the propensity score – could be estimated using a logit or probit equation. Rosenbaum and Rubin (1983) show that conditional independence extends to the propensity score, so that treatment cases may be matched with comparison cases using just the propensity score. Furthermore, the average treatment effect may be obtained by computing the expected value of the difference in the outcome variable between each treated household and the perfectly matched comparison household (as matched using the propensity score). Perfect matching is not possible in reality, so in practice one needs to compute where _Yi_ is the observed outcome for the _i_ th individual who is treated and _Ji_ is the set of comparators for _i_ . The comparators may be chosen with replacement – the approach we take – in which case the bias is lower but the standard error higher than without replacement. We use single nearest neighbor matching, whereby one chooses the closest comparator, although other approaches are possible (Abadie et al. 2001); Dehejia and Wahba (2002) argue that the choice of matching mechanism is not as crucial as the proper estimation of the propensity scores.

Broadly following an algorithm outlined by Dehejia and Wahba (2002), we first estimated propensity scores by applying a probit model to a limited number of covariates. We then sorted the observations by propensity score and divided them into strata sufficiently fine to ensure that there was no statistically significant difference in propensity scores between treated and non-treated households within each stratum. We confined this comparison to the area of “common support” – where the propensity scores of the treated and untreated overlap – and typically needed between 15 and 21 strata. We then checked for the “balancing property,” which means that within each stratum we tested (using a 1% significance level) whether there was a difference in the covariates between the treated and non-treated group. Our initial propensity score models were not well balanced, so we added covariates (including dummy variables for Thailand’s 76 provinces) and we were able to generate models that were adequately balanced. For instance, when we confined our sample to rural areas, the propensity score model had 101 covariates, generated 13 strata, and produced 14 cases where covariates were not balanced. This is acceptable, given that at a one percent level of statistical significance one would expect to find, erroneously, about 13 cases of imbalance (false negatives).

_Village Fund, draft of June 29, 2009_ _Page 10 of 34_
A listing of the variables used in estimating the propensity scores for 2004 is given in Table 3 (except for the provincial dummy variables). The first thing to note is that on average VRF borrowers are substantially poorer than those who do not borrow from the VRF, whether measured by monthly expenditure per capita (2,549 baht vs. 4,286 baht) or income per capita (3,209 baht vs. 6,088 baht), or by access to subsidized medical care (93% have a 30 baht medical card, vs. 77% for non-borrowers). Compared to non-borrowers, those who borrow from the VRF are more than twice as likely to be farmers and to be self-employed, they are more likely to live in the Northeast region, they have larger families, and there are more earners per household. The important point here is that borrowers differ appreciably from nonborrowers, at least unless one conditions on the covariates.

The estimate of the probit propensity score equation for the full sample is also shown in Table 3. The equation fits well enough and, as noted above, appears to be adequately balanced. One of the more influential variables is the inverse of the number of households per village (or block): The Thai Village Fund initially provided a fixed amount to every village, irrespective of size, which means that households living in a large village are less likely to have access to these loans than those in a small village. This effect shows clearly in the estimates of the propensity score equation reported in Table 3.

# Basic Results

Given the propensity scores, it is then possible to match each treatment case with a nearby comparison case, and hence to estimate the impact of VRF borrowing. The results are summarized in Table 4; the upper half of the table refers to 2004 (with separate propensity score equations for the full sample, for rural households only, and for the panel), and the bottom half to 2002.

When propensity score matching is used with the full sample of households surveyed in 2004, VRF borrowing is associated with a statistically significant 3.3% more expenditure per capita and a not-quitesignificant 1.9% higher income per capita. Translated into average increases (at the mean) this implies a rise in per capita spending of 84 baht per month and of income of 61 baht per month. A reasonable interpretation is that VRF loans are partly, but not exclusively, functioning as consumer credit; they also appear to be working through the effect on income. The results based on the 2002 data are comparable: VRF borrowing is associated with a 3.1% rise in income (t=1.90) and a 2.6% rise in expenditure (t=2.15). To put these numbers into perspective, the mean size of a VRF loan was 16,183 baht (Table 2), and mean monthly income per person was 4,987 baht (Table 1) in 2004.

The increases reported in Table 4 are plausible. The boost to income in 2004 represents an annualized rate of return of 4.5% on the amount borrowed (which averaged 16,183 baht). However, these effects are only found when expenditure (or income) per capita is shown in log form; when measured in levels, the VRF has no statistically significant impact in these cases. The use of the log of income (rather than _Village Fund, draft of June 29, 2009_ _Page 11 of 34_
its level) puts more emphasis to increases for poorer households, as the proportional effects (i.e. logs) are given more weight in these cases. To explore this further, we divided households into quintiles based on the levels of expenditure per capita, and then applied propensity score matching (with a single nearest neighbor) to each category. The striking result, shown in Table 5, is that the impact of VRF borrowing is only strong for the poorest quintile, a finding that holds both for 2002 and 2004. It would thus be appropriate to categorize the VRF policy as “pro-poor.” It is instructive to breakdown the impacts further, for each major category of income; the results are shown in rows 8-14 in Table 7. More VRF borrowing is associated with more farm income (up 49%, albeit from a modest base of just 522 baht per capita per month) and more income from non-farm enterprises (up 26%). On the other hand, VRF borrowing is not associated with higher wage or transfer income.

One may also break down the impacts by consumer expenditure category (see rows 15-26 in Table 7). There are substantial increases in spending on grain and meat, and also on vehicle operation, although this last effect is not quite statistically significant. None of the other measured impacts are statistically significant. These results differ somewhat from those reported by Kaboski and Townsend (2009, Table 5), who found, for a sample of villages in central Thailand, that VFR credit raised spending on alcohol, and on repairs to homes and vehicles.

The VRF appears to have the biggest impact in rural areas. If the analysis is repeated for rural households only, the effect is a statistically significant 6.9% boost to expenditure and 4.3% increase in income in 2004 (upper panel of Table 4), although the comparable effects in 2002 were much smaller.

There are minimal gender effects. For households that reported having a male head, VRF borrowing was associated with a 5.2% rise in expenditure and 4.8% increase in income. These figures are only marginally higher than those for female-headed households, where expenditure rose 5.0% and income by a (nonsignificant) 2.8%, as shown in rows 31 and 32 of Table 7.

In addition to the effect on income or expenditure, it might also be expected that VRF borrowing would have an effect on the accumulation of household assets. It is not possible to measure household gross or net assets using the Socioeconomic Survey data, but there is a listing of the major physical assets, of which some of the most important are given in Table 6. There we see, for instance, that 64% of all households surveyed had a phone in 2004; the rate was 59% for VRF borrowers and 67% for non-borrowers. We then used our propensity-score matching and found that, for instance, phone ownership among VRF borrowers was 5.4 percentage points higher than among comparable non-borrowers. Similar effects were found for VCRs, fridges, washing machines, and motorized transport. This, coupled with the smaller impact on income than on expenditure, suggests that VRF borrowing was used to some extent in order to get improved access to consumer and producer durables, despite the fact that fewer than 2% of households reported that this was the ostensible purpose of their VRF borrowing (see Table 2).

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# Robustness

How robust are these findings? A number of useful checks are summarized in Table 7: row 1 shows the basic result from Table 4, which is a 3.3% increase in expenditure per capita. Using the same propensity score equation we first measured the sensitivity of the results to alternative matching methods. Most of the results are of the same order of magnitude: stratification matching (i.e. matching within broader strata) shows a 4.2% impact of VRF borrowing on expenditure; kernel matching, which compares the treated case with all neighbors, but with high weights for near neighbors, shows an impact of between 1.8% (Gaussian kernel) and 4.5% (Epanechnikov kernel). Only caliper matching gives a radically different result – it compares all treated cases (i.e. VRF borrowers) to those with a propensity score within a radius of 0.001 – indicating, implausibly, that VRF borrowing reduced expenditure by 18%. This may be because a substantial number of borrowers with high propensity scores were not matched, and so were excluded, because there were no comparators in the immediate vicinity. However, this result does lead one to question the assertion by Dehejia and Wahba (2002) that the choice of matching mechanism is of secondary importance.

A somewhat different check on the robustness of our results is to match treatment households with non-treatment comparators using _direct_ nearest neighbor matching rather than first estimating propensity scores. It is not clear that direct (“covariate”) matching represents an improvement, even in principle, over propensity-score matching, and it is computationally intensive, but if both approaches give similar results then one can have more confidence in the conclusions. The results, for households living in rural areas (and using dummy variable for regions, rather than provinces) are shown in rows 6 and 7 of Table 7 and show that while VRF borrowing is associated with a statistically significant 7.6% increase in per capita spending as measured using propensity score matching; the effect is much smaller using direct matching – an increase of 1.3% if the direct match is based on a single nearest neighbor – and not statistically significant.

We also re-estimated the results after deleting villages that were either very small (under 50 households) or rather large (with at least 500 households). Perhaps surprisingly, the results are somewhat stronger, and show a 4.8% increase in expenditure and 3.7% rise in income due to the VRF (lines 27 and 28 in Table 7).

The most important maintained assumption in propensity score matching is that “the process by which individuals are assigned or assign themselves to treatment” is ignorable (DiPrete and Gangl 2004). That is, after removing the effects of observable variables, we may proceed as if subjects were randomly assigned to treatment. This is a strong assumption. In practice there are likely to be unobserved variables, such as motivation or ability, that simultaneously affect the outcome, and the assignment to treatment. By definition we cannot quantify the effects of this “hidden bias”. One solution, proposed by Rosenbaum (2002), is to test the sensitivity of the results to the introduction of a hypothetical “confounding variable” _W_ , that affects the _Village Fund, draft of June 29, 2009_ _Page 13 of 34_
odds of being assignment to treatment. Let πi be the probability that unit _i_ receives treatment, and X _i_ the observed covariates. Then the log odds ratio is given by Under the hypothesis of ignorability, γ=0 (or equivalently, Γ=1, where Γ≡e<sup>γ</sup> ). With higher values of Γ, propensity score matching will be less precise. Rosenbaum shows how to obtain significance levels (using a Wilcoxon sign-rank test) and new confidence intervals (if the treatment effects are additive) for different values of Γ. The results of estimating these Rosenbaum bounds for the log of expenditure per capita are shown in Table 8, and show that our results are not especially robust; if an unobserved variable were to cause the odds ratio of treatment assignment to vary by a factor of about 1.07, then our finding of a impact would no longer be statistically significant at even the 10% level. Although our results are sensitive to the assumption of ignorability, this potential loss of significance is, as DiPrete and Gangl (2004) rightly point out, just a worst-case scenario.

Our final robustness check is to estimate the effect of borrowing on income and consumption using a common impact model (Haughton and Khandker 2009). Let _Yi_ measure the outcome, X _i_ be a vector of covariates, _Ti_ measure the treatment under consideration (i.e. VRF borrowing), and εi represent a zero-mean error term, and estimate Then the estimate of the coefficient αTC should be able to measure the impact of the borrowing. The results are shown in Table 9, and use the same other covariates as in the propensity score matching (see Table 3). When the treatment is measured as a binary variable, set equal to 1 if the household borrows from the VRF, then the impact is to raise expenditure per capita by 2.3% - broadly in line with the 3.3% impact as measured using propensity score matching (Table 4); however, the estimated effect on income is nil. One may also measure the impact of the amount of borrowing, _given that one is a borrower_ . The middle section of Table 8 shows that an additional 100 baht of borrowing is associated with 83 baht more spending and 143 baht more income, figures that are on the high side, particularly for income, unless “lumpiness” in investment is a commonly binding constraint. The estimates in the bottom panel of Table 8 imply that a 10% higher loan is associated with 1.4% more consumption or 1.8% more income, again rather large effects. The common impact model is less compelling than propensity score matching because it does not confine the estimates to a region of common support, and does not try to tailor comparisons for each treated case.

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# The Bank for Agriculture and Agricultural Cooperatives

The VRF is not the only, or even necessarily the most important, source of credit for Thai households. The Bank for Agriculture and Agricultural Cooperatives has an extensive network of rural lending. Of the households covered by the 2004 socioeconomic survey, 23% borrowed from the VRF only, 15% borrowed from both the VRF and BAAC, and 6% borrowed from the BAAC only. These figures differ slightly from those presented earlier because they only refer to the two most important loans incurred by any given household. But the fact that many households borrow both from the VRF and the BAAC raises the possibility that our earlier results may be picking up the effect of BAAC borrowing and attributing it to VRF borrowing.

We therefore applied our propensity score matching approach to borrowing from the BAAC, and report the results in Table 10. For each comparison (i.e. row in Table 10) we estimated separate propensityscore equations. From Table 10 it is clear that those who borrowed from the BAAC in 2004 were comparably poor to, and somewhat more dependent on farm income than, VRF borrowers.

The first point to note is that, based on the results of the propensity-score matching analysis set out in Table 10, borrowing from the BAAC, with or without other loans, is associated with substantially higher expenditure per capita (+6.5%) and income per capita (+6.1%). This effect is larger than that of borrowing from the VRF (expenditure per capita rises 3.3%, income per capita by 1.9%, as shown in Table 4).

The most striking finding is that the _combination_ of borrowing from the BAAC and VRF has particularly powerful effects, and is associated with 9.1% higher expenditure and 8.5% higher income. Loans from these two sources appear to be complementary. A plausible interpretation is that many households, particularly farm households, are credit constrained, even if they borrow from the BAAC; the VRF, by relaxing these constraints, enables them to boost their incomes. It is noteworthy that borrowing from the BAAC but not VRF, or from the VRF but not BAAC, has a small and only marginally significant effect on expenditure levels and an even weaker effect on incomes. This hints at a real, but moderate, degree of “lumpiness” in investment, where the full return on using borrowed money is only obtained when the sum is large enough.

The propensity score matching results appear, on balance, to show that VRF borrowing raised household income and expenditures on average, and that much of the productive effect operated in agriculture. In the next section we use a different approach, instrumental variables, further to check the robustness of these results.

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# **6. Instrumental Variables**

We are interested in finding an unbiased estimate of the impact effect – an estimate of γ – in an outcome equation of the form _Yi_ = α +γ . _Ti_ + **X** _i_ β + ε _i_ , _i_ = 1,..., _n_ (3) where _Yi_ is the outcome of interest, _Ti_ is a dummy variable that equals 1 if the household borrows from the VRF, and the Xi variables are relevant covariates. However, _Ti_ is a “troublesome explanator” (Murray 2005) because it is likely correlated with εi: as the basic numbers in Tables 2 and 4 show, VRF borrowers are not a random sample of the population – they are poorer, spend less, and own fewer durable goods.

An unbiased estimate of γ may be found if one can construct an adequate participation (“first stage”) equation of the form _Ti_ = _f_ ( **Z** _i_ , **X** _i_ ), (4) where the instruments Z _i_ should be strongly correlated with _Ti_ (“instrumental relevance”) yet be uncorrelated with εi (“instrument exogeneity”). Then the estimated value,<sup>_T_ˆ</sup> _i_<sup>, is used in place of</sup><sup>_T_</sup> _i_<sup>in equation (3).</sup> We may think of the instrumental variables (IV) estimate of γ as reflecting the “marginal” impact of the treatment; that is, it measures the impact on expenditure (or income) of one more person borrowing from the VRF. This differs from the propensity score matching measure, which quantifies the average impact across all those who are treated. If treatment brings diminishing marginal returns, one might expect the impact, as measured using propensity score matching, to be larger than that measured using the instrumental variables approach.

The main practical problem with the IV approach is finding appropriate instruments, yet “the credibility of IV estimates rests on the arguments offered for the instruments’ validity” (Murray 2005, p.11). In our case there is one good candidate: the inverse of the size of the village. A feature of the VRF is that it provided a million baht to each Village Rotating Fund, irrespective of the size of the village. Thus the probability of obtaining a VRF loan (“participation”) is approximately in inverse proportion to the size of the village. Our measure of the size of the village is the number of households, which is likely to be closely correlated with the theoretically ideal measure (the number of people eligible for VRF loans, which is the number of adults aged 20 and above).

The IV estimates of the impact of the VRF are summarized in Table 11. In each case the first step equation is probit; an example, for the log of expenditure per capita, is shown in detail in Appendix Table A1. In all cases the influence of the instrument in the first-stage equations is highly statistically significant, clearly showing its relevance.

The second-stage equation is linear. Where possible, estimation was done using maximum likelihood and using sampling weights; in the cases when this estimator did not converge we used a simpler two-step _Village Fund, draft of June 29, 2009_ _Page 16 of 34_
procedure on the unweighted data. In all cases the reported z-statistics have been adjusted to account for the fact that one is using<sup>_T_ˆ</sup> _i_<sup>rather than</sup><sup>_T_</sup> _i_<sup>in the outcome equation.</sup> The IV results in Table 11, for 2004, show a positive but not statistically significant impact of the VRF on expenditure and income. In rural areas the measured effects are negative. Curiously, the impact on farm income, and on non-farm income, are separately large and positive. The results for 2002 show that VRF borrowing raised expenditure by 9.9%, and income by 8.4%, although the latter effect is not highly statistically significant.

These results are not particularly robust. The middle rows of Table 11 show the effect on the IV estimates of adding other instruments. The first instrument is “anydebt”, which equals 1 if the household in 2004 has any outstanding debt. This is strongly correlated with whether a household borrows from the VRF, but weakly associated with the outcome variable (e.g. simple correlation with expenditure per capita of -0.035; weighted correlation of -0.109). The inclusion of this instrument raises the measured impact of the VRF to a statistically significant 16% for income and 20% for expenditure, levels that are certainly on the high end.

It might be objected that “anydebt” is not exogenous, if households borrow from the VRF when they would not otherwise have borrowed. Alternatively one could use a measure of “non-VRF debt”, set equal to 1 if the household has debt other than VRF debt. With this instrument the measured impact of VRF borrowing on household spending rises to an implausible 46%, but even here it might be argued that the new instrument is not truly exogenous.

Finally, we also add, as an instrument, the interest rate charged by the VRF. It is plausible that a higher interest rate would deter borrowing – indeed, the weighted correlation coefficient is -0.054 – and be essentially unrelated to the log of expenditure per capita (correlation of 0.046). The inclusion of this instrument raises the measure of the impact of VRF borrowing to unrealistically high levels. But it is by no means a fully satisfactory instrument: when it is included, the sample size falls, because interest-rate information is only available for villages that have an operating VRF.

In sum, the results of our IV analysis are not very sharp and are partly contradictory. It does seem reasonable to conclude, however, that the most satisfactory models just use the inverse of the village size as an instrument; and in this case, the marginal impact of the VRF on expenditure and income is minimal. Combined with the propensity score matching results, it appears that the VRF raises spending and income on average, but is experiencing diminishing returns at the margin.

Our results are broadly in line with those found by Kaboski and Townsend (2006), who also used an instrumental variables approach, but with data from the 2003 and earlier rounds of a panel of 960 households surveyed in four rural provinces. They checked for robustness by applying a variety of econometric specifications (levels, changes, and estimates with and without outliers). Their main findings are that greater use of the VFR was associated with somewhat higher levels of household expenditure, and perhaps an _Village Fund, draft of June 29, 2009_ _Page 17 of 34_
increase in income, and with an increase in agricultural investment as well as spending on fertilizer and pesticides.

Kaboski and Townsend also found that VRF borrowing was associated with an apparent reduction in net household assets. This might seem surprising, but could be due to mismeasurement (a farmer might have invested in drainage or field leveling, and this might not be picked up in survey questions), or because better access to credit reduces the need to hold assets, or because households overborrowed.

# **7. Panel Data**

An effort was made, in the socioeconomic survey of 2004, to re-survey half of the rural households that had been interviewed in 2002. This produced a panel of 5,755 rural households for which information is available for both years. The panel data allow us, in principle, to get a less biased measure of the impact of VRF borrowing, because one can eliminate unobserved variable bias, provided that the bias is linear and does not vary over time. It also helps that the introduction of the VRF was a “surprise”, in the sense that it was proposed and implemented swiftly, and households in 2002 could not easily adjust their behavior in anticipation of future lending.

# Double Differencing

The simplest way to use the panel data is by double differencing. If, before the borrowing, income _Yi_ depends on covariates X _i_ , then and afterwards with ε _it_ =η _i_ + μ _it_ . Differencing gives Considering those households that did not borrow from the VRF in 2002, a regression of the differenced outcome variable on the treatment variable (which equals 1 for those who borrowed from the VRF in 2004) and the change in the covariates should estimate the impact, while “sweeping away” the effects of unobservable or mismeasured (but time-invariant) covariates. The results of this exercise are shown in the middle panel of Table 12, which shows little to no impact of the VRF on expenditure (impact of 2.0% but t- statistic of 1.04), income, or even farm or non-farm income.

To check the robustness of these results, before computing the double differences we first estimated the propensity scores using the 2002 data and the same variables as in Table 3, and then confined the double _Village Fund, draft of June 29, 2009_ _Page 18 of 34_
differencing to the area of common support. We weighted the differences for each treated case (i.e. VRF borrower) by 1, and each comparison case by _p/(1-p)_ – where _p_ is the propensity score – as recommended by Imbens (2004; also Ravallion 2006). The results, shown in the bottom panel of Table 12, were similar to those of the unweighted, unconstrained estimates: there is a hint of an impact on expenditure per capita, and on non-farm income per capita, but none of the effects are statistically significant at the conventional levels.

It is also possible to confine the double differencing to those who did not borrow in 2004 (and look at the effects of borrowing in 2002); or to those who did borrow in 2002 (and look at the effects of continuing to borrow in 2004).<sup>i</sup> None of the results in these cases (not shown here) were statistically significant.

# Panel Instrumental Variables

As a final exercise we undertook an instrumental variables analysis using the (rural) panel data and incorporating household fixed effects. The linear first-stage equation uses, as instruments, the presence of a VRF in the village, this measure multiplied by the educational level of the household head, and the size of the village multiplied by the educational level of the head. The full equations, for the case where the outcome is the log of expenditure per capita and the comparison is between those who borrowed from the VRF in 2004 and those who borrowed neither in 2002 nor in 2004, are shown in Appendix Table A2.

The key results are summarized in table 13. Households that borrowed from the VRF in 2004 had 15% more income and 18% more expenditure than those who borrowed in neither year, holding other influences constant; these increases are statistically significant, but also rather large. If, instead, the comparison is between those who borrowed both in 2002 and 2004 and those who borrowed only in 2004, the impact of the second year of borrowing was to raise income by 8% and spending by 10%. These statistically significant rises are within the bounds of plausibility.

# **8. Conclusions**

This study of the impact of the Thailand Village Fund is based entirely on data from the socio-economic surveys of 2002 and 2004, undertaken just one and three years after the VRF was launched. In the absence of random assignment, we were obliged to use quasi-experimental methods to quantify the effect of the VRF on outcome variables. The propensity score matching approach generates reasonable results: the Village Revolving Fund does appear to have had an impact, raising expenditures by 3.3% and income by 1.9% in 2004. These results are tolerably robust to most specifications of matching, and we may interpret these numbers as reflecting the average impact of the VRF program.

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By and large the other results – based on using instrumental variables on cross-section data, double differences, and instrumental variables using a rural panel – do not contradict the propensity score matching results. The instrumental variables estimates suggest that the _marginal_ impact of the VRF may be small, even though, based on the propensity score matching, the _average_ impact is more substantial. The double difference results show little effect, but the instrumental variables analysis with household fixed effects shows a surprisingly large impact of VRF borrowing in rural areas.

Our interpretation of these findings is that the VRF has indeed had a moderate impact on household spending, and also (but to a lesser extent) on household income; this is consistent with our expectations, based on theory.

Further investigation shows a number of interesting patterns. First, most of the effect of VRF borrowing is concentrated in the poorest quintile of the population (as measured by expenditure per capita), where it raised spending by 5.2%, making the program markedly pro-poor. Second, the effect of the VRF appears to work most convincingly through its influence on farm income, suggesting that it is creditconstrained farmers who have best been able to put the loans to productive use. This is not what the designers of the Fund had envisaged; instead they had expected that it would boost household-level non-farm enterprise (and there is some, if modest, evidence of this too). We speculate that the short-term nature of the VRF loans makes them suitable for farmers – they allow for the financing of inputs during a crop cycle – but are not sufficiently long-term (or perhaps large) enough to be very useful for most of the other remunerative activities that households might initiate.

The third interesting finding is that there are synergies between VRF and BAAC loans; borrowing from one or the other alone has only a modest discernible impact on incomes or even expenditure, in contrast to the large impact associated with borrowing from both sources. This has some important practical implications. The BAAC should be slow to withdraw from village-level lending, even if it is tempted to do so by a perception that the VRF can fill the gap; or alternatively, the BAAC should be sure to channel enough resources via the VRF to allow it to fill the gap adequately. Our results also suggest that if the government wants to expand the VRF, the most productive approach would be to target poorer farming communities.

Finally, a caveat. Our results do not allow one to make a judgment about the desirability of the VRF. That would require additional information about the full costs of the program and an evaluation of its sustainability. It would also be valuable to determine whether the impact of the VRF weakens over time, a finding that is common elsewhere (e.g. Chen et al. 2006; Khandker 2005). These both require further research, which would be particularly desirable given the importance of the Thai experiment with large-scale microcredit.

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