ESTIMATING TREATMENT EFFECTS FROMSPATIAL POLICY EXPERIMENTS:
An Application to Ugandan Microfinance
Craig McIntosh∗
February 5, 2007

Abstract
This paper demonstrates a method for estimating treatment effects inspatial tests, utilizing a second control group to measure unexplained spatial
phenomena. The technique is implemented on two innovations in Ugandan
microfinance, and we measure the ways in which concurrent shocks such as
an ebola outbreak and a contentious presidential election altered outcomesdifferentially across regions. By correcting for this spatial heterogeneity wemeasure the impact of the policies; a program which increased borrowers’
control over the terms of their loans improved outcomes, while the resultsof a program which bundled health insurance into the lending contract weremore mixed.

JEL Classification: C14, C21, O12, O16
Keywords: Impact Analysis, Spatial effects, Microfinance, Insurance∗

International Relations/Pacific Studies, U.C. San Diego. Thanks to Fulbright IIE for researchfunding, and to Eli Berman, Alain de Janvry, Gordon Hanson, Guido Imbens, Ethan Ligon,
Elisabeth Sadoulet, Michael Ward, and seminar participants at U.C. Berkeley, U.C. San Diego,
University of Maryland, RAND, Dalhousie University, WEAI, and NEUDC for helpful comments.

I

Introduction

Spatial policy tests are subject to biases which randomized tests are not (Kremer
2003), and yet they are likely to remain a permanent feature of the quasi-experimental
evidence available to researchers. States, school districts, administrative branches
and the rule of law all describe physical spaces, and so designating physical regions
as treatment and control will continue to be the least intrusive way for many kindsof institutions to experiment (Card & Krueger 1994). The trouble with this approach is that if outcomes are being determined by some process which is itself
spatial and we fail to control for this process, the resulting spatial heterogeneity is
indistinguishable from a treatment effect in a spatial policy experiment and so it
biases difference-in-differences estimators. Many policies, however, are either voluntary or have eligibility requirements. In this case we have a group of agents who
did not choose or qualify to receive the treatment, and so there will be untreatedunits even within the treatment region.
The value of this parallel untreated group is that it allows us to examine thedifferences between the treatment and control region in the absence of a treatment
effect (Rosenbaum 1982), (Gruber 1994). Under assumptions laid out below, ineligible groups experience similar relative spatial heterogeneity to what would havebeen observed in the eligible group had none of these units received the treatment.
Specifically, after running the difference-in-difference regression (without a treatment term) in this non-participant group, we suggest mapping the residuals acrossspace as a means to measure whether or not there are significant unexplained phenomena that differ across the treatment and control regions. These residuals forma spatial surface that allows us to answer the following question: what is the unexplained outcome that we would expect to see for a qualified unit in a given location1

if there had not been a spatial policy test? This contour measures exactly thequantity that biases the difference-in-differences, and so it is subtracted off of outcomes in the group that did qualify for (or choose) the treatment. The result isa fine-grained form of triple-differencing which measures the treatment effect on
the treated, accounting for localized shocks or mis-specification in the estimating
equation. This not only makes spatial impact analysis robust to unexplained shocks
and endogenous placement, but allows us to measure a kind of impact invisible tostandard techniques: the ability of a treatment to insulate agents against shocks.
We apply the technique to two new policies introduced by FINCA Uganda, thecountry’s largest micro-finance institution. The first innovation allowed clients tochange the repayment frequency of their loans, and the second bundles a healthinsurance package into the lending contract. A straightforward spatial testing strategy was implemented, wherein whole administrative branches of the institution were
designated as treatment and control regions. A standard analysis of a voluntary,
spatial test would either compare treated and untreated regions to estimate theintention-to-treat effect, or identify those likely to choose the program in the control in order to estimate the treatment effect on the treated. Here, we dealt withthe selection problem by conducting mock elections in the control region in order toestablish which groups would have chosen the programs had they been offered them.
With this extra degree of identification we can use differences between choosers andnon-choosers as well as the differences between those offered and not offered theprogram to identify the impact of the two treatments.
The results of the analysis have several implications for best practices in microfinance. Weekly repayment is widely perceived to be central to the low default rates
observed in microfinance (Morduch 1999), yet this system entails large transaction2

costs for both lender and borrower. We find that moving from repaying loans every
week to repaying every two weeks causes none of the predicted negative effects, instead causing dropout to fall by 10 percentage points (a 40% reduction) and triggering a slight improvement in repayment performance. The implication of this study
is that when clients are allowed to decide whether their fellow members are capableof repaying reliably biweekly, information revealed by the joint-liability mechanism
allows transaction costs to be reduced without pushing up default. The entire impact of the health insurance program arose due to insulation against shocks, rather
than from directly observable changes in outcomes. New client enrollment increased
sharply, but client composition shifts for the worse in insured groups suggesting thatthe asymmetric information problems in credit and insurance markets need to besolved separately rather than using a single joint-liability contract (Stiglitz 1990),(Ghatak 1999) to solve them both.

II

Bias in the Difference-in-Differences

The joint-liability group is the unit of observation. The change in outcomesis denoted by Yi , which is determined by some function Yi = f (Xi , si , Zi ) + i .
We use simple changes in outcomes rather than a panel because most of our control
data is cross-sectional, and also because using before-after differences eliminates theconcerns raised in Bertrand, Duflo & Mullainathan (2004) over the inconsistency ofstandard errors in a panel DID when outcomes are serially correlated. Xi is a vectorof observable control variables, si is group i’s location in physical space, and Zi isa vector of unobservables. Treatment status is a binary variable indicating whether
a group was in the region in which the treatment was offered, and is denoted by
Ti . Our application involves a spatial treatment-control strategy, which implies a3mapping from location si to the treatment status; we denote this mapping by τ ,so τ (si ) = Ti ∈ {0, 1}. In addition, the treatment is voluntary, and so groups
may either choose or not choose to accept the treatment, a decision denoted by
ωi (this can represent either choice or eligibility to participate; the terms are usedinterchangeably here). Receipt of the treatment, then, indicates that Ti = ωi = 1.
In potential outcomes notation, Y1i represents changes in outcomes for a treatedgroup, and Y0i represents the counterfactual untreated outcome for the same group.
Without loss of generality, we can think of the treatment effect as additive, so that
Y1i = Y0i + t(Xi , si , Zi ). Since both choices and location determine treatment status
in this kind of test, we have a two-tiered selection problem. The rule by which agents
select into ωi = 0 and ωi = 1 is called the selection criterion, and Ti = 0 and Ti = 1
the treatment criterion; both rules are, in general, endogenous. Estimating impact
in such two-tiered tests requires us to account for variation in the determinants of
Yi across both criteria.
We investigate the bias due to spatial heterogeneity by explicitly denoting the
portion of outcomes which is systematic but not explained by a linear function b ofobservables as φ(Xi , si , Zi ). Therefore the equations determining outcomes are:Y0i = bXi + φ(Xi , si , Zi ) + i ,and
Y1i = bXi + φ(Xi , si , Zi ) + t(Xi , si , Zi ) + i ,The Difference in Differences estimator for the average treatment effect on thetreated (ATT) when we observe treatment choices in the control is:4Yi = β1 Xi + δ1 Ti + µi ∀ ωi = 1.
Although the ability to compare choosers to choosers has removed selection bias
from this estimate, the DID will be biased in a spatial test unless unexplained
spatial effects are identical in the treatment and control regions. In the DID estimator, φ(Xi , si , Zi ) is an omitted variable which is orthogonal to X by definition.
Consequently, it will project into T but not into X, and we estimate impact to beδˆ1 = E(t) + PT (φ). Since Ti = τ (si ) is a binary variable defined over space, theprojection of φ into T will equal E(φ | τ (s) = 1) − E(φ | τ (s) = 0).
If we consider the non-choosers of a program to represent a counterfactual forthe spatial variation in outcomes that would have been present in the absence ofa treatment, then we are provided with a spatial surface which forms a naturalbaseline from which to estimate the true effects of the treatment. A simple way
to proceed would be to subtract off locally-averaged outcomes among non-choosers
from the outcomes of each chooser. Upon further reflection, however, we see that
it is only unexplained spatial effects which will bias estimates, and so we should
not include in this local outcome estimate anything which is directly explained byobservables. This suggests that it is the residuals among non-choosers in a local areathat possess the most information about unexplained spatial effects. The reason forthe concern with shocks which vary across space is that it is only unexplained effects
which have some spatial component that will project into the treatment and cause
bias. The direct implication is that if we are able to estimate residual spatial effects,
we can recover an impact term free of both selection bias and spatial bias.

We now introduce two assumptions which allow us to estimate and utilize these5spatial effects. The first is essentially an extension of the typical Selection assumption:
Spatial Assumption : E(φ | si , ωi = 1) = E(φ | si , ωi = 0).
Because we include a constant term in the X-vector, E(φ | ωi = 1) = E(φ | ωi =0) ≡ 0. So the Spatial Assumption says that a chooser and a non-chooser located at
the same place should experience unexplained spatial effects, relative to their owngroup mean, that are the same.
The second required assumption is that there be no spillover effects of the treatment from choosers to non-choosers within this same region.

N o Spillovers Assumption : E(ti | ωi = 0) = 0
These assumptions suggest two straightforward ways of using our assumptions.
The first is the OLS analogy to the general estimators described in Rosenbaum(1982) for testing whether an unobserved covariate differs across the treatment criterion. We can estimate the False Difference-in-Differences (FDID) regression
among non-choosers;
Yi = β2 Xi + γ1 Ti + µi ∀ ωi = 0.
γ̂1 will equal E(PT (φ) | ω = 0), which is a spurious treatment effect arising from unexplained spatial phenomena. If the spatial dispersion of choosers and non-choosers
is identical, the spatial assumption implies that
E(PT (φ) | ω = 0) = E(PT (φ) | ω = 1),
and so γ̂1 is a precise measure of the spatial bias among choosers. In this case, we
6can recover an unbiased estimate of the ATT by subtracting the coefficient fromthe FDID off of the DID, which is analogous to conducting a Triple Difference
regression:
Yi = ωi β1 Xi + (1 − ωi )β2 Xi + α1 Ti + α2 ωi + δ2 (Ti ∗ ωi ) + µi .
In other words, δ̂2 = δ̂1 − γ̂1 .
In the absence of spatial effects, the estimate from the triple-difference will be
the same as from a DID, but less efficient. Since the FDID will also be insignificant
in such cases, this suggests the use of the FDID as a preliminary test for the presenceof spatial effects. Only in the presence of a significant false impact in the FDID
should we proceed to utilize methods designed to remove spatial bias.
In recent years, an increasing number of researchers have been attempting toovercome the limitations of difference-in-difference techniques by some form of triple
differencing. Examples include the comparison of pre-treatment growth to posttreatment growth (McKenzie & Mookherjee 2003), (Banerjee, Duflo & Munshi2003), or comparison of current and past members of a training program to amatched sample of non-participants (Ravallion, Galasso, Lazo & Philipp 2002).
Closer to the application presented here are efforts to compare eligible and ineligible agents in regions which offer and do not offer a program. Hammermesh & Trejo(2000) use a dummy-variable approach to compare the differences between womenand men in California versus non-western states before and after overtime benefits
had been extended to men in California. Kugler (2005) follows Gruber (1994) in estimating a triple-difference by interacting dummies for being eligible, for being in a7

treatment region, and for being in the post-treatment time period. Morduch (1998)
presents a set of tables which demonstrate the mean difference between households
that are eligible and ineligible for microfinance, across villages that do and do nothave microfinance institutions. To date this literature, however, has used the second
control group simply to calculate lump-sum spatial effects through regional meansor dummy variables.
So, under what circumstances will a dummy variable approach to triple differencing form the correct counterfactual? The purpose of the second control group is
to give an estimate of unexplained changes in outcomes across the space that defines
the treatment criterion. Hence if the dummies represent very small units such as
villages (Pitt & Khandker 1998), if spatial effects happen to line up neatly with thedummy used for the treatment unit, or if the spatial distribution of eligible and ineligible is identical, then a dummy-variable approach to triple-differencing recovers
the correct counterfactual. In many cases, however, the spatial unit of treatment
is large, spatial effects are localized, and eligible and ineligible units do not haveexactly the same spatial distribution. In this case, the average spatial effect among
the eligible within a given region differs from the ineligible, and so even under ourassumptions, the triple-difference estimator is inconsistent. This problem cannot
in general be overcome through fine-grained spatial dummies because they will becollinear with the treatment term.

III

The Spatial Matching Estimator

The contribution of this paper is to show that, if we have precise location information, we can recover a consistent estimate of unexplained spatial effects evenwith highly localized shocks. Using the non-chooser (or ineligible) units, we can8first construct a spatial surface which represents this heterogeneity. We can thenutilize techniques designed for propensity-score matching across the selection criterion (Rosenbaum & Rubin 1983), (Angrist 1995), (Dehejia & Wahba 2002) in orderto match agents for whom ωi = 1 to the counterfactual surface estimated amongωi = 0, using physical location. By taking the value of this surface at the exact
location of each chooser (or eligible) unit, we correctly form the counterfactual regardless of differences in the exact spatial distribution across the groups, as long as
they share a common support.
The closest analogy to this is the ‘regression-adjusted conditional difference indifferences matching estimator’ discussed in Heckman, Ichimura & Todd (1997).
They invoke an exclusion restriction to match across the selection criterion, andsubtract off counterfactual fitted values from a linear regression. The resulting
estimator performs well when compared to experimental identification of the true
impact of a job training program. The estimator suggested here is able to add
an additional level of differencing because we observe selection status in treatment
and control alike, and so can eliminate selection effects and match instead acrossthe treatment criterion. Seen in this light, we can recast our assumptions as the
exclusion restriction required to use physical location as an instrument for treatment
status in comparing the difference-in-differences across choosers and non-choosers.
To operationalize the method, we first run the FDID regression among ωi = 0,
except that the treatment term is omitted so that all spatial effects remain in theresiduals. We then calculate a local average using linear distance around eachchooser i of the residuals among non-choosers, denoted by µ̂i0 . For each i andnumber of nearest neighbors M we have a set J(M, i) of nearest neighbors.

9The local average is denoted by:
µ̃i =

1 X
µ̂i0 .
M i0 ∈J(M,i)

This is the value at chooser’s location si of the residual surface among non-choosers
i0 , smoothed by M . This value can then be subtracted off the dependent variable
and the difference-in-differences is run on the choosers.
So, the Spatial Matching estimator estimates the ATT as follows:
Yi − µ̃i = β3 Xi + δ3 Ti + µi ∀ ωi = 1.
Because it is a mean, for small M , E(µ̃i | si ) = E(µ̂i0 | si ). In the absence of thetreatment, µ̂i = Yi − β̂Xi = φi +i . Epsilon is an i.i.d. error term and we assume thatthe untreated receive no treatment effect, and therefore the spatial expectations ofresiduals contain only spatial effects: E(µi0 | si ) = E(φi0 | si ) ∀ s. Applying the
spatial assumption to this expression shows that E(µ̃i | si ) = E(φi | si ).
This implies that Yi − µ̃i is an outcome which allows for unbiased estimationof the ATT even when PT (φ) 6= 0. The counterfactual dependent variable amongchoosers is determined by:
Y0i − E(φ | si ) = bXi + φi − E(φ | si ) + i .
The term φi − E(φ | si ) represents the unobserved effect minus the unexplained
effect conditional upon being in that location. Crucially, the resulting term is itself
orthogonal to space, and so can be written as φi − E(φ | si ) ≡ Ms (φi ): this is theresidual vector that remains when φ has been projected into s, or the component
10

of the outcome vector that projects off of both X and s.
The unexplained residual is orthogonal to X by definition, and is orthogonal to
the treatment by construction, since:Ms (φ)⊥[τ (s), βX]
Because PT (Ms (φi )) ≡ 0, when we use our modified dependent variable to run a
DID regression
Yi − µ̃i = βXi + δ3 Ti + µi ∀ ωi = 1,
E(δˆ3 ) = E(t) + PT (Ms (φi )) = E(t), giving an unbiased estimate of the ATT.
One attractive feature of this approach is that it allows for consistent estimationof treatment effects even under endogenous placement. If a program is (intentionallyor unintentionally) placed in a region which has inexplicably different rates of growthfrom the control, this is usually fatal to our ability to estimate impact. The spatial
assumption, however, will apply as long as it is the case that the non-choosers of
the program share the outcome differences seen among nearby choosers. In otherwords, if treatment regions contain non-random draws of administrative quality,
economic prospects, or ethnicity, this only biases spatial impact assessments because
it introduces spatial heterogeneity. To the extent, then, that this spatial effect is not
related to selection into the program in a way that varies across space, the effectsof the endogenous placement will be removed by the use of spatial matching to thesecond control.
Although there is no way to directly estimate the intention to treat effect when
spatial effects are present, we can back out an estimate from the ATT. The reason11

is that we have already assumed no spillover effects, which means that E(ti | ωi =0) = 0, and so the intention to treat effect can be estimated by:
IT E = δˆ3 ∗ P r(ω = 1),
where P r(ω = 1) is the fraction of choosers. To the effect that the treatment effectitself is spatial, we estimate the ATT over the control space.
A technical problem arises in the use of OLS residuals due to the potential
clustering of the Xs in space, which will cause observables to proxy for underlying
spatial effects. If we do nothing to address this issue, then the spatial assumption
in reality requires a similar spatial distribution of the Xs between choosers andnon-choosers, which is an unpalatable assumption. To address the issue, we usean orthogonalizing procedure known as Gauss-Seidel Regression (Telser 1964) to‘backfit’ the residual vector among non-choosers. This procedure uses a spatialsmoother to extract spatial information present in the residuals, subtract it off of thedependent variable, and iterates until there is no spatial component remaining. The
resultant βs are used to predict a vector of residuals which contain the full degreeof spatial variation. This procedure is deemed to make the spatial assumption more
realistic, and so it is implemented throughout the paper.
There are alternative ways to use the two controls which do not require backfitting. One would be to use raw residual surfaces and to match choosers to nonchoosers across both location and other observable variables. This solution, however, does not correct for the mis-estimation of the residual surface itself and so stillrequires an assumption over the similarity of the spatial distribution of the Xs between choosers and non-choosers. An alternative to this would be directly to match12

outcomes across both location and observable variables. Either of these methods
require that we use a more complex weighting matrix (typically the Mahalanobis
metric) to measure multi-dimensional distances. The non-parametric approach also
deprives us of the residual surface altogether, and insofar as this surface is of directinterest in the application at hand, we proceed to estimate it using backfitting.
We draw on the extensive literature developed to solve matching problems acrossthe selection criterion. We utilize a bias-correction technique suggested by Abadie& Imbens (2006) to estimate the following OLS regression:µ̂i0 = λsi0 + ηi ∀ ωi = 0.
The estimated shock at location si is then adjusted according to the distance anddirection between si and si0 and the average slope of the residuals across longitude
and latitude measured by λ. For the case where M=1 with i00 as i’s nearest neighbor,
we would haveµ̃i = µ̂i00 + λ̂(si − si00 ).
This removes bias that would result from imperfect spatial matching when theresiduals have a clear tilt across s.
The second technique taken from that paper is to establish a double counterfactual; not only do we estimate what all of the choosers would have looked likein the absence of the treatment, but we also estimate what all of the non-choosers
would have looked like had they received the treatment. Because we backfit residuals for both choosers and non-choosers, we can estimate a residual vector amongchoosers which contains the treatment effect. The regression used to estimate impact can be written in block matrix form as follows:
13

Y C − µ̃iN C
Y

NC

− µ̃C
i

XC

0

0

NC

T

=
X

-T

βC
βNC
δ

+ µ

Finally, we can vary the number of agents used to form the estimate of thelocal spatial residual. Matching to the single nearest residual generates a low-bias,
high-variance estimate. Matching to increasing numbers of agents is analogous
to smoothing the residual surface. Because the sum of the residuals among nonchoosers is identically zero, as we match to a larger number of agents the spatial
matching estimator approaches the DID estimator because the residual surface goes
towards zero everywhere. In our empirics we use a single match, which is theminimum-bias estimate, as well as 16 matches, to investigate how altering the sizeof the local area affects the impact estimates.

IV

Two Policy Innovations

FINCA Uganda is among the oldest formal microfinance institutions in the country and is one of the largest and best-established in Africa. Their standard lending
product utilizes a group-lending methodology, wherein the thirty members of ‘village
banks’ are jointly liable for each others’ loans. Loans are made almost exclusively
to women. There is no formal screening of new clients, so membership in groups isconstrained only by the selection imposed by current clients on members of theircommunity for whom they will accept liability. Loans begin at fifty dollars, andsubsequent increases are based on fixed multiples of clients’ savings determined by
the client’s grade, which in turn is based on repayment and attendance of weekly
meetings. The village banking methodology, using large groups and frequent meetings, in general targets the poorest market segment served by major microfinance14

organizations. Wealthier clients with rapidly growing businesses may eventually‘graduate’ to higher-tier lenders who use smaller groups and offer more customized
financial services (McIntosh, de Janvry & Sadoulet 2005). The standard loan has
a 16-week cycle, and clients pay 4 percent per month flat interest (87% effective).
Each client is covered by a life-insurance policy, whose premiums are included in
the interest payments. FINCA Uganda now has more than 25,000 clients in 1,000
village banks, spread over most of the conflict-free parts of Uganda.
At the beginning of 2000 FINCA Uganda began offering two new policies, as
shown in Figure 1. The programs were offered simultaneously, but to different
parts of the country. The health treatment was offered in downtown Kampala andin the area around Masaka, while the biweekly treatment was offered in the eastand north of the country. This leaves the central region, with the exception of thecapital itself, as the control. The biweekly treatment allowed groups to elect (bya unanimous vote) to change from the standard practice of repaying loans weekly,
to repaying them every other week instead. While it is clear that making fewer
payments is preferable to clients, the widespread perception that frequent repayment
is central to preventing default has made institutions slow to offer this service, andindeed makes members of joint-liability groups reluctant to accept it when it isoffered. Frequent repayment is likely to be particularly important to delinquency
rates for the poor (de Aghion & Morduch 2000). Thus, the primary concern for thosegroups which switch to biweekly repayment is whether the reliability of repayment
drops. Since clients in groups that have switched to biweekly payment have lower
transaction costs, dropout should fall. The same effect would cause new client
enrollment to rise, however biweekly groups may also be more selective in admitting
new clients; thus the effect on the fraction of new clients is ambiguous. Weekly15

repayment also places a very tight cash-flow constraint on client businesses; from
anecdotal evidence, the amount which can be repaid in the worst typical week often
determines what clients are willing to borrow. Thus, we hypothesize that biweekly
repayment will cause loan volume to increase.
The second new policy offered a voluntary health insurance package to village
banking clients and their families. The package costs roughly $13 per four-month
cycle and covers the client, spouse, and four dependants against routine medical
expenses. As an attempt to control adverse selection, in order for groups to beeligible for the health insurance package, more than sixty percent of the individuals
in any village banking group had to enroll (in effect, causing the adverse selectionof unhealthy groups rather than unhealthy individuals. Uganda is an environment
characterized by high mortality and morbidity; consequently medical costs can constitute a major burden for poor families. It is thus almost certainly the case that
FINCA will more attractive to new clients as it adds the health insurance option.
In practice, the insurance program suffered from major cost overruns; premia
calculated on the basis of pre-insurance health expenditures turned out to be far too
low to cover costs among the insured. Given the relative destitution of this client
base, there is good reason to think that this is a result of more than the standard
moral hazard story: if agents were truly constrained in their pre-insurance healthexpenditures, then the problem they face is fundamentally not one of insurance(which relates to smoothing) but one of limited income. Hence, even in the presenceof a well-designed program, we might expect to encounter cost overruns. These werelikely exacerbated by the fact that the 60% voting rule does very little to control
adverse selection, and does nothing to utilize information possessed by clients about
their fellow group members.

16Given the somewhat chaotic time period over which this data was collected,
we have prior reason to believe that spatial shocks may be present in outcomes.
An ebola outbreak occurred in October of 2000; the disease was contained to thenorthern part of the country but the town of Masindi, a part of the biweekly treatment, was effected. Figure 5 indicates that there was a significant increase in credit
demand in the region around Masindi, potentially as a result of the epidemic. In
addition, Uganda experienced political unrest surrounding the presidential electionin March of 2001 as Kizza Besigye mounted an unexpectedly strong challenge tothe incumbent president Yoweri Museveni. This episode led to insecurity and someminor rioting in the capital (the health treatment region), potentially explaining
the dramatic drop in credit demand there. It is also conceivable that pork-barrel
spending in the run-up to the election was apportioned in a non-random way acrosselectoral districts, creating differences in differences in the spatial pattern of business outcomes. While we cannot easily determine the causality behind such spatialdifferences, we confirm that they are present, and their mere presence is enough tobias the difference-in-differences.
The data are taken from the accounts of FINCA Uganda, and from surveys conducted at the individual and the group level during the test. The number of usablegroups, restricted to those which were in existence prior to the beginning of the test
and are in the relevant areas, is 450. Data was missing from roughly 10 percent of
the surveys, and groups which participated in either treatment were eliminated fromthe analysis of the other, reducing the overall number of observations to roughly 400
for each program. Table I lists the outcome and explanatory variables used in theanalysis. The chooser/non-chooser status of groups in control areas was establishedthrough a mock election as a part of the group survey; voting rules were applied17

in the same way that they had been in the treatment, e.g. 60 percent required for
health insurance, and unanimity for biweekly repayment.
In Table II, we see the number of groups that were offered and that chose thetreatments. In each case there is a slightly higher fraction of choosers in the control
than the treatment, possibly indicating that hypothetical decisions are more easily
taken than real decisions; to the extent that this bias exists it creates problems
for any assumption across the selection criterion. If some of the controls who said
they would accept the treatment would not actually do so when offered it, thenwe are comparing the treated to an insufficiently selected group of controls, andso some selection bias may still be present in our estimates. We perform t-testsof the differences in take-up rates across treatment and control regions, and findthat the difference is significant for the insurance treatment and insignificant forthe biweekly treatment.
Table III allows us to make conjectures as to the direction of this selection
bias. Here we compare means of the exogenous and (pre-treatment) endogenous
variables for both programs. We see evidence of program placement bias in bothcases through differences across the treatment criterion. Selection effects are present
in the exogenous variables for both programs; choosers of the biweekly program weremore urban and optimistic, and choosers of the insurance program came from older
groups and had larger families. There is evidence of selection bias in outcomes forthe biweekly treatment, where choosers are better repayers and less likely to dropout (consistent with (de Aghion & Morduch 2000)). If we had significant differences
in take-up rates in combination with selection effects in pre-treatment outcomes, wewould have reason to think that both double- and triple-difference estimators would
contain selection bias. In this case, because the take-up rate is not different where18

a selection effect in outcomes exists (biweekly), and no selection effect in outcomesexists where take-up rates are different (insurance), there is no obvious selection
problem. Any bias that exists would be in the direction of the effects seen at thebottom of Table III.

V

Investigating Spatial Effects

We begin our empirical analysis by investigating spatial heterogeneity, using thevariation in loan volume among non-choosers of the biweekly treatment as a test
case. In order to visualize these spatial effects, we create a moving average composedof the twelve nearest neighbors for each outcome. In Fig. 2, we plot the spatial
surface of deviations from the average loan size. The view is from the south-west,
over Lake Victoria, and the defining feature of this image is the large spike over thecapital Kampala, located on the north-west side of the lake. Obviously, conditionsin this city induce clients to take vastly larger loans on average than anywhere elsein the country.
Figure 3 is the same except that we now we use changes in loan volume. At
first glance, this picture appears to be the inverse of the previous, and again we see
the enormous difference between the capital and the rest of the country. It would
appear that changes in loans are inversely related to size, however the correlation
between loan size and loan growth in this subsample is positive (.014). Thus it
is more likely that the strong negative spike under Kampala is related to shocks
surrounding the 2001 presidential elections, which were disproportionately felt in
the capital.
It is unsurprising to find large spatial differences in raw rates of change. The useof a DID estimator in spatial tests, however, relies crucially on the assumption that19

the control variables will remove all spatial heterogeneity other than that imposedby the test itself. Consequently, if we examine the spatial surface of the residuals
among non-choosers (who have no treatment effect), under the assumptions of the
DID we should see a flat surface, meaning that no significant spatial information
remains in the residuals. The FDID, indeed, is measuring the difference in the
average height of this surface between the treatment and control regions. In Figure
4 we carry out the exercise of plotting residuals of loan changes, and we see that ourcontrol variables have achieved almost nothing in terms of removing the kinds ofspatial heterogeneity that will bias the DID; in fact, figures 3 and 4 appear virtually
identical.
Under the two assumptions presented in Section 3, the surface in Figure 4 isthe counterfactual surface for choosers, showing what the spatial heterogeneity inresiduals would have been in the absence of the test. The presence of such extreme
spatial heterogeneity in this picture, coupled with the fact that the capital is apart of the control for the biweekly treatment, implies that the DID estimate of
impact will be sharply biased upward. The lack of difference between the contours
in Figures 3 and 4 indicates that the DID estimate would be almost as biased as an
impact estimate arrived at by simply subtracting the raw changes in the control of
the raw changes in the treatment.
We can verify the problems inherent to the use of the DID regression in a context
with this kind of spatial shocks in several other ways. First, we compose a simple
table of the means and t-tests of differences for loan size, loan changes, and residualsof loans taken by choosers and non-choosers of the program across the treatment
and the control:

20Comparing Differences Across Treatment and Control:
Non-Choosers
Choosers
TCt-testTC
t-testLoans
113.9 119.8
1.10
117.4.9
110.4-.96
Loan Changes 39.0
14.4 -3.57**
36.0
15.2 -2.28**
Residuals
8.8-14.5 -3.97**
7.06-8.18 -1.99**
While these residuals are not backfitted, this table tells us several things. First, theuse of differencing can exacerbate bias in a spatial DID if the source of bias is spatial
shocks. We see this from the fact that the levels of loans are not significantly different between the treatment and control in the non-choosers, but loan changes andresiduals are significantly different in both groups. Secondly, we see the inefficacyof this vector of controls at removing spatial heterogeneity, despite the fact thatthey are fairly standard and were chosen from a large groups of potential controls
for their explanatory power. Thirdly, under the assumptions in Section 3, we seethat the DID cannot be unbiased when the counterfactual surface (residuals among
non-choosers) shows such strong differences between treatment and control. In thisexample we see that far from being equal to zero, the difference between treatment
and control among non-choosers is stronger than among choosers, leading us tobelieve that the DID coefficient may actually have the wrong sign.
In order to investigate the surprising failure of our vector of controls at removing
spatial heterogeneity, we regressed both changes in loan size and the residuals on aset of district-level dummies. In the former regression the R2 was .073 and in thelatter .065, meaning that according to this rough measure our control variables only
removed ten percent of the spatial heterogeneity. This result may not generalize
to other studies, but it is troubling that this fairly typical battery of controls doessuch a poor job of removing the effects that would bias a spatial treatment/control
setup.
21

To get a clearer picture of the magnitude of these effects, we bootstrap theresidual surface in Figure 4. Not only would we like to know whether the spatial
effects observed are significant, but we would like to know whether there are significant effects at the locations of the choosers. This achieved by matching eachchooser to the residual that is estimated at the location of the closest non-chooser.
We then sample with replacement from the empirical marginal distribution of theresiduals, randomizing over location, and so we bootstrap datasets that are spatially i.i.d by construction. We then run a spatial smoother (a Gaussian smootherwith a bandwidth of .2 standard deviations) over these bootstrapped datasets, andselect the envelope that contains 95% of the smoothed surfaces. Finally, we smooth
our observed nearest-neighbor residuals with the same smoother, and then compare
these pointwise smoothed outcomes with the pointwise smoothed i.i.d. outcomes.
Any observations that lie below the confidence region have experienced a significant
negative residual effect, and any observations above have experienced a positiveeffect.
Figure 5 shows the locations of all of the choosers. Those observations which
experienced insignificant shocks are denoted with an X, and those with significant
shocks are denoted by an arrow pointing in the direction of the effect. It is clear byinspection that the area around and to the west of Kampala, which is the control
region, displays more significantly negative residuals, while residuals in the northernand eastern sections of the country, the treatment, are disproportionately positive.
While the treatment and the control contain six groups each that experienced significant negative effects, the treatment region contains twelve groups that experienced
positive effects, while the control region contains only two. This is consistent with
our prediction of a significant positive treatment effect in the False DID. We thus

22

proceed confident that we do indeed experience significant spatial heterogeneity inour data, and thus the standard DID estimates will be biased (in this case upwards).

VI

Regression Results

The first column in Table IV shows the DID impact estimates for five outcomesunder each of the treatments. The programs appear to have few significant effects,
with the exception of an increase in loan volume under the biweekly treatment,
significant at the 95% level. These will be unbiased estimates of impact only inthe case that no other unexplained spatial effects coincide with the treatment andcontrol regions. To test this, we run the False DID for the same five outcomes inboth programs, and these results are reported in column 2. We reject the absenceof such effects among the group of non-choosers in three out of ten cases, implyingthat significant unexplained spatial phenomena are present. Therefore, the DID
estimator will be biased in this spatial test, and only because the non-choosers
provide us with a counterfactual for these spatial effects are we able to back out an
unbiased estimate of the impact of the programs.
In the cases where the false treatment effect observed is similar to the treatment
effect measured in the DID, we suspect that the DID is picking up only spatial bias,
and there is unlikely to be any real treatment effect. The increase in loan volume
in the biweekly program measured by the False DID, for example, is similar to thatobserved in column 1, implying that all of the ‘treatment effect’ picked up by the
DID is bias. Where we have significant false effects in the FDID which differ fromthose found in the DID, we suspect that the bias in the DID may be masking real
underlying treatment effects.

23

If the spatial mapping of choosers and non-choosers were identical, then we could
get an unbiased treatment estimate by subtracting the coefficient from the second
column off of the first. The spatial matching estimator differs from this tripledifference estimate because of differences in the spatial distributions of the two
populations. Column 3 gives the estimate of the spatial matching estimator using
only the nearest neighbor as a match, and column 4 uses the 16 nearest neighbors.
Column 4 thus uses a larger area to define the ‘local’ shock.
These estimates demonstrate no impact of the biweekly program on loan volume,
despite the significant positive DID estimate. Where we do see significant effects
for the biweekly program are in strongly decreased dropout, and grades that are
somewhat higher. Because these effects are similar to the selection effects seen in
Table III, and the take-up rate in the treatment was weakly lower, some concern
remains that these results could be contaminated by selection bias. While we havenot seen the jump in loan volumes that was predicted by theory, we do observethat these groups which have tailored products to the clients have managed to
become significantly more attractive to current members, and so have improved
retention. The costs of lending are, obviously, dramatically lower when the credit
officers halve the number of meetings they are required to oversee, and so if thistransition leaves loan volumes unchanged and actually improves client quality, itsuggests that extending the option of biweekly repayment to the rest of the country
will both increase the sustainability of the institution and help to tailor products
towards the needs of groups.
Intriguingly, every outcome for which the FDID is significant and the DID is
not is found under the insurance program. The obvious intuitive interpretationis that the insurance program has insulated participants against a shock observed

24

in an uninsured population, which is precisely what we would expect from such atreatment. New client enrollment is weakly lower, dropout weakly higher, and loans
significantly lower for clients within areas offered the insurance treatment who did
not choose it. For those who chose and received the treatment, however, we see
no evidence of these spatial differences, leading us to infer that the treatment has
played a causal role in insulating them.
The insurance program has been strongly effective in attracting new clients, or atleast in avoiding a decrease in enrollment which was otherwise occurring. A study ofindividual clients who have joined groups after they received the insurance productshows that these clients are low-quality borrowers (low grades, small loans, small
growth in loans) and hence are probably participating in FINCA only to get accessto the insurance product. The fact that average default does not increase indicatesthat the screening process continues to be effective in preventing the admissionof deadbeat clients. It is also important, however, that insuring clients against
health expenditure risk creates no worsening in repayment, implying that illness
is not driving default even in this high-mortality environment. The weak decreasein savings and increase in loans is likely driven primarily by the need to pay the
insurance premia at the time when savings and loan volumes are recorded.
We perform two robustness checks. First, we modify a new method of calculating
the variance of matching estimators presented in Abadie & Imbens (2006). Because
we perform the spatial matching without replacement, agents may be used as amatch multiple times, requiring an upwards adjustment in the estimator of thevariance. We re-calculate the standard errors of the spatial matching estimatorusing the square roots of the corresponding diagonal elements of:25(X 0 X)−1

X 1 + KM (i)1
N −K iM2 M(µ̂i − µ̂i0 )2
M +1where N is the number of agents, M is the number of nearest neighbors usedas matches, and KM (i) is the number of times that each control agent is used asa match. The results are presented in Table V; the sample standard errors fromthis method are roughly twice as large as those calculated by the normal method.
Only the decrease in dropout in the biweekly program remains significant at the
95% level, and the increase in new clients for the insurance program falls to 90%
significance. Different FINCA groups often meet at the same location, meaning thatmultiple groups in the parallel population may qualify as a ‘nearest neighbor’. We
dealt with this problem in the data by averaging residuals for all units of a given
status at a given location, but this multiple matching led to a substantial increasein the estimated variance. A study population with a more dispersed, uniform
spatial distribution would likely not see this large difference between standard errors
calculated by the two different methods. The additional uncertainty introduced bymultiple matches to the same units substantially decreases our confidence in the
conclusions, but the main results are still present.
Our second robustness check takes advantage of the fact that for all of our outcomes except savings, we have two pre-treatment observations. This allows us totest the spatial assumption because we can verify whether the spatial shocks incurred by choosers and non-choosers were similar. The results of this exercise arereported in Table VI. Because there are no treatment effects experienced anywherein this population, both of our DID regressions are now false. The first column
reports the False DID among choosers, and the second the False DID among nonchoosers. We see once again that significant spatial phenomena exist that were26

not properly picked up by our control variables. While the number of observations
among choosers is limited, we see that in every case where there are significant
spatial effects among non-choosers, the magnitude of the effects among choosers issimilar. When we run the spatial matching estimator (using the normal SE calculation and M=1) we see that there are no significant differences between the spatial
shocks experienced by these two populations in the 8 months prior to treatment.
We thus fail to reject the spatial assumption.

VII

Conclusion

In the presence of a second control group, we have a way of testing the assumptions underlying the use of a DID estimator of spatial treatment effects. Not only
does the application in this paper display heterogeneity of a type that will result inbias in the DID, but our battery of control variables have been largely ineffective inremoving this heterogeneity. While this result needs to be tested in other data sets,
the implication is that studies which appear to be estimating spatial DID impacts
having controlled for all observable differences between regions may be very sensitive
to any differences in raw growth rates across the space of the treatment criterion.
Particularly when legislative or administrative units are used to define treatment
and control regions, we have myriad reasons to expect that unexplained differences
will exist. Data collection, managerial talent, differing incentive structures, shocks,
and endogenous policy placement can all cause units to differ in unexplained ways
across the treatment rule, and hence the DID will be inconsistent.
Through the use of the spatial matching estimator we can directly measure otherforms of unexplained spatial heterogeneity and recover unbiased impact estimates.
Using the non-choosers of the program to eliminate this spatial heterogeneity, we
27

find the biweekly repayment program improving retention of existing clients while
also improving repayment. Since it lowers transaction costs on both sides of thecontract, our results indicate significant welfare gains from extending the choice of
this program to the rest of FINCA’s groups in Uganda.
Insuring clients against health expenditure risk has no effect on their repayment
performance. Since few environments on earth have a higher incidence of endemic
diseases than Uganda, this is relatively strong evidence for the fact that healthshocks are not a major determinant of microfinance delinquency. The insurance
program retained existing clients more successfully and attracted new ones at amuch greater rate than control groups. In addition, it caused a weak drop in savings
and increase in loans. It is very likely that the insurance caused increases in thehousehold welfare of participants, however the program as currently constituted
represents a mixed blessing from the perspective of the lender. Increasing debt
loads and decreasing savings also indicate that the financial burdens of paying forthe insurance policy may be undermining the economic self-sufficiency which shouldbe the ultimate goal of microfinance.
The impact of these programs is closely related to the manner in which groups
choose whether or not to accept them, and hence to the difference between the average treatment effect and the treatment effect on the treated. We have strong reason
to suspect that the ATE of the biweekly repayment program would be negative,
particularly in terms of repayment performance. What this experiment shows isthat as long as a mechanism exists to expose group members to the negative repercussions of their choices (in this case, joint liability), then the groups themselves
will make the correct decisions regarding insurance and risk. The more mixed success of the insurance program illustrates these same concepts. Insured groups were28

able to accept a large number of new clients who appeared less attractive without
sustaining a drop in repayment, indicating an ability to overcome the asymmetric
information present in the lending contract. The insurance program itself, however, suffered from adverse selection in client health, huge cost overruns, and useof the system which was dramatically higher than predicted. Because FINCA’s
joint liability contract did not expose the groups to any health-related asymmetric
information costs, local information was not used to overcome these problems. If
we wished to learn the lessons of microfinance, a financially sustainable insurance
program might include features like a joint co-payment to be made collectively by
all members of a group; this will mobilize local information and induce agents toscreen on health quality.
It has become increasingly clear that program evaluation needs to be built into
the design of programs in order for us to have any hope of measuring their effects
accurately. In many contexts, the best way of doing this is to randomize some
aspect of the design or implementation of the program. What is suggested here isa different path; we show that the use of a simple rule for the treatment criterion
presents us with a measurable dimension along which we need to worry about bias.
Because this dimension can be used for matching purposes, we can generate highquality controls in situations where a second control group is present and assignment
into the treatment is based on easily observable criteria. The implication is that,in environments where randomization is not feasible, a spatial testing design withtransparent eligibility requirements is an alternate way of producing high-quality
impact estimates.

29

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31

VIII

Tables

I: Variables Used in the Analysis:
Outcome Variables:
1. Dropout (percent that took a loan last cycle and do not return)
2. New clients (percent of clients starting this cycle that are new)
3. Grades (repayment performance and meeting attendance)
4. Average loans in a village bank
5. Average savings in a village bankControl Variables:
1. Loan cycle number (e.g. loans taken by this VB)
2. Ethnic homogeneity of the group
3. Borrower’s perception of their local business climate
4. A dummy equal to one if the VB is in a rural area
5. The average number of children in clients’ households
6. The average number of non-working adults in clients’ households
7. The share of clients in a VB that own their own homes
8. Does the VB conduct other informal internal savings and lending
9. Did the group pre-exist in some form prior to formation of the VB

32

II: Numbers of Groups in Treatment and Selection Categories:
Biweek:Selection
Criterion

ω=0
ω=1
Total

Treatment Criterion
T =0
T =1
102
168
51
59
153
227

Total
270
110
380

ω=0
ω=1
Total

Treatment Criterion
T =0
T =1
140
91
99
18
239
109

Total
231
117
348

Insurance:

Selection
Criterion

33

III: T-tests of Differences in Means Across the Treatment and Selection
Criteria:
Treatment Criterion
Selection Criterion(Mean difference between (Mean difference between
treated & untreated)chooser & non-chooser)
Exogenous:
BiweekInsurance
BiweekLocated in Village
0.0334-0.1285**-0.1418**
Cycle No. of Group
0.6935**-0.0859
0.2689Group conducts ROSCA-0.0106-0.0133-0.0106
Ethnic Heterogeneity
0.08810.0867-0.0279
Perceived Econ. Climate-0.0502
0.2185**0.2885**
No. of Children in HH.
0.10880.1643-.1019No. of Adults in HH.
0.1739**-0.0829-0.0345
Own Home?
0.00960.02370.0081Pre-existing Group
0.0111-0.0199-0.0606
Endogenous:(Pre-treatment)% Dropout
0.1581-0.3488-0.8554**% New Clnts-0.5844-0.1820-0.1757
Av. Ind. Loans, USD-11.712**12.0221**-1.874
Av. Ind. Savings, USD -12.0557**
16.4137**-0.4804
Grades, A=4, D=1-0.04180.08840.3845**(**=Difference in means significant at 95% level.)

34

Insurance-0.0073
0.8595**0.1042**-0.1762**-0.10480.1996**0.2842**-0.0231-0.0157-0.4072-0.7421-6.2119-0.4287
0.0018Biweekly: # obs:
% New Clients:

IV: Regression Results:
False
Difference- DifferenceSpatial
ininMatching
Differences Differences
M=1
110
270
380
-5.3331.2736-2.4280(-1.0223)(.0890)(-.7521)

SpatialMatching
M=16380-.4867(-.1818)% Dropout:-5.0194(-1.2097)

3.0012(1.2474)-12.9544** -9.5690**(-4.7618) (-4.5962)

Savings (USD):-4.9995(-1.1161)-9.3477(-1.0105)13.3042(1.4288)8.0221(1.1692)

Loans (USD):

17.5045**(2.0508)

24.6750**(4.0369)

2.8716(.4455)-3.8805(-.7796)

Grades (A=4, D=1):-0.0674(-.4842)-.0403(-.4418).2468 **
(2.4766).0743(.9671)

Insurance: # obs:
% New Clients:

117
.2263
(.0549)231-3.6515(-1.6399)

348
5.2698**(2.1727)348
3.8479**(1.9612)% Dropout:

2.5454(.508)

4.6773*(1.6934)

6.5050**(2.0535)-1.5620(-.6322)

Savings (USD):

0.4842(.0787)12.9900(1.2227)-10.4638(-1.2494)-12.9625(-1.6056)

Loans (USD):-4.6143(-.4485)-14.7495**(2.1586)4.2655(.5716)

9.0664*(1.6566)

Grades (A=4, D=1):

.2357
.0195
-.0598-.0243(1.3368)(.2104)(-.5621)(-.2832)(t-statistics in parentheses, *=90% significance, **=95% significance)35

V: Regression Results using Robust Variance Estimator:

Biweekly:# obs:% New Clients:% Dropout:

SpatialSpatialMatching Matching
M=1
M=16
380
380
-2.4280-.4867(-.3955)(-.0867)-12.9544* -9.5690**(-1.7730) (-2.0624)

Savings (USD):

13.3042(.8912)8.0221(.6094)Loans (USD):

2.8716(.1842)-3.8805( -.3860)

Grades (A=4, D=1):.2468(.9105).0743(.4311)348
5.2698(.9924)348
6.8398*(1.6609)% Dropout:

6.5050(.7695)-1.5620(-.2858)

Savings (USD):-10.4638(-1.0575)-12.9625(-.8947)

Loans (USD):

4.2655(.3129)9.0664(.8164)

Insurance:# obs:% New Clients:

Grades (A=4, D=1):-.0598-.0243(-.1838)(-.1304)(t-statistics in parentheses, *=90% significance, **=95% significance)36VI: Counterfactual Test of Spatial Assumption:(False Impact Estimates)
Choosers Non-Choosers False Spatial
False DID
False DID
Matching
Biweekly:# obs:
72
162
234% New Clients:-4.6611-4.0120*-3.0326(-1.4165)(-1.7716)(-1.1252)% Dropout:-.2362(-.0415)

4.9902(1.4189)-2.2653(-.5778)

Loans (USD):

8.0202(1.1398)

12.2790**(3.5661)-2.3783(-.5098)

Grades (A=4, D=1):-.0387(-0.1554)-.0039(-.0314)-.0066(-.0423)61
1.7701(.3329)173-1.0621(-.5213)234-.0663(-.0313)% Dropout:4.3708(.6838)-.3149(-.0907)2.5592(.6696)Loans (USD):-9.8486(-1.0493)-11.1089**(-3.2083)-1.6184(-.3545)

Insurance:# obs:% New Clients:

Grades (A=4, D=1):.0908.2259*-.1672(.3328)(1.7591)(-1.3548)(t-statistics in parentheses, *=90% significance, **=95% significance)

37

IX

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Figure 1: Treatment-control regimes: Circle=control, Square=Health Treatment
offered, Triangle=Flexibility Treatment offered38

Figure 2: Spatial distribution of Loan Sizes

39

Figure 3: Spatial distribution of Loan Changes

40Figure 4: Spatial distribution of Loan Change Residuals

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 $#  !
 "#     ) 9 + 4 9 +  %&'3 )4 3 +0 5+(6
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 

6486556760 5+5/(6.+49249)

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0 + 7 + .+  
4=+.+1)8+05+*+*+.+ (+ 4 9+ (+     . + ( )7 )> 2.=286*+
 

Figure 5: Shocks at the locations of the choosers; X=insignificant shock, and anarrow indicates the direction of significant shocks

42.+,-12*; +