Microfinance and Home Improvement:
Using Retrospective Panel Data to Measure
Program Effects on Discrete Events
Bruce Wydick
Professor of Economics, University of San Francisco
Visiting Professor , UC Santa Barbara
joint with
Craig McIntosh
University of California at San Diego
Gonzalo Villaran
University of San Francisco
Background:
• Microfinance Summit: As of January 2006,
3,133 microcredit institutions have reported
reaching 113,261,390 clients, 81,949,036 of
whom were among the poorest when they
took their first loan.
• Still amazing that don’t have robust results of
positive microfinance impact (Armendáriz de
Aghion and Morduch, 2005).
• Recent renewed emphasis on program impact
appraisal (e.g. Easterly, 2006; Center for
Global Development, 2006)
An “evaluation gap” has emerged because
governments, official donors, and other funders
do not demand or produce enough impact
evaluations and because those that are conducted
are often methodologically flawed.”
--Center for Global Development (Saveduff,
Levine, Birdsall, 2006 with E. Duflo, P. Gertler,
etc.)
Problems with lack of quality impact studies:
1. Accurately measuring program impacts has
historically been logistically difficult, time
consuming, and costly.
Problems with lack of quality impact studies:
1. Accurately measuring program impacts has
historically been logistically difficult, time
consuming, and costly.
2. Many institutions would like to evaluate the
effectiveness of their programs ex-post to
implementation, creating problems with the
establishment of baseline surveys, control groups,
and other means of identification.
3. Use of instruments or program rules (e.g. Pitt
and Khandker, 1998) to obtain program impacts
is theoretically appealing, but practically
problematic:
•
•
If available, instrumental variables will differ
from one situation to the next.
Finding instruments in a particular context
strongly correlated with program access, but
uncorrelated with impact variables, requires
substantial ingenuity.
Point: complicates use of a standardized
instrumental variable approach.
4. Matching Models -- creating artificial controls in
order to identify treatment effects.
(e.g. propensity scores, nearest neighbor, etc.)
4. Matching Models -- creating artificial controls in
order to identify treatment effects.
(e.g. propensity scores, nearest neighbor, etc.)
Gomez and Santor (2003) use statistical matching
model to identify the effect of group lending
relative to individual lending among 1389
individual and group borrowers among 1,389
borrowers in Canadian lending institution.
4. Matching Models -- creating artificial controls in
order to identify treatment effects.
(e.g. propensity scores, nearest neighbor, etc.)
Gomez and Santor (2003) use statistical matching
model to identify the effect of group lending
relative to individual lending among 1389
individual and group borrowers among 1,389
borrowers in Canadian lending institution.
Problem: Cannot control for unobservables.
5. Randomized experiments--become very popular
as way of ascertaining impact of development
programs.
• Maximum degree of exogeneity in treatment and
control, allowing means of overcoming selfselection, endogeneity, and omitted variable bias
(common to microfinance)
• Most elegant way of ascertaining impacts, and
least controversial.
Difficulties:
a) To create control group needed for identification of
treatment, necessary that treatment withheld for some
who desire it so impact can be measured on treatment
group relative to the control…often undesirable or
infeasible
Difficulties:
a) To create control group needed for identification of
treatment, necessary that treatment withheld for some
who desire it so impact can be measured on treatment
group relative to the control…often undesirable or
infeasible
b) Some treatments (e.g. microfinance) may take years
to realize full effects on household--timeframe may not
intersect with time one can “hold off” control
group…"bleeding" of control group.
Difficulties:
a) To create control group needed for identification of
treatment, necessary that treatment withheld for some
who desire it so impact can be measured on treatment
group relative to the control…often undesirable or
infeasible
b) Some treatments (e.g. microfinance) may take years
to realize full effects on household--timeframe may not
intersect with time one can “hold off” control
group…"bleeding" of control group.
c) To avoid bleeding of control group, often short-term,
but then only capture effects of initial adopters.
d) Point estimates from randomized experiments are
subject to influence of time-specific economic shocks
occurring within the relatively narrow timeframe of the
experiment…understates true standard errors.
e) Because randomized field experiments typically
represent a snapshot of program impact over a short
time frame, they are often unable to capture important
dynamics of treatment impact.
Ideally, we would like to understand how an
intervention affects a treatment group over time.
Our paper presents a methodology for ascertaining
welfare changes brought about by development
programs that may be applicable in a variety of
contexts (explain later).
Main Advantages:
•Uses a single wave of cross-sectional surveying.
•Impact evaluation can be undertaken ex-post.
•No firm requirement for standard control group.
•Allows for a dynamic analysis of impacts
Our methodology appropriate when…
• Program has existed for a number of years.
• Has been phased in over time in different
geographical regions or identifiably separate
populations for reasons that are independent
of dependent variables.
• Stable populations with little geographical
movement.
Methodology uses a single cross-sectional
survey to create a retrospective panel data set
based on discrete, memorable events in the
history of households.
e.g. install indoor plumbing, new house,
purchase of first cell phone, miscarriages,
infant deaths, land purchases etc.
Identification of impact rests in analyzing the
timing of these events with respect to the
timing of treatment.
Test is for differences in the probability of these
major events within window surrounding the
treatment.
(Post vs. Pre--under conditions of exogeneity)
We apply methodology to studying the effects of a
microfinance program in rural Guatemala on home
improvements
We apply methodology to studying the effects of a
microfinance program in rural Guatemala on home
improvements
Study discrete changes in the probability of major
dwelling improvements, upgrades of walls, roofs,
floors, the installation of indoor toilets, and the
purchase of new land + compilation of these.
We apply methodology to studying the effects of a
microfinance program in rural Guatemala on home
improvements
Study discrete changes in the probability of major
dwelling improvements, upgrades of walls, roofs,
floors, the installation of indoor toilets, and the
purchase of new land + compilation of these.
Use linear probability estimator that incorporates
household and year fixed-effects. (Chamberlin, 1980)
Sneak Preview of Results:
Microfinance loans for enterprise expansion is likely
to exhibit significant, positive effects on some
dwelling upgrades, especially to walls & floors.
Roofs uncertain.
Apparently not for toilets and land.
Identification of impacts is achieved through
the existence of counterfactual, i.e. what
would have happened to treatment group in
the absence of a particular treatment.
Counterfactual in a randomized field
experiment in microfinance is the resulting
level or change in impact variables realized
within a subset of borrowers in the control
group who desired credit but were prevented
by researchers from receiving it.
Counterfactual that yields identification in our
methodology is difference in probability of discrete
events among those who received the treatment in
separate years, controlling for these differences in
years with village- and year-level fixed-effects.
Main contributions:
1. Offer a sequence of steps that include diagnostics
on the data to check for supply-side & demand-side
endogeneities in the rollout of a program.
2. Establish framework for thinking about when and
how retrospective panel data can be used in impact
analysis.
3. When data meets certain diagnostic criteria, allows
us to examine the dynamics over probability of
these discrete events before and after treatment &
test for significance of a type of treatment effect.
Steps involved in methodology:
Part A: Survey
Steps involved in methodology:
Part A: Survey
Step S1: Identify a program that has been phased in
over a number of years in different
geographical areas or among different
populations.
Steps involved in methodology:
Part A: Survey
Step S1: Identify a program that has been phased in
over a number of years in different
geographical areas or among different
populations.
Step S2: Carry out random survey of program
participants who have been given access to
the treatment in different time periods.
Steps involved in methodology:
Part A: Survey
Step S1: Identify a program that has been phased in
over a number of years in different
geographical areas or among different
populations.
Step S2: Carry out random survey of program
participants who have been given access to
the treatment in different time periods.
Step S3: Identify discrete historical changes with a
theoretical basis for causality from the
treatment & create historical panel.
Steps involved in methodology:
Part A: Survey
Step S1: Identify a program that has been phased in
over a number of years in different
geographical areas or among different
populations.
Step S2: Carry out random survey of program
participants who have been given access to
the treatment in different time periods.
Step S3: Identify discrete historical changes with a
theoretical basis for causality from the
treatment & create historical panel.
E.g. fresh water → reduced infant mortality
Steps involved in methodology:
Part A: Survey
Step S1: Identify a program that has been phased in
over a number of years in different
geographical areas or among different
populations.
Step S2: Carry out random survey of program
participants who have been given access to
the treatment in different time periods.
Step S3: Identify discrete historical changes with a
theoretical basis for causality from the
treatment & create historical panel.
E.g. fresh water → reduced infant mortality
E.g. smallpox vaccine → lower instances of smallpox
Steps involved in methodology:
Part A: Survey
Step S1: Identify a program that has been phased in
over a number of years in different
geographical areas or among different
populations.
Step S2: Carry out random survey of program
participants who have been given access to
the treatment in different time periods.
Step S3: Identify discrete historical changes with a
theoretical basis for causality from the
treatment & create historical panel.
E.g. fresh water → reduced infant mortality
E.g. smallpox vaccine → lower instances of smallpox
E.g. microcredit access → higher enterprise profits →
more rapid home improvements
Steps involved in methodology:
Part B: Econometrics
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program.
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program.
Step E2: Estimation of the Retrospective Intention
to Treat Effect
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program.
Step E2: Estimation of the Retrospective Intention
to Treat Effect
Step E3: Testing for Demand-Side Endogeneity
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program.
Step E2: Estimation of the Retrospective Intention
to Treat Effect
Step E3: Testing for Demand-Side Endogeneity
Step E4: Estimation of the Take-up Effect
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program.
Step E2: Estimation of the Retrospective Intention
to Treat Effect
Step E3: Testing for Demand-Side Endogeneity
Step E4: Estimation of the Take-up Effect
Step E5: Treatment Window Regression and F-test
of Take-up Effects
2005 (BASIS/USAID funded) survey of 218
households located in 14 different villages near
Quetzaltenango, Guatemala.
• MFI: Fe y Alegria: 3,000 new clients/year
• Questionnaire ascertained changes in different
categories of dwelling improvement: upgrades to
walls, roofs, floors, plumbing, and increases in
land.
• Each borrower was asked about changes in these
variables during the history of the household, and
the timing of these changes.
Table 1A: Frequencies of Dwelling Type
(Pre- and Post- Credit)
block
finished adobe
adobe
wood
total**
--- Pre-Credit ( t  1) --obs.
percent
106 (96)*
52.5 (51.9)
22 (19)
10.9 (10.3)
61 (57)
30.2 (30.8)
13 (13)
6.4 (7.0)
202 (185)
100.0 (100.0)
--- Post-Credit ( t  1) --obs.
percent
113
61.1
18
9.7
45
24.3
9
4.8
185
100.0
Roof
concrete
tile
corrugated iron
palm leaves
total
--- Pre-Credit ( t  1) --27 (22)
13.4 (11.9)
51 (46)
25.2 (24.9)
122 (115)
60.4 (62.2)
1 (1)
0.5 (0.5)
202 (185)
100.0 (100.0)
--- Post-Credit ( t  1) --31
16.8
44
23.8
109
58.9
1
0.5
185
100.0
Floor
tile
concrete
dirt
--- Pre-Credit ( t  1) --25 (23)
12.4 (12.4)
118 (108)
58.3 (58.4)
58 (53)
28.7 (28.6)
202 (185)
100.0 (100.0)
--- Post-Credit ( t  1) --26
14.05
114
61.6
45
24.32
185
100
Walls
total*
--- Pre-Credit ( t  1) ---
Toilet
indoor plumbing
outhouse
total
Land
mean: cuerdas***
standard
deviation
obs.
97 (87)
99 (92)
202
48.0 (47.0)
49.0 (49.7)
100.0
--- Pre-Credit ( t  1) --mean & std. dev
195 (178)
2.962 (2.940)
3.85 (3.73)
obs.
99
82
185
--- Post-Credit ( t  1) --percent
53.51
44.3
100.0
--- Post-Credit ( t  1) --mean & std. dev
178
3.041
3.72
* values in parenthesis exclude borrowers receiving credit in 2005 who do not appear in final columns
** totals may not equal category sum due to unrecorded observations for individual categories
*** equals approximately 25 x 25 meters
Table 1B: Summary Statistics of Variables
Variable
Mean
Dependent Vars.:
New Walls
0.0213
New Roof
0.00875
New Floor
0.0220
New Toilet
0.0171
New Land
0.0402
Home Improvmnt.
0.1481
Control Variables:
Educ. Men (Years)
4.06
Educ. Wm (Years)
2.41
Age--Male
35.03
Age--Female
31.01
Initial Land
2.60 cuerdas
Retail
0.751
Livestock
0.90
Manufacturing
0.406
Dates of Credit Introduction into
Villages (no. of households/village):
Std. Deviation
Max
Min
0.1446
0.0931
0.1469
0.1298
0.5948
0.3552
1
1
1
1
1
0
0
0
0
0
3.61
3.12
9.60
8.86
3.62
15
18
75
63
20
0
0
14
19
0
V1: 2001 (20); V2: 2001 (3); V3: 1998 (47); V4: 1998 (10); V5: 2000 (40);
V6: 2000 (4); V7: 2004 (3); V8: 2001 (3); V9: 2000 (6); V10: 1999(14);
V11: 1998 (8); V12: 1999 (9); V13: 1995 (2); V14: 1993 (31).
Empirical Steps:
Step E1: Check for supply-side endogeneity in
the rollout of a program.
Diagnostics:
1A: Is there endogeneity in the levels of the pretreatment outcome?
(Regress average pre-treatment outcome on the year
in which credit was offered to the village.)
Empirical Steps:
Step E1: Check for supply-side endogeneity in
the rollout of a program.
Diagnostics:
1A: Is there endogeneity in the levels of the pretreatment outcome?
(Regress average pre-treatment outcome on the year
in which credit was offered to the village.)
1B: Is there endogeneity in the pre-treatment trend?
(Regress average of the 1st difference of the pretreatment outcome on year credit offered.)
Empirical Steps:
Step E1: Check for supply-side endogeneity in
the rollout of a program.
Diagnostics:
1A: Is there endogeneity in the levels of the pretreatment outcome?
(Regress average pre-treatment outcome on the year
in which credit was offered to the village.)
1B: Is there endogeneity in the pre-treatment trend?
(Regress average of the 1st difference of the pretreatment outcome on year credit offered.)
1C. Is the rollout endogenous to shocks?
(Run fixed effects using only pre-treatment data with
dummy for 1st lead of year credit offered.)
Table 2: Tests for Supply-Side Endogeneity
1A. Is there endogeneity in the levels of the pre-treatment outcome? (Regress average
pre-treatment outcome on the year in which credit was offered to the village.)
Year of rollout
Observations
R-Squared
New Walls
-0.0018
(0.003)
14
0
New Floor
0.0025
(0.004)
14
0.04
New Roof
0.0002
(0.001)
14
0
New Toilet
0.0013
(0.001)
14
0.21
New Land
0.0111
(0.010)
14
0.04
1B. Is there endogeneity in the pre-treatment trend? (Regress average of the 1st difference of
the pre-treatment outcome on year credit offered.)
Year of rollout
Observations
R-Squared
New Walls
0.0006
(0.001)
14
0.02
New Floor
0.0011
(0.002)
14
0.06
New Roof
-0.0001
(0.000)
14
0
New Toilet
0.0001
(0.000)
14
0.08
New Land
0.0110
(0.012)
14
0
1C. Is the rollout endogenous to shocks? (Run FE regression using only pre-treatment data w/
dummy for 1st lead of year credit offered.)
ITE lead 1
Observations
R-Squared
New Walls
0.0253
(0.018)
887
0.01
Robust standard errors in parentheses.
New Floor
-0.0066
(0.014)
1215
0.02
New Roof
0.0014
(0.009)
1191
0.01
New Toilet
-0.0087
(0.023)
956
0.06
New Land
0.0119
(0.029)
1318
0.04
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program. ✔
Step E2: Estimation of a Retrospective Intention to
Treat Effect
Table 3A—Intention to Treat Effect
(1)
newwalls
Credit Prog. Available
(2)
newroof
(3)
newfloor
(4)
newtoilet
(5)
newlandd
0.039**
0.003
-0.012
0.004
0.031
(0.019)
(0.012)
(0.014)
(0.017)
(0.024)
Constant
-0.005
0.023
0.029
0.031
0.028
(0.032)
(0.015)
(0.017)
(0.019)
(0.030)
Observations
1159
1359
1991
1298
2359
R-squared
0.04
0.01
0.01
0.03
0.03
Robust standard errors in parentheses. Estimation uses year and village-level fixed effects.
* significant at 10%; ** significant at 5%; *** significant at 1%
(6)
homeimprv
0.060
(0.039)
0.028
(0.050)
2359
0.04
Table 3B—Intention to Treat Effect with Individual Characteristics
(1)
newwalls
Credit Prog. Available
(2)
newroof
(3)
newfloor
(4)
newtoilet
(5)
newlandd
0.201
0.055
0.054
-0.077
0.043
(0.202)
(0.106)
(0.115)
(0.143)
(0.116)
education father
0.001
-0.000
0.003
-0.000
0.004
(0.002)
(0.002)
(0.003)
(0.002)
(0.004)
education mother
-0.002
0.003*
-0.002
-0.001
0.003
(0.003)
(0.002)
(0.003)
(0.002)
(0.005)
age of father
-0.003
0.004
0.001
0.002
-0.026***
(0.005)
(0.005)
(0.005)
(0.005)
(0.006)
age father squared
4.0e-05
-3.8e-05
-5.3e-06
-6.5e-05
2.8e-04***
(5.9e-05)
(7.6e-5)
(6.1e-05)
(7.7e-05)
(7.8e-05)
initial land (cuerdas)
-0.002
-0.000
-0.001
-0.000
-0.002
(0.002)
(0.003)
(0.002)
(0.002)
(0.005)
retail
-0.006
-0.002
-0.013
-0.034
0.049*
(0.022)
(0.008)
(0.022)
(0.027)
(0.025)
livestock
0.019
0.026
0.005
-0.024
-0.006
(0.026)
(0.024)
(0.029)
(0.025)
(0.029)
educ father*program
-0.009*
0.001
-0.003
0.005
-0.008*
(0.005)
(0.004)
(0.002)
(0.003)
(0.004)
educ mother*program
0.008
-0.001
0.001
0.013*
0.001
(0.007)
(0.004)
(0.003)
(0.006)
(0.005)
age father*program
-0.007
-0.003
-0.001
-0.002
0.005
(0.011)
(0.005)
(0.006)
(0.008)
(0.006)
age father^2*program
6.9e-05
3.1e-05
3.8e-05
8.4e-05
-7.6e-05
(1.2e-04)
(7.3e-05)
(6.4e-05)
(1.1e-04)
(6.2e-05)
initial land*program
0.005
-0.000
-0.000
-0.002
-0.000
(0.003)
(0.002)
(0.002)
(0.002)
(0.004)
retail*program
-0.016
0.018
-0.006
0.042
-0.059*
(0.041)
(0.012)
(0.029)
(0.041)
(0.033)
livestock*program
0.110*
-0.011
-0.010
0.066
-0.040
(0.055)
(0.040)
(0.050)
(0.046)
(0.028)
constant
0.076
-0.094
0.004
0.050
0.500***
(0.086)
(0.070)
(0.099)
(0.062)
(0.119)
Observations
817
1035
1421
947
1701
Number of Villages
13
13
14
14
14
R-squared
0.07
0.02
0.02
0.05
0.08
Robust standard errors in parentheses. Estimation uses year and village-level fixed effects.
* significant at 10%; ** significant at 5%; *** significant at 1%
(6)
homeimpr
0.161
(0.102)
0.004
(0.005)
0.000
(0.004)
-0.024***
(0.007)
2.5e-04***
(8.6e-05)
-0.002
(0.006)
0.022
(0.037)
-0.009
(0.040)
-0.013**
(0.005)
0.004
(0.004)
0.001
(0.005)
2.6e-07
(5.4e-05)
0.001
(0.005)
-0.046
(0.048)
-0.037
(0.050)
0.476***
(0.114)
1701
14
0.06
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program. ✔
Step E2: Estimation of the Retrospective Intention
to Treat Effect ✔
Step E3: Testing for Demand-Side Endogeneity
We estimate the following equation:
N
yit  v j   t    n X n 
n 1
k

t t   k
T
i , t  t i ,t  t
 uit
(1)
where yit is a bivariate dependent variable that is equal
to 1 if household i has housing upgrade in year t.
vj is a village-level fixed effect,
t is a year-level fixed effect, Xn are controls
uit is an error term, and treatment dummy variable T is
equal to 1 if household i first received a microfinance
loan (or began receiving remittances) t  t periods
“ago,” and zero otherwise.
Data Set Example:
Obs. HH Year Toilet? Credit?
11. | 3 2003
0
0
12. | 3 2004
0
0
13. | 3 2005
0
1
14. | 4 2000
0
0
15. | 4 2001
0
0
16. | 4 2002
1
0
17. | 4 2003
0
0
18. | 4 2004
0
1
19. | 4 2005
0
1
t-2
1
.
.
0
0
1
0
.
.
t-1
0
1
.
0
0
0
1
0
.
t=0
0
0
1
0
0
0
0
1
0
t+1
.
0
0
.
0
0
0
0
1
t+2
.|
.|
0|
.|
.|
0|
0|
0|
0|
...which can be adjusted for
demand-side endogeneity:
N
yit  v j   t    n X n 
n 1
1
k

t t   k
pre-treatment
interactive term
T
i ,t  t i ,t  t

t t   k

T
i ,t  t i , t  t i ,t  t
 uit (2)
where yit is a bivariate dependent variable that is equal
to 1 if household i has housing upgrade in year t.
vj is a village-level fixed effect,
t is a year-level fixed effect, Xn are controls
uit is an error term, and treatment dummy variable T is
equal to 1 if household i first received a microfinance
loan (or began receiving remittances) t  t periods
“ago,” and zero otherwise.
Reason: Demand-side Endogeneity
Suppose borrowing is an endogenous
decision because people borrow in good
economic times
→ creates upward bias, δ’s > 0
Suppose borrowing is an endogenous
decision because people borrow when they
are in difficult economic times
→ creates downward bias, δ’s < 0
Table 4—Test for Demand Endogeneity with Five-Year Credit Treatment Window
(1)
(2)
(3)
(4)
(5)
newwalls newroof
newfloor
newtoilet
newland
fyrcreditplus2
0.077*
0.018
0.085*
-0.031
0.028
(0.044)
(0.044)
(0.040)
(0.036)
(0.125)
fyrcreditplus1
0.141
0.032
0.040
0.028
-0.008
(0.119)
(0.037)
(0.034)
(0.045)
(0.080)
fyrcredit
0.059
-0.015
0.030
0.083
-0.006
(0.068)
(0.015)
(0.026)
(0.062)
(0.049)
fyrcreditminus1
0.039
-0.015
0.027
0.054
0.029
(0.059)
(0.015)
(0.039)
(0.045)
(0.067)
fyrcreditminus2
-0.065
-0.026
0.000
0.013
-0.068**
(0.042)
(0.021)
(0.011)
(0.026)
(0.025)
noprogcredminus1
-0.014
0.005
-0.019
-0.096
0.429
(0.079)
(0.022)
(0.038)
(0.060)
(0.495)
noprogcredminus2
0.052
0.079
0.035
0.060
0.039
(0.077)
(0.061)
(0.050)
(0.069)
(0.042)
education father
-0.004
0.001
0.000
0.002
-0.009*
(0.003)
(0.002)
(0.002)
(0.003)
(0.005)
education mother
0.003
0.003
-0.001
0.005***
0.002
(0.005)
(0.002)
(0.003)
(0.002)
(0.005)
age of father
-0.009
0.000
0.001
-0.008
0.005
(0.008)
(0.003)
(0.002)
(0.010)
(0.006)
age father squared
9.8e-05
5.5e-06
-1.8e-05
1.2e-04
-5.8e-05
(9.3e-05) (3.6e-05) (2.5e-05)
(1.5e-04)
(7.0e-05)
initial land (cuerdas)
-0.001
0.000
-0.002
-0.000
0.002
(0.003)
(0.001)
(0.001)
(0.002)
(0.004)
retail
-0.010
0.008
-0.014
0.003
-0.044
(0.016)
(0.009)
(0.018)
(0.024)
(0.087)
livestock
0.058
0.032*
-0.001
0.027
-0.088
(0.038)
(0.017)
(0.020)
(0.030)
(0.085)
Constant
0.164
-0.036
0.060
0.102
-0.024
(0.195)
(0.066)
(0.054)
(0.128)
(0.088)
Observations
611
769
992
729
1185
F-stat for Dem Endog.
0.11
1.46
0.05
0.16
0.91
p-value
0.747
0.250
0.821
0.698
0.358
Number of Villages
13
13
14
14
14
R-squared
0.09
0.04
0.02
0.07
0.02
Robust standard errors in parentheses. Estimation uses year and village-level fixed effects.
* significant at 10%; ** significant at 5%; *** significant at 1%
(6)
homeimprv
0.025
(0.051)
0.047
(0.073)
0.085*
(0.045)
0.033
(0.040)
-0.029
(0.036)
0.052
(0.098)
0.047
(0.051)
-0.006**
(0.002)
0.002
(0.002)
-0.001
(0.006)
3.8e-05
(7.4e-05)
0.001
(0.003)
-0.007
(0.026)
0.003
(0.036)
0.097
(0.119)
1185
0.94
0.349
14
0.03
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program. ✔
Step E2: Estimation of the Retrospective Intention
to Treat Effect ✔
Step E3: Testing for Demand-Side Endogeneity ✔
Step E4: Estimation of the Take-up Effect
Table 5A—Test for Take-up Effect
Credit Taken
Constant
Observations
No. of villages
R-squared
(1)
(2)
(3)
(4)
(5)
(6)
newwalls
0.066**
(0.032)
-0.032
(0.038)
1159
13
0.04
newroof
0.031
(0.024)
-0.005
(0.015)
1359
13
0.02
newfloor
0.017*
(0.010)
0.001
(0.009)
1991
14
0.01
newtoilet
0.000
(0.043)
0.035
(0.040)
1298
14
0.03
newland
-0.016
(0.025)
0.064***
(0.019)
2179
14
0.01
homeimprv
-0.041
(0.029)
0.129***
(0.024)
2359
14
0.04
Table 5B—Test for Take-up Effect with Individual Characteristics
(1)
(2)
(3)
(4)
(5)
newwalls
newroof
newfloor
newtoilet
newlandd
credit
-0.156
-0.203
-0.081
-0.256
0.037
(0.347)
(0.171)
(0.119)
(0.363)
(0.203)
edufather
-0.002
-0.001
0.002
0.003
-0.003
(0.002)
(0.002)
(0.002)
(0.003)
(0.006)
edumother
-0.001
0.001
-0.001
0.003
-0.000
(0.003)
(0.002)
(0.002)
(0.002)
(0.006)
agefather
-0.012
-0.001
-0.001
0.001
0.005
(0.008)
(0.003)
(0.002)
(0.005)
(0.005)
agefathersquared
1.3e-04
-6.0e-05
1.0e-05
-4.4e-05
-5.7e-05
(9.0e-05)
(3.3e-3)
(2.8e-05)
(8.1e-05)
(7.1e-05)
initialcuerdas
-0.001
-0.000
-0.001
-0.000
0.002
(0.003)
(0.001)
(0.001)
(0.003)
(0.004)
retail
-0.027
0.007
-0.022**
-0.021
-0.131*
(0.029)
(0.008)
(0.009)
(0.019)
(0.067)
livestock
-0.007
0.012
-0.006
-0.006
-0.152*
(0.024)
(0.019)
(0.020)
(0.028)
(0.081)
edufather*credit
-0.002
0.005
-0.001
0.001
-0.016
(0.009)
(0.007)
(0.004)
(0.005)
(0.012)
edumother*credit
0.009
0.007
-0.000
0.006
0.008
(0.009)
(0.007)
(0.004)
(0.007)
(0.006)
agefather*credit
0.007
0.007
0.005
0.005
-0.005
(0.012)
(0.005)
(0.004)
(0.016)
(0.010)
agefathers^2*credit
-8.1e-05
-6.0e-05
-5.8e-05
1.8e-06
3.4e-05
(1.1e-04)
(4.8e-5)
(3.7e-05)
(2.0e-04)
(1.1e-05)
initialland*credit
0.002
-0.001
-0.002
-0.006
0.006
(0.010)
(0.002)
(0.002)
(0.007)
(0.007)
retail*credit
0.054
0.019
0.018
0.051
0.168**
(0.039)
(0.020)
(0.018)
(0.076)
(0.060)
livestock*credit
0.329**
0.045
0.024
0.082
0.165
(0.133)
(0.070)
(0.056)
(0.082)
(0.106)
Constant
0.263
-0.003
0.032
0.066
0.070
(0.184)
(0.055)
(0.058)
(0.102)
(0.113)
Observations
779
1035
1421
947
1608
Number of local
13
13
14
14
14
R-squared
0.09
0.03
0.02
0.05
0.02
Robust standard errors in parentheses. Estimation uses year and village-level fixed effects.
* significant at 10%; ** significant at 5%; *** significant at 1%
(6)
homeimprv
-0.725***
(0.240)
-0.002
(0.004)
0.004
(0.003)
-0.031***
(0.007)
3.2e-04***
(9.1e-05)
-0.002
(0.004)
-0.011
(0.025)
-0.077**
(0.033)
-0.008
(0.008)
-0.001
(0.004)
0.034***
(0.010)
-3.7e-05
(1.0e-04)
0.002
(0.003)
0.021
(0.044)
0.131
(0.079)
0.767***
(0.128)
1701
14
0.07
Steps involved in methodology:
Part B: Econometrics
Step E1: Check for supply-side endogeneity in the
rollout of a program. ✔
Step E2: Estimation of the Retrospective Intention
to Treat Effect ✔
Step E3: Testing for Demand-Side Endogeneity ✔
Step E4: Estimation of the Take-up Effect ✔
Step E5: Treatment Window Regression and F-test
of Take-up Effects
Table 6A—Five-Period Treatment Window with F-tests
fyrcreditplus2
fyrcreditplus1
fyrcredit
fyrcreditminus1
fyrcreditminus2
education father
education mother
age of father
age father squared
initial land (cuerdas)
retail
livestock
constant
Observations
Number of local
F-statistic: 2 Post-Treatment
vs. .2 Pre-Treatment
(1)
newwalls
0.080*
(0.046)
0.144
(0.119)
0.062
(0.067)
0.039
(0.050)
-0.047
(0.036)
-0.004
(0.003)
0.003
(0.005)
-0.009
(0.008)
2.6e-05
(3.3e-05)
-0.001
(0.003)
-0.010
(0.016)
0.057
(0.037)
0.168
(0.193)
611
13
4.73**
(2)
newroof
0.025
(0.045)
0.039
(0.039)
-0.008
(0.016)
-0.009
(0.014)
-0.005
(0.025)
0.001
(0.001)
0.003
(0.002)
0.000
(0.003)
6.4e-07
(2.1e-05)
-0.000
(0.001)
0.006
(0.009)
0.031*
(0.017)
-0.036
(0.066)
769
13
1.26
(3)
newfloor
0.074**
(0.036)
0.037
(0.032)
0.031
(0.027)
0.033
(0.029)
0.008
(0.015)
0.001
(0.001)
-0.001
(0.002)
0.002
(0.003)
-1.8e-05
(2.7e-05)
-0.001
(0.001)
-0.013
(0.014)
0.003
(0.017)
0.050
(0.062)
1053
14
5.25**
(4)
newtoilet
-0.031
(0.039)
0.027
(0.043)
0.082
(0.061)
0.037
(0.035)
0.029
(0.039)
0.002
(0.003)
0.005***
(0.002)
-0.009
(0.010)
1.2e-04
(1.5e-04)
-0.000
(0.002)
0.001
(0.025)
0.025
(0.031)
0.109
(0.128)
729
14
1.11
(5)
newland
-0.009
(0.025)
0.028
(0.045)
0.024
(0.018)
0.010
(0.018)
-0.015
(0.017)
-0.003**
(0.001)
0.001**
(0.001)
0.001
(0.002)
-1.2e-05
(2.1e-05)
-0.000
(0.001)
0.006
(0.022)
-0.005
(0.022)
-0.005
(0.035)
1185
14
0.47
p-value
0.050
0.2814
0.039
0.312
0.503
R-squared
0.09
0.03
0.02
0.05
0.01
Robust standard errors in parentheses. Estimation uses year and village-level fixed effects.
* significant at 10%; ** significant at 5%; *** significant at 1%
(6)
homeimprov
0.032
(0.049)
0.054
(0.072)
0.092*
(0.047)
0.046
(0.035)
-0.015
(0.034)
-0.006**
(0.002)
0.002
(0.002)
-0.001
(0.006)
4.9e-06
(7.3e-05)
0.001
(0.003)
-0.008
(0.025)
0.003
(0.035)
0.099
(0.116)
1185
14
0.28
0.606
0.03
Table 6B—Seven-Period Treatment Window with F-tests
fyrcreditplus3
fyrcreditplus2
fyrcreditplus1
fyrcredit
fyrcreditminus1
fyrcreditminus2
fyrcreditminus3
education father
education mother
age of father
age father squared
initialcuerdas
retail
livestock
constant
Observations
Number of local
F-statistic: 3 Post-Treatment
vs. 3 Pre-Treatment
(1)
newwalls
0.237
(0.217)
-0.030
(0.039)
0.215
(0.137)
0.070
(0.064)
0.040
(0.053)
-0.033
(0.032)
0.015
(0.030)
-0.005
(0.003)
0.004
(0.006)
-0.012
(0.010)
1.3e-04
(1.1e-04)
-0.001
(0.004)
0.001
(0.019)
0.074*
(0.038)
0.326
(0.244)
535
13
2.34
(2)
newroof
-0.001
(0.011)
-0.012
(0.016)
0.054
(0.036)
0.009
(0.017)
0.010
(0.014)
0.013
(0.029)
0.041
(0.025)
0.001
(0.002)
0.004*
(0.002)
0.000
(0.005)
7.4e-06
(5.0e-05)
0.000
(0.001)
0.006
(0.011)
0.033
(0.020)
-0.039
(0.096)
648
13
0.31
(3)
newfloor
0.181
(0.148)
0.044
(0.060)
0.029
(0.022)
0.031
(0.026)
0.025
(0.033)
-0.008
(0.020)
-0.007
(0.016)
-0.001
(0.002)
0.002
(0.003)
0.002
(0.003)
-2.0e-05
(3.1e-05)
-0.001
(0.001)
-0.002
(0.015)
0.019
(0.018)
-0.009
(0.072)
846
14
2.47
(4)
newtoilet
-0.048
(0.057)
-0.018
(0.045)
0.051
(0.045)
0.046
(0.073)
0.004
(0.021)
0.021
(0.046)
-0.011
(0.032)
0.001
(0.001)
0.004
(0.004)
-0.003
(0.007)
2.3e-05
(9.8e-05)
-0.001
(0.001)
0.006
(0.028)
0.019
(0.030)
0.037
(0.103)
621
14
0.040
(5)
newland
-0.092**
(0.039)
-0.103**
(0.047)
0.012
(0.128)
-0.006
(0.078)
0.115
(0.127)
-0.070**
(0.026)
-0.047
(0.067)
-0.008
(0.007)
0.002
(0.007)
0.003
(0.007)
-4.0e-05
(7.0e-05)
0.002
(0.005)
-0.058
(0.102)
-0.101
(0.095)
0.098
(0.098)
998
14
9.69
p-value
0.152
0.586
0.141
0.840
0.008
R-squared
0.12
0.04
0.04
0.05
0.02
Robust standard errors in parentheses. Estimation uses year and village-level fixed effects.
* significant at 10%; ** significant at 5%; *** significant at 1%
(6)
homeimprov
0.150
(0.129)
-0.007
(0.051)
0.083
(0.076)
0.090
(0.058)
0.043
(0.042)
-0.018
(0.039)
0.034
(0.032)
-0.008***
(0.002)
0.003
(0.002)
-0.002
(0.007)
1.1e-05
(7.7e-05)
0.000
(0.001)
-0.004
(0.022)
-0.004
(0.026)
0.111
(0.165)
998
14
0.84
0.377
0.04
Change in Probability of New Walls
5-year Credit Window
0.400
0.350
0.300
0.250
0.200
0.150
0.100
0.050
0.000
-0.050
-0.100
-0.150
t-2
t-1
t=0
Upper 90% Confidence
Point Estimate
Lower 90% Confidence
t+1
t+2
Change in Probability of New Roof:
5-year Credit Window
0.120
0.100
0.080
0.060
0.040
0.020
0.000
-0.020
t-2
t-1
t=0
-0.040
-0.060
Upper 90% Confidence
Point Estimate
Lower 90% Confidence
t+1
t+2
Change in Probability of New Floor
5-year Credit Window
0.160
0.140
0.120
0.100
0.080
0.060
0.040
0.020
0.000
-0.020
t-2
t-1
t=0
-0.040
Upper 90% Confidence
Point Estimate
Lower 90% Confidence
t+1
t+2
Change in Probability of New Toilet:
5-year Credit Window
0.200
0.150
0.100
0.050
0.000
-0.050
t-2
t-1
t=0
-0.100
-0.150
Upper 90% Confidence
Point Estimate
Lower 90% Confidence
t+1
t+2
Change in Probability of New Land Purchase:
5-year Credit Window
0.120
0.100
0.080
0.060
0.040
0.020
0.000
-0.020
t-2
t-1
t=0
-0.040
-0.060
Upper 90% Confidence
Point Estimate
Lower 90% Confidence
t+1
t+2
Change in Probability of Home Improvement:
5-year Credit Window
0.200
0.150
0.100
0.050
0.000
t-2
t-1
t=0
-0.050
-0.100
Upper 90% Confidence
Point Estimate
Lower 90% Confidence
t+1
t+2
Conclusions:
Presented a methodology for ascertaining the impact
of development programs such as microfinance
that offers several advantages:
1. Can be used within existing client base.
Conclusions:
Presented a methodology for ascertaining the impact
of development programs such as microfinance
that offers several advantages:
1. Can be used within existing client base.
2. Data can be collected in single x-sectional survey
Conclusions:
Presented a methodology for ascertaining the impact
of development programs such as microfinance
that offers several advantages:
1. Can be used within existing client base.
2. Data can be collected in single x-sectional survey
3. Illustrates timing and dynamics of impact
Conclusions:
Presented a methodology for ascertaining the impact
of development programs such as microfinance
that offers several advantages:
1. Can be used within existing client base.
2. Data can be collected in single x-sectional survey
3. Illustrates timing and dynamics of impact
Other (easier) applications: Fresh water systems,
Nutrition programs, Cash transfers, Vaccinations
Electrification…