American Economic Association
Schooling and Labor Market Consequences of School Construction in Indonesia: Evidence
from an Unusual Policy Experiment
Author(s): Esther Duflo
Source: The American Economic Review, Vol. 91, No. 4 (Sep., 2001), pp. 795-813
Published by: American Economic Association
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Schooling and Labor Market Consequences of School
Construction in Indonesia: Evidence from
an Unusual Policy Experiment
By ESTHER DuFLo*
Between 1973 and 1978, the Indonesian government engaged in one of the largest
school construction programs on record. Combining differences across regions in
the number of schools constructed with differences across cohorts induced by the
timing of the program suggests that each primary school constructed per 1,000
children led to an average increase of 0.12 to 0.19 years of education, as well as a
1.5 to 2.7 percent increase in wages. This implies estimates of economic returns to
education ranging from 6.8 to 10.6 percent. (JEL 12, J3 1, 015, 022)
The questions of whether investments in infrastructure
can cause an increase in educational
attainment, and whether an increase in educational
attainment causes an increase in earnings
are basic concerns for development economists.
A large body of literature investigates the impact
of schooling infrastructure on schooling, as
well as the returns to education in developing
countries [see George Psacharopoulos (1994)
and John Strauss and Duncan Thomas (1995)
for surveys]. Estimated returns to education are,
in general, larger in developing countries than in
industrialized countries. However, most of the existing
studies are based on simple correlations
between years of education and wages. Family
and community background are important determinants
of both schooling and labor market outcomes
in developing countries, and the bias in
estimates that treat an individual's education level
as exogenous could be important.
This paper exploits a dramatic change in policy
to evaluate the effect building schools has on
education and earnings in Indonesia, a country
where the GDP per capita in 1995 was only $720,
3.5 percent that of the United States. In 1973, the
Indonesian government launched a major school
construction program, the Sekolah Dasar INPRES
program. Between 1973-1974 and 1978-1979,
more than 61,000 primary schools were constructed-an
average of two schools per 1,000 children
aged 5 to 14 in 1971. Enrollment rates among
children aged 7 to 12 increased from 69 percent in
1973 to 83 percent by 1978. This was in contrast
to the absence of capital expenditure and a decline
in enrollment in the early 1970's.
Using a large cross section of men born between
1950 and 1972 from the 1995 intercensal
survey of Indonesia (SUPAS), I linked an
adult's education and wages with district-level
data on the number of new schools built between
1973-1974 and 1978-1979 in his region
of birth. The exposure of an individual to the
program was determined both by the number of
schools built in his region of birth and by his
age when the program was launched. After controlling
for region of birth and cohort of birth
effects, interactions between dummy variables
indicating the age of the individual in 1974 and
the intensity of the program in his region of
birth are plausibly exogenous variables, and are
used as instruments in the wage equation. Similar
strategies were used to estimate the effect of
* Department of Economics, Massachusetts Institute of
Technology, 50 Memorial Drive, Cambridge, MA 02142.
Financial support from the Fondation Thiers and the Alfred
P. Sloan Dissertation Fellowship is gratefully acknowledged.
I also thank the World Bank for partially funding this
research, the Central Bureau of Statistics of Indonesia, the
Bappenas and the Ministry of Education and Culture for
data, and the staff of the HIID office in Jakarta (in particular
Joe Stem and Peter Rosner) for their help and hospitality. I
am grateful to Joshua Angrist, Abhijit Banerjee, Michael
Kremer, and Jonathan Morduch for their advice and support
throughout this research, and to Daron Acemoglu, David
Card, Anne Case, Aimee Chin, Angus Deaton, Guido Imbens,
Emmanuel Saez, various seminar participants, and
two referees for helpful comments. I bear sole responsibility
for the content of this paper, which is not meant to reflect
the views of the World Bank or any government agency.
795
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796 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
school quality on returns to education (David
Card and Alan Krueger, 1992), and the effect of
college education on earnings (Card and
Thomas Lemieux, 1998).
The estimates suggest that each new school
constructed per 1,000 children was associated
with an increase of 0.12 to 0.19 in years of
education and 1.5 to 2.7 percent in earnings
for the first cohort fully exposed to the program.
This implies estimates of economic returns
to education ranging from 6.8 to 10.6
percent.
The remainder of this paper is organized as
follows. In Section I, I describe the data, the
INPRES program, and an overview of the identification
strategy. In Section II, I present the
estimated impact of the program on education.
Section III is devoted to the estimation of the
effect of the program on wages, and Section IV
to the estimate of economic returns to education.
Section V combines the estimates of the
program effect on wages with detailed data on
the cost of education in Indonesia in a tentative
cost-benefit analysis of the program. Section
VI concludes.
I. The Program
A. Data
The data used in this paper come from the
1995 intercensal survey of Indonesia (SUPAS).
I focus on men born between 1950 and 1972.
Summary statistics for this sample are presented
in Table 1, panel A. There are 152,989 individuals
in the sample, with an average level of 7.98
years of completed education (6 years of education
correspond to graduation from primary
school). There are 60,633 individuals who work
for a wage (sample selection issues are examined
in Section IV).
Using information on the district of birth of
each individual, I matched the individual survey
data with district-level census data and the
number of schools scheduled to be constructed
in each district under the INPRES program.1
TABLE 1-DESCRIPTIVE STATISTICS
Mean
Panel A: Individual Level Means
Education (whole sample N = 152,989) 7.98
Education (sample with valid wage data
N = 60,663) 9.00
INPRES schools built per 1,000 children 1.98
INPRES schools built per 1,000 children
(sample with valid wage data) 1.89
INPRES schools built per 1,000 children
(High program regions) 2.44
INPRES schools built per 1,000 children
(Low program regions) 1.54
Log(hourly wage) 6.87
Monthly earnings (SUPAS 1995),
thousands Rupiah 13
Monthly earnings (SUSENAS 1993) of
wage earners, thousands Rupiah 205
Monthly earnings (SUSENAS 1993) of
self-employed individuals, thousands
Rupiah 152
Panel B: District Level Means (N = 293)
INPRES schools constructed (1973-1974
to 1978-1979) 222
INPRES schools constructed per 1000
children (1973-1974 to 1978-1979) 2.34
Number of teachers in 1973-1974 1,530
Number of teachers in 1978-1979 2,082
Number of schools in 1973-1974 219
Fraction of the population attending school
in 1971 (Census) 0.174
Enrollment rate in primary school in 1973
(Ministry of Education and Culture) 0.68
Panel C: Indonesian Family Life Survey,
Individuals Born Between 1950 and
1972 (all numbers are in percentages)
Proportion of individuals having migrated
between birth and age 12 8.5
Proportion of people having repeated at
least one grade in primary school 20.0
Proportion of people completing more than
primary having repeated at least one
grade in primary school 6.0
Proportion of individuals having attended
primary school after age 12 (estimated) 15.8
Proportion of individuals having attended
primary school after age 13 (estimated) 6.8
Proportion of individuals born 1950-1961,
completing primary or less, who left
school after 1974 2.8
Proportion of individuals born 1962-1966,
completing primary or less, who left
school after 1974 24.5
Sources: IFLS, SUPAS, SUSENAS, INPRES instruction,
Census (1971), Ministry of Education and Culture.
1 According to a survey of the implementation of the
program conducted by the Ministry of Education and Culture
in 1983, the actual number of schools constructed
closely corresponded to the plans.
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 797
District-level descriptive statistics are presented
in Table 1, panel B.
B. The Sekolah Dasar INPRES Program
Starting in 1973, the Indonesian government
emphasized the need for "equity" across provinces.
Oil revenues were mobilized to finance
centrally administered development programs,
the "presidential instructions" (INPRES). The
Sekolah Dasar INPRES was one of the first
INPRES programs and by far the largest at the
time it was launched (in 1973-1974). As a
result of the oil boom, real expenditures on
regional development more than doubled between
1973 and 1980, and the Sekolah Dasar
INPRES program became extremely important.
Between 1973-1974 and 1978-1979, 61,807
new schools were constructed (Table 1, panel
B), at a cost of over 500 million 1990 U.S.
dollars (1.5 percent of the Indonesian GDP in
1973). This represented more than one school
per 500 children aged 5 to 14 in 1971, which
reportedly makes INPRES the fastest primary
school construction program ever undertaken in
the world (World Bank, 1990).
Once an INPRES school was established, the
government recruited the teachers and paid their
salaries (each school was designed for three
teachers and 120 pupils). An effort to train more
teachers paralleled the INPRES program
(World Bank, 1990), and the proportion of
teachers meeting the minimum qualification requirements
did not worsen significantly between
1971 and 1978. The stock of schools
multiplied by two over the period, and the stock
of teachers grew by 43 percent. This contrasted
with a freeze of capital expenditure and teacher
recruiting prior to 1973 (Daroesman, 1971).
The program was designed explicitly to target
children who had not previously been enrolled
in school. The general allocation rule was
that the number of schools to be constructed in
each district was proportional to the number of
children of primary school age not enrolled in
school in 1972. The "presidential instructions"
also listed the exact number of schools to be
constructed in each district. Table 2 presents the
results that a regression of the logarithm of the
number of INPRES schools planned in each
region had on the logarithm of the nonenrollment
rate and the logarithm of the number of
TABLE 2-THE ALLOCATION OF SCHOOLS
Log(INPRES schools)a
Log of number of children 0.78
aged 5-14 in the region (0.027)
Log(1 - enrollment rate in 0.12
primary school in 1973)b (0.038)
Number of observations 255
R 2 0.78
Notes: Standard errors are in parentheses.
a The dependent variable is the log of the number of
INPRES schools built between 1973 and 1978.
b The enrollment rate in primary school is the number of
children enrolled in primary school in 1973 (obtained from
the Ministry of Education and Culture) divided by the
number of children aged 5-14 in the region in 1973.
children. The actual rule implies that both coefficients
should be close to 1. Both coefficients have
the expected sign, but the coefficient of the nonenrollment
rate is smaller than 1. This might be
explained by measurement error in the nonenrollment
measure as well as by imperfect application
of the general rule: The program appears to
have been less redistributive than it intended to.
C. Identification Strategy
The date of birth and the region of birth
jointly determine an individual's exposure to
the program.
Indonesian children normally attend primary
school between the ages of 7 and 12. All children
born in 1962 or before were 12 or older in 1974,
when the first INPRES schools were constructed.
Thus, they did not benefit from the program, since
they should have left primary school before the
first INPRES schools were opened. Grade repetition
and delayed school entry could lead a few of
these children to benefit from the program during
their last year in school. However, according to
the 1993 Indonesian Family Life Survey (IFLS)
data set (conducted in 1993 by RAND and the
Demographic Institute at the University of Indonesia),
less than 3 percent of the children born
between 1950 and 1962 were still in primary
school in 1974. For younger children, the exposure
is an increasing function of their date of birth.
Hence, the effect of the program should be close
to 0 for children 12 or older in 1974 and increasing
for younger children.
Because the program intensity was related to
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798 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
TABLE 3-MEANS OF EDUCATION AND LOG(WAGE) BY COHORT AND LEVEL OF PROGRAM CELLS
Years of education Log(wages)
Level of program in region of birth Level of program in region of birth
High Low Difference High Low Difference
(1) (2) (3) (4) (5) (6)
Panel A: Experiment of Interest
Aged 2 to 6 in 1974 8.49 9.76 -1.27 6.61 6.73 -0.12
(0.043) (0.037) (0.057) (0.0078) (0.0064) (0.010)
Aged 12 to 17 in 1974 8.02 9.40 -1.39 6.87 7.02 -0.15
(0.053) (0.042) (0.067) (0.0085) (0.0069) (0.011)
Difference 0.47 0.36 0.12 -0.26 -0.29 0.026
(0.070) (0.038) (0.089) (0.011) (0.0096) (0.015)
Panel B: Control Experiment
Aged 12 to 17 in 1974 8.02 9.40 -1.39 6.87 7.02 -0.15
(0.053) (0.042) (0.067) (0.0085) (0.0069) (0.011)
Aged 18 to 24 in 1974 7.70 9.12 -1.42 6.92 7.08 -0.16
(0.059) (0.044) (0.072) (0.0097) (0.0076) (0.012)
Difference 0.32 0.28 0.034 0.056 0.063 0.0070
(0.080) (0.061) (0.098) (0.013) (0.010) (0.016)
Notes: The sample is made of the individuals who earn a wage. Standard errors are in parentheses.
enrollment rates in 1972, which differed widely
across regions, region of birth is a second dimension
of variation in the intensity of the
program. Region of birth is highly correlated
with the region of education: 91.5 percent of the
children in the IFLS sample were still living in
the district where they were born at age 12.
However, unlike region of education, it is not
endogenous with respect to the program [which
would lead to bias in the program effect; see
Rosenzweig and Wolpin (1988)], given that all
individuals in the sample were bom before the
program was started.
The basic idea behind the identification strategy
can be illustrated using simple two-by-two
tables. Table 3 shows means of education and
wages for different cohorts and program levels.
Regions are separated in "high program" and
"low program" regions. The difference between
the number of schools constructed per 1,000
children constructed in high and low program
regions is 0.90.2 In panel A, I compare the
educational attainment and the wages of individuals
who had little or no exposure to the
program (they were 12 to 17 in 1974) to those of
individuals who were exposed the entire time
they were in primary school (they were 2 to 6 in
1974), in both types of regions. In both cohorts,
the average educational attainment and wages in
regions that received fewer schools are higher
than in regions that received more schools. This
reflects the program provision that more schools
were to be built in regions where enrollment
rates were low. In both types of regions, average
educational attainment increased over time.
However, it increased more in regions that received
more schools. The difference in these
differences can be interpreted as the causal effect
of the program, under the assumption that
in the absence of the program, the increase in
educational attainment would not have been
systematically different in low and high program
regions. An individual young enough,
born in a high program region, received on
average 0.12 more years of education, and the
logarithm of his wage in 1995 was 0.026 higher.
These differences in differences are not significantly
different from 0. This simple estimator
suggests that one school per 1,000 children contributed
to an increase in education by 0.13
years (0.12 divided by 0.90) and wages by
0.029 for children aged 2 to 6 when the program
was initiated. The Wald estimate of returns to
education is the ratio of these two estimates.
The identification assumption should not be
taken for granted: The pattern of increase in
2 To make Wald estimates meaningful, estimates in Table
3 are presented for the sample with valid wage data.
High program regions are defined as regions where the
residual of a regression of the number of schools on the
number of children is positive.
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 799
education could vary systematically across regions.
In particular, there could be mean reversion.
However, an implication of the
identification assumption can be tested because
individuals aged 12 or older in 1974 were not
exposed to the program. The increase in education
between cohorts in this age-group should
not differ systematically across regions.
In Table 3, panel B, I present this control
experiment. I consider a cohort aged 18 to 24 in
1974 and a cohort aged 12 to 17 in 1974. The
estimated differences in differences are very
close to 0. These results provide some suggestive
evidence that the differences in differences
are not driven by inappropriate identification assumptions,
although they are imprecisely estimated.
In panel B, for example, the differences in
differences are insignificantly different from 0 but
also from the differences in differences in panel A.
The remainder of this paper will elaborate on this
strategy to lead to more convincing results.
II. Effect on Education
A. Basic Results
To exploit the variation in treatment intensity
across regions and cohorts, this strategy can be
generalized to a regression framework. Consider
first the difference between the average
education of a young cohort exposed to the
program and that of an older cohort not exposed
to the program. If additional schools led to an
increase in educational attainment, the difference
will be positively related to the number of
schools constructed in each region.
This suggests running the following regres-
sion:
(1) Sijk = C1 + alj + Ilk + (PiTi)y1
+ (CiTi)51 + Eijk
where Sijk is the education of individual i born
in region j in year k, Ti is a dummy indicating
whether the individual belongs to the ''young"
cohort in the subsample, c1 is a constant, Olk iS
a cohort of birth fixed effect, a1lj is a district of
birth fixed effect, Pj denotes the intensity of the
program in the region of birth, and Cj is a vector
of region-specific variables.
Table 4 (columns 1-3) presents estimates of
equation (1) for two subsamples. In panel A, I
compare children aged 2 to 6 in 1974 with
children aged 12 to 17 in 1974. In column 1, the
specification controls only for the interaction of
a cohort of birth dummy and the population
aged 5 to 14 in 1971. The suggested effect is
that one school built per 1,000 children increased
the education of the children aged 2 to
6 in 1974 by 0.12 years for the whole sample,
and by 0.20 years for the sample of wage
earners.
This interpretation relies on the identification
assumption that there are no omitted timevarying
and region-specific effects correlated
with the program. The allocation of schools to
each region was an explicit function of the
enrollment rate in the region in 1972. Therefore,
the estimate could potentially confound the effect
of the program with mean reversion that
would have taken place even in its absence. The
identification assumption will also be violated if
the allocation of other governmental programs
initiated as a result of the oil boom (and potentially
affecting education) was correlated with
the allocation of INPRES schools. Thus, I
present specifications that control for the interactions
between cohort dummies and the enrollment
rate in the population in 1971, as well as
for interactions between cohort dummies and
the allocation of the water and sanitation program,
the second largest INPRES program centrally
administered at the time. Controlling for
both the enrollment rate and the water and sanitation
program makes the estimates higher
(columns 2 and 3), suggesting that the estimates
are not upwardly biased by mean reversion or
omitted programs.
Panel B of Table 4 shows the results of the
control experiment (comparing the cohort aged
12 to 17 to the cohort aged 18 to 24 in 1974). If,
before the program was started, education had
increased faster in regions that received more
schools, panel B would show (spurious) positive
coefficients. But the impact of the "program"
is very small and never significant. The
coefficients are statistically different from the
corresponding coefficients in panel A. Although
this is not definitive evidence (education level
could have started converging precisely after
1973), it is reassuring.
Even if the identification assumption is satisfied,
the coefficient may slightly overestimate
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800 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
TABLE 4-EFFECT OF THE PROGRAM ON EDUCATION AND WAGES: COEFFICIENTS OF THE INTERACTIONS BETWEEN COHORT
DUMMIES AND THE NUMBER OF SCHOOLS CONSTRUCTED PER 1,000 CHILDREN IN THE REGION OF BIRTH
Dependent variable
Years of education Log(hourly wage)
Observations (1) (2) (3) (4) (5) (6)
Panel A: Experiment of Interest: Individuals Aged 2 to 6 or 12 to 17 in 1974
(Youngest cohort: Individuals ages 2 to 6 in 1974)
Whole sample 78,470 0.124 0.15 0.188
(0.0250) (0.0260) (0.0289)
Sample of wage earners 31,061 0.196 0.199 0.259 0.0147 0.0172 0.0270
(0.0424) (0.0429) (0.0499) (0.00729) (0.00737) (0.00850)
Panel B: Control Experiment: Individuals Aged 12 to 24 in 1974
(Youngest cohort: Individuals ages 12 to 17 in 1974)
Whole sample 78,488 0.0093 0.0176 0.0075
(0.0260) (0.0271) (0.0297)
Sample of wage earners 30,225 0.012 0.024 0.079 0.0031 0.00399 0.0144
(0.0474) (0.0481) (0.0555) (0.00798) (0.00809) (0.00915)
Control variables:
Year of birth*enrollment rate in 1971 No Yes Yes No Yes Yes
Year of birth*water and sanitation
program No No Yes No No Yes
Notes: All specifications include region of birth dummies, year of birth dummies, and interactions between the year of birth
dummies and the number of children in the region of birth (in 1971). The number of observations listed applies to the
specification in columns (1) and (4). Standard errors are in parentheses.
the effect of the program on average education.3
Note that such a large program could potentially
have affected the returns to education by increasing
the stock of primary school graduates (Angrist,
1995). Individuals' education choices could
then have responded to this decrease in the returns
to education. To the extent that Indonesia is an
integrated labor market, the returns to education
would have declined in the entire country. The
estimates do not take this negative effect of the
program into account because it is common to all
regions. This effect, however, is not likely to be
very large. Its size ultimately depends on the elasticity
of the demand for educated labor (which is
likely to be low in a rapidly growing economy),
the sensitivity of educational choice to perceived
returns to education, and the extent of integration
in the Indonesian labor market.
B. Reduced-Form Evidence
This identification strategy can be generalized
to an interaction terms analysis.
Consider the following relationship between
the education (Sijk) of an individual i, born in
region j, in year k, and his exposure to the
program:
(2) Sijk = C I+ a lj +f1k
23
+ E (pj x dil)yll
1=2
23
+ E (Cj X di,)>S1 + 6ijk
where di, is a dummy that indicates whether
individual i is age 1 in 1974 (a year-of-birth
dummy). In these unrestricted estimates, I
measure the time dimension of exposure to
the program with 22 year-of-birth dummies.
Individuals aged 24 in 1974 form the control
group, and this dummy is omitted from the
regression. Each coefficient yll can be interpreted
as an estimate of the impact of the
program on a given cohort. This is simply a
3In the working paper version (Duflo, 2000), this point
is made in the context of a simple formal model.
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 801
X ~~~~~~~~~~~~~~~0.2
0. 1
0
22 21 20 1 9 1 8 17 1 6 15 114% 13 1 2 1 1 1Q 9 8 7 6 5 4 3
'-~~~~~~~~~~~~~~ ~~~~-0.1
0 ,* ,-- - - -----S z . - - -------'-- - - --'--- - '- - ----'--'-------------0.12
t.~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~0 2
Age in 1974
FIGURE 1. COEFFICIENTS OF THE INTERACTIONS AGE IN 1974* PROGRAM INTENSITY IN THE REGION OF BIRTH IN THE
EDUCATION EQUATION
generalization of equation (1) to estimate cohortby-cohort
contrasts.
There is a testable restriction on the pattern of
the coefficients Yii Because children aged 13 and
older in 1974 did not benefit from the program,
the coefficients Yll should be 0 for 1 > 12 and start
increasing for 1 smaller than some threshold (the
oldest age at which an individual could have been
exposed to the program and still benefit from it).
Figure 1 plots the YjI Each dot on the solid
line is the coefficient of the interaction between
a dummy for being a given age in 1974 and the
number of schools constructed per 1,000 children
in the region of birth (a 95-percent confidence
interval is plotted by broken lines). These
coefficients fluctuate around 0 until age 12 and
start increasing after age 12. As expected, the
program had no effect on the education of cohorts
not exposed to it, and it had a positive
effect on the education of younger cohorts. All
coefficients are significantly different from 0
after age 8. These figures show that the identification
strategy is reasonable and that the program
had an effect on education.
C. Restricted Estimation
Instead of testing whether the Yll are
equal to 0 for I ? 13, one can impose this
restriction. The equation to be estimated is
then
12
(3) Sijk = CI + aj1 + Olk + E (Pjdj&)y I
I = 2
12
+ Z (Cjdil) 1T + Sijk
1=2
The omitted group (the control group) is now
comprised of individuals aged 13 to 24 in
1974. This is more efficient and leads to
more precise estimates of the effect of the
program.
Columns (1)-(3) in Table 5 show the coefficients
of the interactions between age in 1974
and the intensity of the program in the region of
birth in three specifications in the whole sample
[columns (4)-(6) show the same results for the
sample of wage earners]. In all columns, the
estimated effect is positive after age 10. All
coefficients are significantly greater than 0 after
age 8. All sets of interactions are statistically
different from 0 (the F-statistic for the null
hypothesis is presented at the bottom of the
table). The coefficients generally increase with
date of birth (decreasing with age), except for a
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802 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
TABLE 5-EiFECT OF THE PROGRAM ON EDUCATION AND WAGES: COEFFICIENTS OF THE INTERACTIONS BETWEEN DUMMIES
INDICATING AGE IN 1974 AND THE NUMBER OF SCHOOLS CONSTRUCTED PER 1,000 CHILDREN IN REGION OF BIRTH
Dependent variable: years of education Dependent variable:
Whole sample Sample of wage earners log(hourly wage)
Age in 1974 (1) (2) (3) (4) (5) (6) (7) (8) (9)
12 -0.035 -0.025 0.002 -0.040 -0.010 0.009 0.016 0.019 0.027
(0.047) (0.048) (0.054) (0.077) (0.078) (0.091) (0.013) (0.013) (0.015)
11 0.011 0.025 0.018 0.008 0.014 -0.003 -0.014 -0.013 -0.009
(0.046) (0.047) (0.051) (0.073) (0.074) (0.083) (0.012) (0.013) (0.014)
10 0.059 0.049 0.078 0.10 0.092 0.13 0.0036 0.0042 0.0059
(0.047) (0.049) (0.054) (0.075) (0.076) (0.090) (0.013) (0.013) (0.015)
9 0.14 0.14 0.15 0.067 0.063 0.17 0.0095 0.010 0.018
(0.039) (0.041) (0.044) (0.065) (0.066) (0.077) (0.011) (0.011) (0.013)
8 0.088 0.11 0.11 0.19 0.20 0.28 0.019 0.021 0.027
(0.049) (0.050) (0.054) (0.078) (0.079) (0.089) (0.013) (0.013) (0.015)
7 0.12 0.14 0.16 0.11 0.13 0.16 -0.0095 -0.0049 0.0066
(0.044) (0.046) (0.051) (0.072) (0.073) (0.084) (0.012) (0.012) (0.014)
6 0.14 0.17 0.26 0.23 0.23 0.32 0.011 0.013 0.018
(0.042) (0.044) (0.049) (0.070) (0.070) (0.084) (0.012) (0.012) (0.014)
5 0.10 0.13 0.13 0.14 0.16 0.27 0.021 0.023 0.052
(0.043) (0.045) (0.050) (0.075) (0.075) (0.088) (0.013) (0.013) (0.015)
4 0.11 0.12 0.18 0.19 0.19 0.29 0.019 0.020 0.038
(0.039) (0.041) (0.046) (0.069) (0.069) (0.082) (0.012) (0.012) (0.014)
3 0.11 0.14 0.20 0.15 0.17 0.30 0.0079 0.013 0.027
(0.044) (0.046) (0.053) (0.079) (0.080) (0.097) (0.013) (0.014) (0.016)
2 0.14 0.19 0.19 0.20 0.22 0.25 0.016 0.023 0.040
(0.041) (0.043) (0.049) (0.073) (0.074) (0.088) (0.012) (0.013) (0.015)
Control variables:a
Year of birth*enrollment
rate in 1971 No Yes Yes No Yes Yes No Yes Yes
Year of birth*water and
sanitation program No No Yes No No Yes No No Yes
F-statisticb 4.03 5.18 6.15 2.70 2.74 4.38 1.13 1.29 2.05
R 2 0.19 0.19 0.17 0.14 0.14 0.13 0.14 0.15 0.13
Number of observations 152,989 152,495 143,107 60,633 60,466 55,144 60,633 60,466 55,144
Notes: All specifications include region of birth dummies, year of birth dummies, and interactions between the year of birth
dummies and the number of children in the region of birth (in 1971). Standard errors are in parentheses.
a The control group is comprised of individuals aged 13-24 in 1974.
b The F-statistics test the hypothesis that the coefficients of the interaction between the year of birth dummies and the
program intensity in the region of birth are jointly zero.
high value at age 9 and a decline between ages
6 and 5. They increase faster between ages 12
and 9 than they do subsequently, thus suggesting
that once the education level in the population
reaches a certain point, increasing it by
building primary schools becomes more
difficult.
The estimates in column (1) (without controls)
suggest that one school per 1,000 children
increases the education of the youngest children
by 0.14 years. On average, 1.98 schools were
built per 1,000 children. This implies that at its
mean value, the program caused an increase in
education of 0.27 years for these children (the
average education in the sample is 7.98 years).
As before, controlling for enrollment rate in
1971 [colunm (2)] and the water and sanitation
program [column (3)] makes the estimate
slightly higher. In columns (4)-(6), I present the
same estimates for the subsample of wage earners.
The program effect is higher for wage earners
than it is in the whole sample.
More insight into why this program was effective
is obtained by examining its impact in
different types of regions. In Table 6 (panel A),
I present results equivalent to the specification
in Table 4 [equation (1)] for various subsamples
of regions of birth. Columns (2) and (3) suggest
that the program had no effect in densely populated
regions, and a large effect in sparsely
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 803
TABLE 6-PROGRAM EFFECT AND RETURNS TO EDUCATION BY CATEGORIES OF REGION OF BIRTH
Characteristics of region of birth
Preprogram
Whole Densitya 1976 Povertyb educationc
sample <Median >Median High Low <Median >Median
(1) (2) (3) (4) (5) (6) (7)
Panel A: Effect of the Program on Educati
Dependent variable: Years of education.
Sample: individuals ages 2 to 6 or 12 to 17
in 1974
Interaction 0.15 0.19 -0.014 0.13 0.083 0.14 0.13
(2-6 in 1974)*program intensity in region of (0.026) (0.035) (0.048) (0.058) (0.035) (0.040) (0.036)
Panel B: Effect of the Program on Wages
Dependent variable: log(hourly wage). Sample:
individuals ages 2 to 6 or 12 to 17 in 1974
(wage earners)
Interaction 0.017 0.032 -0.00084 0.051 -0.00083 0.028 0.0046
(2-6 in 1974)*program intensity in region of (0.0074) (0.011) (0.012) (0.017) (0.0094) (0.013) (0.0095)
Panel C: Returns to Education
Dependent variable: log(hourly wage). Sample:
wage earners
Years of education 0.078 0.11 No First 0.10 No First 0.12 0.029
(0.00062) (0.026) stage (0.028) stage (0.032) (0.052)
[0.9] [0.86] [0.88] [0.72] [0.83]
Notes: Region of birth dummies, year of birth dummies,
and the enrollment in the region in 1971 are included in
overidentification test are in square brackets.
a The median density (the density for the region of birth for the median person in the weighted sample) is 308 habitants
per square kilometer.
b The high poverty provinces are the provinces where the proportion of people consuming less than 1,500 Rp per capita
is larger than the national for rural regions (in the 1976 SUSENAS). I define "high poverty" as rural districts in these
provinces, which are: Lampung, Central East Java, East Nusa Tenggara, Central Sulawesi, South Sulawesi, Southeast
Sulawesi, Maluku, Irian Jaya (World Bank, 1979).
c The preprogram education is the average education in the region of birth for people born in 1962 or before. The median
is 3.18 years.
populated regions. In sparsely populated regions,
each new school significantly reduces the distance
to school. In densely populated regions, the main
effect will be to increase the availability of slots or
to reduce the overcrowding of old schools. This
suggests that reducing the distance children traveled
to school was the most important effect of the
program. This interpretation, however, should be
taken with caution, in that this difference may
come from other characteristics correlated with
density. Columns (4) and (5) suggest that the
program had more impact in poor provinces. In
columns (6) and (7), I divide the sample into
regions where the education of the cohort not
exposed to the program (men born between 1950
and 1962) was lower or higher than the median
(3.08 years of education). Results are similar for
both sets of regions.
In summary, it appears that the school construction
program had an impact on education. It
should be recalled that this program was accompanied
by a general effort by the Indonesian government
in favor of education, a priority of the
second five-year plan. As part of this effort, primary
school fees were suppressed in 1978 (World
Bank, 1990). Therefore, these results cannot be
generalized to less favorable contexts without applying
caution.
D. At What Level of Education Was the
Program Effective?
The impact of the program on welfare
depends on whether it primarily affected children
with a low or a high level of education.
Differences in differences in the cumulative
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804 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
0.08-
0.06
0
-0.02
-0.04
0 2 4 6 8 10 12 14 16 18 20
Years of education
FIGURE 2. DIFFERENCE IN DIFFERENCES IN CDF (ESTIMATED FROM LINEAR PROBABILITY MODEL)
WITH 95-PERCENT CONFIDENCE INTERVAL
distribution function of education provide information
on the level at which the program was
effective. In practice, for Sijkm, a dummy that
indicates whether the individual i, born in region
j, in year k, completed m years of education
or less, and for Pj, a dummy indicating
whether the child was born in a high program
region, I estimate the following equation:
(4) Sijk,?, = c + aj + Pk + (Pj Ti) K,?, + 8 ijk
The Km, for m = 0 to 19, are the values of the
estimated impact of the program at each level of
education. They are plotted in Figure 2 (the 95percent
confidence interval is plotted by broken
lines).
The shape of Figure 2 indicates at what level
the program was effective. The effect is increasing
until the sixth year of education, decreasing
until the twelfth, and slightly increasing thereafter.
A maximum of about 6 percent of the
sample living in high program regions were
induced to complete at least primary school.
This also shows some impact of the program on
the probability of completing lower secondary
school (1.5 percent of the sample is estimated to
have been induced by the program to complete
the 7th, 8th, and 9th grades or more). There is a
negative difference in differences at the senior
high-school level.
The program increased average schooling
through increasing primary schooling essentially.
This provides additional evidence that the
assumption underlying the identification strategy
is reasonable as the estimated effect of the
program for the levels of education that it did
not target is small or nonexistent. The negative
difference in differences at the senior high
school level may indicate that some variable
predicting the probability of attending senior
high school is omitted from this regression (and
changed in low program regions more than in
high program regions). The program could also
have induced more marginal people to complete
primary school and move on to junior high
school.4 However, the direct and indirect
costs of junior high school were much higher
than the costs of primary education and were
not equalized across regions at the time. This
4For example, Angrist and Imbens (1995) find that compulsory
attendance laws in the United States induce a fraction
of the sample to complete some college as a
consequence of constraining them to complete high school.
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 805
may explain why we do not observe large
spillovers.
III. Effect on Wages
A. Basic Results
The same identification strategy can be applied
to estimate the effect of the program on
wages. As with education, I estimate:
(5) Yijk Cl + alj + Olk
+ (PjTi)-yl + (CjTi)51 + 8ijk
where Yijk iS the logarithm of the 1995 wage of
an individual i, born in region j, in cohort k.
Results are presented in Table 4 [columns
(4)-(6)] and in Figure 1. In Table 4, panel A, I
set Ti equal to 1 for children aged 2 to 6 in 1974,
and use children aged 12 to 17 as the comparison
group.
In Table 4, panel A, the estimates range
from 1.5 to 2.7 percent. As in the case of
education, the estimates increase when I
control for enrollment rates in 1971 and for
the allocation of the water and sanitation program,
although none of these estimates is
significantly different from each other. In
panel B (which presents the control experiment),
the interaction coefficient is small and
not significantly different from zero in all
specifications. However, these estimates are
imprecise and I cannot reject equality of
the coefficients in panels A and B (although
the point estimates are much smaller
in panel B).
B. Reduced-Form Evidence
As for education, we can write an unrestricted
reduced-form relationship between exposure to
the program and the logarithm of the wage of an
individual (Yijk):
23
(6) Yijk = C2 + a2j + 02k + E (Pjdil)Y21
1=2
23
+ E (Cjdil)821 + Vijk
1=2
where a2j is a region-of-birth effect and 2k i
a cohort-of-birth effect. Pi, Ci, and di, are de
fined as in the education equation: Pj is the
intensity of the program in the region of birth,
Cj is the vector of control variables, and di, is a
dummy indicating whether individual i was of
age 1 in 1974.
The Y21 should be zero for 1 greater than 12
and start increasing thereafter. Moreover, if
the program affected wages only through its
effect on education, the coefficients Y21
should track the yil (in the education
equation).
In Figure 3, the Y21 are plotted by a dotted
line, and the yli are plotted by a solid line.
Both are oscillating until age 10 and start
increasing after age 11. The coefficients of
the interactions for education and wages track
each other.
C. Restricted Estimates
Finally, in columns (7)-(9) of Table 5, I
present estimates of the equation
12
(7) Yijk C2 + a2j + 02k + E (Pj dil)Y21
1=2
12
+ E (Cjdil)a21 + Vijk.
1=2
The effect of the program on wages is less
precisely estimated than as on education because
wages fluctuate more and the sample is
smaller (given that wages are not collected for
self-employed people). However, qualitatively,
the results parallel the estimated effects on education.
No effect is found for children aged 10
or older in 1974. The coefficients are positive
for younger children (except at age 7). The
coefficients of the interactions generally decrease
with age. The estimates are higher when
I control for both enrollment rate and the water
and sanitation program. The last line in this
table indicates that constructing one school per
1,000 children increased the 1995 wages of
individuals aged 2 in 1974 by 1.6 percent to 4.0
percent. The average number of schools constructed
per 1,000 children is 1.89 in the sample
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806 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
0.25
0.2
0.15
0.1
0.05
- - ~~~~~~~~~~~~~~~~~~~~~0
-0.05
_____ -0.1
24 23 22 21 20 19 18 17 16 15 14 13 12 11 10 9 8 7 6 5 4 3 2
Age in 1974
education . - -Iog(wage)
FIGURE 3. COEFFICIENTS OF THE INTERACTIONS AGE IN 1974* PROGRAM INTENSITY IN THE REGION OF BIRTH IN THE WAGE
AND EDUCATION EQUATIONS
with valid wage data. Thus, on average, the
program caused a 3 to 7 percent increase in the
wages of this cohort.
In Table 6 (panel B), I present the estimates
of equation (5) for different subsamples. The
variations of the effect of the program on
wages across subsamples parallel those on
education. In particular, the program had no
effects on wages in regions where it had no
effect on years of education. This suggests
that the program effect on wages was caused
by the changes in years of education. In the
next section, I use this to construct instrumental
variables (IV) estimates of the effect of
education on wages.
IV. Estimating Returns to Education
The identification assumption that the evolution
of wages and education across cohorts
would not have varied systematically from one
region to another, in the absence of the program,
is sufficient to estimate the impact of the program.
Additionally, if we assume that the program
had no effect on wages other than by
increasing educational attainment, one can use
this program to construct instrumental variables
estimates of the impact of additional years of
education on wages. The most serious concern,
for this interpretation, is that the program might
have affected both the quality and the quantity
of education, and that changes in wages could
reflect both effects. I examine below whether
there is evidence that this occurred.
A. Two-Stage Least-Squares Estimates of the
Returns to Education
Estimates of equation (3) are of intrinsic interest
because they provide an assessment of the
impact of the program on education. But they
also represent the first stage of a two-stage leastsquares
(2SLS) estimation of the impact of
education on wages. Consider the following
equation which characterizes the causal effect
of education on wages:
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 807
(8) Yijk = d + aj + Pk + SyIk b + TIjk
where cj and Pk denote region-of-birth and
cohort-of-birth effects, respectively. Note that the
returns to education are measured in 1995. If the
program was large enough to have general equilibrium
effects on the returns to education, this
will therefore be reflected in the estimates.
Ordinary least-squares (OLS) estimates of
equation (8) may lead to biased estimates if
there is a correlation between Nijk and Sijk.
However, under the assumptions that the differences
in wages across cohorts would not have
been systematically correlated with the program
intensity in the absence of the program, and that
the program had no direct effect on wages, the
interactions between the age in 1974 and the
program intensity in the region of birth are
available as instruments for equation (8). These
instruments have been shown to have good explanatory
power in the first stage. The equation
will also be estimated using a single instrument,
the interaction of being in the "young" cohort
and the program intensity in the region of birth.
Equation (8) can also be modified to incorporate
control variables as follows:
(9) Yijk =d + aj + bk + Sikb
12
+ E (Cjdi)YIr + TijkI
=2
The results are presented in Table 7, panel Al
(panel A2 presents results with the logarithm of
monthly earnings as the dependent variable).
The first line shows the OLS estimate. The
estimated return to education is 7.8 percent and
is not affected by introducing control variables.
This is lower than OLS estimates in Indonesia
in older samples, but consistent with estimates
in other Indonesian data sets of the 1990's and
with the decline in estimated returns to
education over time. The estimates reported in
World Bank (1990) decrease from 19 percent in
1982 to 10 percent in 1986.
The second line presents 2SLS estimates of
equation (9) (the F-statistics of the overidentifying
restrictions test are shown in square
brackets). In column (1), the number of children
in 1971 is the only control variable. The point
estimate (6.75 percent) is slightly lower than the
OLS estimate, although I cannot reject equality.
In column (2), I introduce interactions between
the enrollment rate in 1971 and year-of-birth
dummies. The point estimate is higher than
without the controls (8.1 percent). When I introduce
a control for the water and sanitation
program, the estimate is again slightly higher
(10.6 percent). In the third line, I present the
2SLS estimate using only one instrument. The
results are very similar to the IV estimates using
more instruments.
In Table 6, panel C, I examine whether
returns to education vary across regions.5
They are higher (11 percent) in sparsely
populated regions and in regions where the
average education level of cohorts not exposed
to the program is low (12 percent). They
seem to be lower in regions where initial education
was high, although the standard error of
this estimate is too large to be conclusive. This
last result is consistent with the idea that the
general equilibrium effect of an increase in
education is to depress the returns, but it suggests
that even after the program, returns were
still higher in regions that received more
schools.
I now turn to two potential sources of bias:
the assumption that the program had no impact
on wages other than through the increase in the
quantity of education, and problems arising
from sample selection.
B. Could Change in Quality Bias
the 2SLS Estimates?
Estimates of returns to education are biased if
the program affects both the quality and the
quantity of education. Two pieces of evidence
suggest that the program did not substantially
affect the quality of education.
First, using data from the ministry of education
and culture, I verified that changes in average
pupil/teacher ratio between 1973 and
1977 were not systematically related to the
number of INPRES schools constructed in each
region.
5 I have not presented the 2SLS estimate when the Fstatistic
for the joint significance of the instruments in the
first stage was below 2, because it would not be interpret-
able.
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808 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
TABLE 7-EFFECT OF EDUCATION ON LABOR MARKET OUTCOMES: OLS AND 2SLS ESTIMATES
Method Instrument (1) (2) (3) (4)
Panel A: Sample of Wage Earners
Panel Al: Dependent variable: log(hourly wage)
OLS 0.0776 0.0777 0.0767
(0.000620) (0.000621) (0.000646)
2SLS Year of birth dummies*program 0.0675 0.0809 0.106 0.0908
intensity in region of birth (0.0280) (0.0272) (0.0222) (0.0541)
[0.96] [0.9] [0.93] [0.9]
2SLS (Aged 2-6 in 1974)*program 0.0752 0.0862 0.104
intensity in region of birth (0.0338) (0.0336) (0.0304)
(0.0338) (0.0336) (0.0304)
Panel A2: Dependent variable: log(monthly earnings)
OLS 0.0698 0.0698 0.0689
(0.000601) (0.000602) (0.000628)
2SLS Year of birth dummies*program 0.0756 0.0925 0.0913 0.134
intensity in region of bilth (0.0280) (0.0278) (0.0219) (0.0631)
[0.73] [0.63] [0.58] [0.7]
Panel B: Whole Sample
Panel B1: Dependent variable: participation in the wage sector
OLS 0.0328 0.0327 0.0337
(0.00311) (0.000311) (0.000319)
2SLS Year of birth dummies*program 0.101 0.118 0.0892
intensity in region of birth (0.0210) (0.0197) (0.0162)
[0.66] [0.93] [1.12]
Panel B2: Dependent variable: log(monthly earnings), imnputed for self-employed individuals
OLS 0.0539 0.0539 0.0539
(0.000354) (0.000354) (0.000355)
2SLS Year of birth dummies*program 0.0509 0.0745 0.0346
intensity in region of birth (0.0157) (0.0136) (0.0138)
[0.68] [0.58] [1.16]
Control variables:
Year of birth*enrollment rate No Yes Yes Yes
in 1971
Year of birth*water and No No Yes No
sanitation program
Propensity score, propensity No No No Yes
score squared
Notes: Year of birth dummies, region of birth dummies, and the interactions between year of birth dummies and the number
of children in the region of birth in 1971 are included in the regressions. Standard errors are in parentheses. F-statistics of
the test of overidentification restrictions are in square brackets.
Second, the program did not affect the educational
attainment of individuals completing nine
years of education or more (as shown in Section
IV). However, if the quality of education had been
affected, their wages would have reflected it. I
estimated equation (2) in the sample of individuals
with an education level above 9 years. No specific
pattern emerges.6 The evidence in Table 6 can be
interpreted along the same lines: In densely populated
regions [column (4)], the program had no
effect on years of education, and it also had no
effect on wages. If the quality of education had
changed and this had affected wages, we would
see an effect of the program on wages.
These two separate pieces of evidence lend
some support to the assumption that the increase
in wages was attributed mainly to the increase in
the quantity of education. There is no clear evidence
that the program significantly altered the
quality of education.
6 A figure is shown in the working paper version (2000)
of this study.
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 809
D. Correction for Sample Selection
The returns to education are estimated in a
selected sample: Only 45 percent of the individuals
in the sample are working for a
wage, with most remaining individuals being
self-employed.
The probability of working for a wage is
potentially affected by education. To examine
this, I use 2SLS to estimate
(10) wijk - d + aj + bk + eijkA
12
+ E (Cjdil)I + Thijk
l=2
where wijk is a dummy variable, indicating
whether an individual reports a positive wage.
Estimates of this equation are presented in Table
7, panel B 1. The IV coefficient range is 0.09
to 0.12. The probability of working for a wage
is indeed affected by education.
This is an interesting result, but it casts a
shadow on the validity of the 2SLS estimate of
returns to education. Because the probability of
working for a wage is affected by schooling
(and by the instruments), the sample selection is
likely to induce a correlation between the instruments
and the error in equation (9). I implement
two alternative procedures to investigate
whether sample selection is likely to be an important
problem in this case.
First, I follow a suggestion introduced by
James Heckman and Joseph Hotz (1989), later
elaborated by Hyungtaik Ahn and James L.
Powell (1993), to condition in the second stage
on the probability of selection given the instruments.
In practice, an indicator of whether the
individual is working for a wage is regressed on
the instruments, and polynomials of the predicted
value from this regression are introduced
as controls in the wage equation. The result of
the introduction of the correction for sample
selection is presented in Table 7, column (5)
(panel Al). The coefficient changes very little,
from 8.1 percent [in column (3)] to 9.2 percent.
An alternative approach is to impute an income
for self-employed individuals and examine
whether the results change when the
estimation is performed in this "completed sample."
The income and expenditure module of the
1993 SUSENAS survey, made up of 50,000
individuals, allows us to compute income for all
individuals but it does not contain the region of
birth. Households report the members' occupations
and the sector of activity from which they
derive their main source of income. I calculate
the average income derived from the main activity
of the household for cells defined by sector
(nine industrial sectors and services and four
types of agricultural activities), status, and
urban/rural residence. I then "complete" the
SUPAS sample by defining the dependent variable
as the logarithm of monthly earnings if
they are recorded in the SUPAS data (for individuals
working for wages) and the logarithm of
the average income from the SUSENAS in the
individual's occupation cell for all self-employed
individuals (multiplied by the wage inflation
factor defined as the ratio of the average
wage from the SUPAS and the average income
of wage earners imputed from the SUSENAS).7
The results are presented in Table 7, panel
B2. They must be compared to the results in
panel A2, where the dependent variable is the
logarithm of monthly earnings of wage earners.
In all cases, the estimates using the completed
sample are smaller than those using the sample
of wage earners. In the specification controlling
for the water and sanitation program it drops to
3.5 percent. This particular result is surprising,
but the fact that the returns for the complete
sample are somewhat smaller than those for the
sample of wage earners indicates that returns to
education might be higher in the wage sector
than that among the self-employed.
V. Comparing Costs and Benefits
The estimates of the program' s effect on
wages can be used to compare the costs of
building and operating the new schools to the
additional wealth they generated, under the assumption
that the increase in wages represents
an increase in human capital. Note that in this
case, the increase in wages underestimates the
total benefit generated by the program: The
increase in education is likely to affect other
7Individuals who did not work at least one hour in the
previous week do not report a branch of activity. They are,
therefore, still excluded from this sample.
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810 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
outcomes (fertility, child morbidity and mortality,
etc.). These calculations require additional
assumptions and should be taken with considerable
caution. Nevertheless, it is useful to estimate
the magnitude of the consequences of
such a large-scale program.
Using information contained in the presidential
instruction and in a study on the cost of
education in Indonesia conducted in 1971
(Daroesman, 1971), I estimated the cost of
building, staffing, and maintaining the INPRES
school for 20 years. Yearly costs are estimated
using the following formula:
C(t) = rK + rTC + W(t) 1.25
where K is the total capital cost, TC is the total
training cost of new teachers, W(t) represents
the sum of teachers' salaries at date t, 1.25 is the
average ratio of total recurrent costs over wage
costs, and r is the real interest rate (discount
rate). I present the cost-benefits analysis for
two different assumptions about the deadweight
burden of taxation (0.2 and 0.6).
Further assumptions are needed to compute
the yearly benefits of the program. First, an
important assumption is that the increase in
wages attributed to the program represents an
increase in the productivity of labor (and that
there is no general equilibrium effect on the
returns to education). Second, I assume that the
effect on (working) women and on selfemployed
people is the same as the effect on
men working for a wage. I also assume that the
share of total labor income going to people of
any given age is constant across years and is
equal to the share of total wages going to this
cohort in 1995 (which I can calculate from my
data). Thus, I estimate the benefit of the program
at date t, for a cohort c using the following
formula:
B(c, t) o aGDP(t)S(c, t)E(c)
where a is the share of labor in GDP, S(c, t) is
the fraction of total wages earned by cohort c in
year t, and E(c) is the estimated average effect
of the program on cohort c. To obtain the total
benefits for each year, I take the sum of these
benefits over all cohorts.
The relevant variable for the cost-benefit calculation
is the discounted sum of net benefits. In
Table 8, I present an evaluation of the program's
returns for the first two specifications
estimated in Table 4 and three different assumptions
about the projected growth rate of GDP
from 1996 to 2050. To evaluate the contribution
of economic growth to the benefits of the program,
I also present these results with the assumption
that Indonesia's GDP grew at a rate of
2 percent annually from 1973 to 2050.
The cost-benefits analysis is sensitive to the
specification chosen for the estimation of the
program effect and to the assumptions about
future growth rates in Indonesia. Nevertheless,
three main points emerge from this analysis.
First, a school construction program takes a
very long time to generate positive returns
(because the costs are incurred early on,
whereas the benefits are spread over a generation).
Second, the returns generated are large.
The internal rates of return range from 8.8 to 12
percent, well above the average interest rate on
government debt in Indonesia during the period.
Third, the benefits are, to a large extent, driven
by the rapid growth of Indonesia's GDP from
1973 to 1997 (which results from the fact that
each year's benefits are a fraction of that year's
GDP). If the growth rate had been very low
from 1973 until today, the net present value of
the program would actually have been slightly
negative, according to all specifications but one.
Investing in education is much more valuable,
from a government point of view, if it expects a
fast subsequent growth.
VI. Conclusion
The INPRES program led to an increase in
educational attainment in Indonesia. On average,
the estimates indicate that the program led
to an increase of 0.25 to 0.40 years of education
(0.12 to 0.19 years for each new school built per
1,000 children), and increased by 12 percent the
probability that an affected child would complete
primary school. The estimates also suggest
that the program led to an increase of 3 to 5.4
percent in wages.
Combining the effect of the program on years
of schooling and wages generates 2SLS estimates
of economic returns to education ranging
from 6.8 to 10.6 percent. These 2SLS estimates
are close to and not significantly different from
the OLS estimates. Therefore, these estimates
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VOL. 91 NO. 4 DUFLO: CONSEQUENCES OF SCHOOL CONSTRUCTION IN INDONESIA 811
TABLE 8-EVALUATION OF THE PROGRAM'S NET RETURN
Deadweight loss coefficient
0.2 0.6
(1) (2) (3) (4)
Panel A: Results
Control for year of birth*enrollment rate No Yes No Yes
First year where benefit > costs (discount rate = 5 percent)
In annual value 1996 1996 1997 1997
In discounted sum 2005 2002 2009 2005
Discounted sum of net benefits in 2050 (growth rate after 1997 = 5 percent, discount rate 5 percent)
In million 1990 U.S.$ 13,025 13,096 11,340 18,807
As a fraction of Indonesia's GDP in 1973 0.30 0.36 0.31 0.52
Divided by initial costs 24.1 24.2 21.0 35.0
Discounted sum of net benefits in 2050 (growth rate after 1997 = 2 percent, discount rate 5 percent)
In million 1990 U.S.$ 6,691 11,589 5,008 9,905
As a fraction of Indonesia's GDP in 1973 0.18 0.32 0.14 0.27
Divided by initial costs 12.4 21.4 9.26 18.3
Discounted sum of net benefits in 2050 (growth rate from 1973 = 2 percent, discount rate 5 percent)
In million 1990 U.S.$ -631.6 1,200 -2,315 -483
As a fraction of Indonesia's GDP in 1973 -0.017 0.033 -0.063 -0.013
Divided by initial costs -1.16 2.22 -4.28 -0.89
Intemal rate of returna
Growth rate after 1997 = 5 percent 0.102 0.118 0.0895 0.105
Growth rate after 1997 = 2 percent 0.088 0.106 0.0750 0.0915
Growth rate from 1973 = 2 percent 0.0443 0.059 0.0326 0.0467
Panel B: Assumptions and Parameters
Population growth rate after 1997 0.015
Yearly teacher's salary in 1973 (1990 U.S. dollars) 363
Yearly teacher's salary in 1995 (1990 U.S. dollars) 2,467
Total recurrent costs/teacher salary 1.25
Total cost of construction (million 1990 U.S. dollars) 522
Number of schools constructed 61,800
Lifetime of the schools (years) 20
Share of labor income in GDP 0.7
Notes: The estimates underlying these calculations are taken from Table 5 [columns (7) and (8)]. Program effect has been set
to 0 for children aged 7 or older in 1974.
a The internal rate of return is the interest rate such that the net present value of the project at infinity is 0.
do not support the view that OLS estimates of
returns to education in developing countries are
biased upward as a result of omitted family and
community background variables, which has
been argued by Behrman (1990), among others.
Nor do they conform to most studies in industrialized
countries, which obtain higher IV estimates
than OLS estimates [see surveys in Orley
Ashenfelter et al. (1999) and Card (1999)].
Both the OLS estimates and the 2SLS estimates
are similar to most estimates reported for
developed countries, but smaller than estimates
reported in Psacharopoulos (1994) for developing
economies. A number of specification
checks support the causal interpretation of these
estimates of the effect of the INPRES program.
However, they need not generalize to other contexts.
First, the emphasis on education in Indonesia
at the time of the program created a
context particularly favorable to its success.
Second, the program was large and could have
had general equilibrium effects on the returns to
education. Since the returns to education are
estimated for 1995, in an environment where
the education levels were higher than when the
program began, individuals' returns may be
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812 THE AMERICAN ECONOMIC REVIEW SEPTEMBER 2001
lower than they would be in other developing
countries. Finally, if returns to education are not
constant, the 2SLS estimates are a weighted
average of the returns to education for people
who are affected by the instruments (Angrist
and Imbens, 1995). The INPRES program induced
variation only at the primary school level.
Returns to secondary education may be different.
In particular, flexible OLS specifications
allowing the returns to education to vary by year
suggest that returns to education may be convex
in developing countries (Strauss and Thomas,
1995). Moreover, individuals whose education
level changed because of the program may expelience
returns to education that differ from
the population average. On one hand, those
affected children likely belong to the poorest
segment of the population because they were
prevented from attending school by the lack of
infrastructure. On the other hand, they took
advantage of the opportunity once it arose. It is
conceivable that only individuals with high expected
returns chose to do so.
The findings reported here are important
because they show that an unusually large government-administered
intervention was effective
in increasing both education and wages in Indonesia.
This intervention was meant to increase the
quantity of education. It is sometimes feared that
the deterioration in the quality of education that
might result from this type of program could offset
any gain in quantity. However, the estimates
reported here suggest that the program was effective
in increasing not only education levels but
also wages. This suggests that the combined effect
of quality and quantity changes in education was
an increase in human capital.
This study concentrated on estimating the
private returns to education. This large increase
in the education of the young cohorts, however,
may have had a broader impact on the Indonesian
economy. How did the economy adjust to a
shock in the supply of educated workers?
Studying these effects will be the object of
future work.
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