The Impact of Preprimary Construction on Primary school
Progress in Rural Guatemala
*May, 2011
Nicolas Luis Bottan
Masters Thesis
Universidad de San Andrés
Advisors: Julian Cristia and Paulo Bastos (Inter-American Development Bank)
Abstract
This paper estimates the impacts of opening a preprimary in rural communities on primary school progression in Guatemala. Using administrative school-level data from 1992 to 2006 and a difference-in-difference approach, this paper exploits a large-scale construction program that increased the number of preprimaries in Guatemala from 4,200 to 7,000 between 1998 and 2005. Results indicate that opening a preprimary increases first grade promotion rate by 2.4 percentage points (4.5 percent of the baseline level) in the first grade though no statistically significant impacts are found for second and third grade. The effects are more pronounced for females. Impacts are modest compared to the previous evidence from more developed countries.
1. Introduction
The evidence on the effects of large-scale preprimary expansion is limited and
mostly circumscribed to high and middle-income countries. Cascio (2009) uses data from
four decennial censuses and exploit the state-by-state expansion of Kindergarden in the
US to estimate long term impacts. She finds that whites affected by the expansion are less
likely to drop out from high school and to be in incarcerated or in a mental health facility
but no effects are found for blacks. Berlinski et al (2008), using data from siblings in
Uruguay, finds that preschool attendance generates large effects in the probability of
going to school by age 15. Finally, Berlinski et al (2009) analyze a large preschool
construction program in Argentina and finds that one year attendance to preprimary
produces sizable increases in third grade test scores as well as improvements in children
behavior in class.
It is difficult to extrapolate these findings to less developed countries. Shifting a
child from a poor home environment to attend preprimary may have a lower opportunity
cost in settings where her mother’s education is low. On the other hand, the quality of
education may be sensibly lower in poor countries compared to the countries referred to
above. The effects can potentially be negative since they are highly dependant on the
quality of the center attended and the quality of maternal time (Baker et al., 2008;
Almond and Currie, 2010).
This paper aims to contribute to this literature by exploiting a unique large-scale
preprimary expansion in rural Guatemala, where large segments of the indigenous
population live in poverty. As a consequence of signing the Peace Accords that ended 36
program that almost doubled the number of preprimary schools between 1998 and 2005
from 4,200 to 7,800.
Longitudinal school-level administrative data from 1992 to 2006 are combined
with Population Census data from 2002 matched at the community level to estimate
impacts of opening a preprimary in a rural community on the promotion rate in primary
school. The very precise geographic information allows constructing a panel data of
primary schools that are unique in their communities during the period analyzed (i.e.
there was no other primary school in the community) and that did not have a preprimary
constructed by 1997 or after 2001. Impacts are estimated by exploiting the variation
across primary schools over time regarding the introduction and timing of preprimary
construction. Focusing on rural communities with only one primary school tackles the
potential problem that the opening of a preschool annexed to a primary school may affect
the student composition attending the primary school. The research design is similar to
the one used by Duflo (2001) and Berlinski et al. (2009) but sharper variation can be
exploited in the variable of interest due to the use of very disaggregated geographical
information.
Results indicate that opening a preprimary annexed to a primary school increases
promotion rates in the first grade by 2.4 percentage points (4.5 percent of the mean). No
effects are found for higher grades associated to preprimary construction. These results
are robust to the introduction of time-varying controls, the use of trimming and
propensity score weighting techniques, controlling for differential trends at different
geographic aggregation levels as well as changes in the age-structure of the cohort
the robustness of the results are provided documenting similar pre-treatment trends
between schools that had a preprimary annexed and those who had not as well as running
placebo tests for higher grades that should have not been impacted by the program during
unexposed years. Furthermore, there is no evidence suggesting the existence of spillover
effects to other communities.
Regarding heterogeneity of impacts, the impacts on girls are significantly larger
compared to boys for repetition rates. Greater impacts for girls are of significance given
the documented large impacts of mothers’ education on fertility, children’s health and the
larger intergenerational transmission of education between mothers and children (Martin,
1995; Glewwe, 1999; Black et al., 2005). This finding mimics the results from several
studies in the US and other developed countries where larger impacts have been found for
girls (Oden et al., 2000; Anderson, 2008; Cascio, 2009; Havnes and Mogstad, 2009).
Section 2 of this paper provides a general background of education in Guatemala
and a description of the construction program. Data and the empirical strategy followed
are presented in section 3. The main results are discussed in section 4, followed by
various robustness tests in section 5. Finally, the last section concludes.
2. Background
2.1. Primary and Preprimary Education in Guatemala
Guatemala is considered a low middle income country. Around half of its 13.7
million inhabitants live in rural areas and a similar fraction is indigenous.1 The significant
inequality in the country explains high poverty (51 percent) and extreme poverty rates
(15 percent) which are concentrated in indigenous, rural populations. Life expectancy at
birth reached 69.9 years in 2006, compared to 72.9 years for the rest of the Central
American countries. Similarly, infant and child mortality rate (31 and 21 deaths per 1000
live births, respectively) are significantly higher in Guatemala compared to the rest of
Central America (41 and 25, respectively).
Illiteracy is high, 23.7% of individuals between the age of 18 and 49 have no
formal education (Living Standards Measurement Survey – LSMS, 2006). Primary
school coverage is practically universal, though the quality of education is considered
low. Alvarez (2007) finds that Guatemalan teachers use inadequate teaching methods
given the cultural barriers and socio-demographic context. Primary school repetition and
dropout rates are very high, especially during the initial grades (e.g. in first grade they
reach 30% and 14%). As a result, Guatemala has one of the lowest average accumulated
years of education in Latin America (Calderón and Urquiola, 2006).
Several factors contribute to such poor performance. Almost 40% of the child
population does not speak Spanish natively and fare worse than native-Spanish speakers.
In addition, parent’s education is low in rural areas and anecdotal evidence suggest that
education is not greatly valued in this context since child’s aspirations are to work in
agriculture related activities or housework (Rodríguez, 2001). Also, low income levels
seem to be a factor when deciding whether to enroll or withdraw a child from school
(Alvarez, 2007). Finally, studies have shown that the high rates of malnutrition are
associated to a 50% larger probability of dropping out, and double the chances of
Primary education in Guatemala has been compulsory since 1985. However,
parents have to pay a small fee (between $0.60 and $5 for tuition) to cover operational
costs related to running the school (e.g. electricity bills).2 Preprimary attendance is
compulsory as well, though this not enforced due to low coverage. It covers children aged
4 to 6. First grade is typically started at the age of 7, though this is not strict.
2.2.Preprimary Construction
In 1996, the signing of the Peace Accords ended 36 years of harsh civil war. As
part of the Accords, the national government agreed to expand basic education and health
services in rural and indigenous areas with inadequate coverage. In education, the
government embarked in an ambitious preschool construction program that resulted in
increasing the number of public preprimaries from approximately 4,200 in 1998 to 7,800
in 2005 (see Figure 1). Preprimaries were usually constructed as annexes to primary
schools.
Regarding the selection of beneficiary communities, according to former
government staff this was a two-step process. In the first step, agents at the regional
offices of the Ministry of Education identified eligible communities as those that have
enough number of preprimary school aged children that lacked adequate access. As a
result, lists of eligible communities were constructed at the regional level. In the second
step, final decisions were made at the central level. The procedures were quite ad hoc and
it is suggested that political considerations played a significant role.3
2 Though this was a base charge, schools later could charge for materials, meals, etc. There is no data on this.
3. Data and empirical strategy
3.1. Data
This paper uses school-level administrative data obtained from the Ministry of
Educationfor all primary schools from 1992 until 2006. At the start and end of the school
year, each operating educational establishment (e.g. preprimary, primary, high school)
has to send information by grade and sex on initial enrollment, number of children that
drop out during the year, and final enrollment (along with number of children that were
promoted). Data disaggregated by age was reported as of 1995.
This is combined with 100% samples of the Population Censuses data for 1994
and 2002. The data contains basic socio-economic characteristics at the household and
individual level. Important for in the analysis, the geographic location of the household is
identified at the community level and it is possible to match communities from the 1994
to the 2002 Population Census.4 Additionally, the National Institute of Statistics provides
geo-referenced information for communities in the 2002 Population Census.
Finally, an infrastructure census of primary and preprimary schools was
performed in 2005 which provided information about the school location. This
information allows matching primary and preprimary schools at the community level and
also provides geo-referenced information.
3.2. Research Design
The empirical strategy of this paper exploits the variation across primary schools
over time regarding the introduction and timing of preprimary construction, comparing
trends in promotion rates. This type of strategy has been previously used evaluating the
effects of primary and preprimary school construction programs by Duflo (2001) in
Indonesia and Berlinski et al. (2009) in Argentina. However, while in these two papers
the intervention variable (school construction) is defined at a somewhat aggregate level,
in this paper the intervention variable is defined at the school level. The differences in
aggregation are apparent as in the case of the Indonesia’s study, program construction is
defined over 255 districts, in Argentina’s study it is defined over 407 municipalities
whereas in this study the final sample includes 2,753 communities.
There are two advantages of having the intervention defined at a lower level of
aggregation. First, estimates are more efficient as there is increased variation in the
variable of interest. Second, the sharper changes over time in the variable of interest may
reduce the potential for confounding the impacts of the program with differential
underlying trends across geographical units. However, in all cases there exists an
assumption of absence of “spill over” effects that needs to be maintained to yield
unbiased estimates. That is, opening a preprimary school in one geographical unit
(treated) should not induce that individuals in non-beneficiary units start attending the
treated school. If that happens, estimates are attenuated as individuals in the
non-beneficiary units are also affected by the intervention.
Spill-over effects are assumed to be minimized in this context due to clustering of
population in communities and that the rugged geography and poor infrastructure makes
communities. Anecdotal evidence suggests that cultural factors related to a strong sense
of belonging to living in certain community reduce the possibility of seeking services
outside the own community. Moreover, the availability of geographic coordinates for
schools and communities are exploited to test for spill-over effects and find that indeed
they are non-existent.
The measure of school success used is promotion rates. Promotion is defined as
the fraction of children that pass the grade at the end of the school year. Though in some
cases children that were not promoted at the end of a year are able to progress to the next
grade passing an exam at the beginning of the following year, data limitations impedes
the identification of these cases.
Attention is restricted to this indicator, as opposed to analyzing impacts in test
scores, due to data restrictions. Nonetheless, examining impacts on promotion is of
interest for several reasons. First, under the assumption that students below certain
threshold are assigned to repeat the grade, impacts on repetition rates signal impacts on
learning at least for students in the margin of repeating. Second, the accumulated
evidence from preschool evaluations in the US suggest that impacts on test scores tend to
fade out quite rapidly whereas as children age positive effects on school progress and
other non-cognitive outcomes arise (Almond and Currie, 2010). Hence, impacts on
repetition can indicate effects on accumulated years of schooling in the absence of
changes in age at school exit. Third, in many developing countries high rates of repetition
and school dropout and re-entry causes increased expenses and problems associated to
3.3. Sample Construction
Table 1 presents descriptive statistics for the construction of the sample of
primary schools using data for 1994. Column 1 contains all primary schools in the
country. The top panel presents school information generated from administrative records
whereas the lower panel presents community data constructed from the 1994 Population
Census. The total number of primary students at that time was over 1.4 million; there are
over 10 thousand schools in the country, 20% are private institutions. The department of
Guatemala is dropped since it is the most urbanized and differs greatly from the rest of
the country in terms of infrastructure and health conditions. Private institutions are also
dropped from our sample (column 3) since they operate independently and the choice of
building a preprimary would be endogenous. School characteristics almost do not change
when applying these restrictions.
The administrative data reported by primary schools does not allow directly
linking them to preprimaries in the same communities. To do so, the Infrastructure
Census implemented in 2005 is used. This covered most of the public schools. Some
schools are lost in this match because their communities were not surveyed but sample
characteristics do not change (column 4). Because preprimaries opened after 2005 cannot
be linked to their respective school, this study restricts to openings up to the year 2005.
Around 90 percent of schools were matched to the respective community in the Census;
again, sample characteristics do not vary markedly (column 5).
As described, the research design involves restricting attention to rural
communities that have only one school (column 6). School and community
infrastructure and lower average adult education. Finally, the sample is restricted to
schools that do not have a preschool in 1998 to be able to test whether pre-intervention
trends are similar in schools were a preprimary is opened compared to those that
continued operating without a preprimary along the period (column 7).5 Hence, the final
sample contains rural primary schools that are unique in their communities and that did
not have a preprimary by 1998.
To analyze differences in beneficiary and non-beneficiary primary schools, Table
2 presents descriptive statistics during the pre-intervention period (1992-1998). There are
very small differences in promotion rates across groups though treatment schools are
somewhat larger. Comparing community characteristics based on the 1994 census, there
is evidence that beneficiaries tend to have a larger percent of indigenous population and
characteristics associated with better socio-economic status and infrastructure. This result
suggests that selection may have been tilted towards areas with high indigenous
population but with better infrastructure services.
Table 3 explores the selection process further by predicting whether a preprimary
was constructed in a community using the set of school and community characteristics
described. In column 1 observe that preprimaries were more likely to be constructed in
communities of larger size, with better infrastructure and average education, and with
larger indigenous populations. This could have been a way to increase services to the
indigenous population, as agreed in the Peace Accords, but targeting communities with
lower costs associated to preprimary construction (proxied as those with better
infrastructure). Columns 2 and 3 introduce department and municipality fixed effects to
check whether this type of selection was present within these geographical areas.6 Results
indicate that most of the coefficients are reduced approximately by half, except for school
enrollment in first grade, which remains unchanged under all specifications. Given the
evidence of smaller selection within these geographical levels, in the main specification
the interactions in department and year are controlled for so as to adjust by differential
trends across departments. Moreover, in alternative specifications in the robustness
section, linear trends in municipalities are added to exploit variation within municipalities
over time.
4. Results
4.1. Impacts on School Progression
To estimate the impacts of preprimary construction on primary school
progression, a panel is constructed where the unit of observation is defined at the
school-grade-year level. The indicator of interest, exposure to preprimary (PS), is set to one if
students in the school-grade-year that have progressed adequately had the opportunity to
attend preprimary. That is:
(1)
where T represents the year a preprimary was opened, and i, t and g indexes school, year
and grade.7 Children in first grade would not have been exposed to preprimary until T+1.
Therefore, the PS variable for that grade and school will take the value of 0 until , then
6 There are 23 departments in Guatemala that are similar to states in the US. Municipalities are analogous to counties and there are 330 in the country.
7 Primary schools in communities where no preprimary was opened will have PS equal to 0 for all
1 from onwards. For second grade, the indicator will take the value of 0 until T+1
and then 1 from T+2 onwards and similarly for other grades.
To identify the impact of preprimary construction on promotion rates, the
following baseline model is estimated:
€
Yi,t g
=α0+βPSi,t
g
+ψt+ηi+λd,t+εi,t
g (2)
where
€
Yi,t
g is the outcome of interest (dropout or repetition rate) in grade for school
in year , is a set of year fixed effects, are school fixed effects, and is a set of
department-year fixed effects controlling for time varying shocks at the department level.
The parameter of interest captures the average effect of opening a preprimary in a
community on repetition and dropout rates of students in the community. This is an
“intention-to-treat” (ITT) parameter. It is different from estimating the effect of attending
preprimary on the analyzed outcomes. However, it is highly relevant from a policy
perspective as it shows the final effect of expanding preprimary coverage on primary
progression.
Table 4 present the estimated effects for two specifications. The basic model
described above is presented in the uneven numbered columns, and municipality linear
time trends are introduced in even numbered columns to account for possible differential
trends across municipalities.8 Each column in the table corresponds to a separate
regression. In the first grade, a statistically significant, though modest, effect of preschool
construction is found for promotion rate. For the basic specification, opening a
preprimary increases promotion rate by 2.6 percentage points in the first grade (4.9
percent of baseline levels). Comparing even and odd Columns, results are robust to the
inclusion of municipality linear time trends.9
The construction of preprimaries does not seem to have positive effects in the
second and third grade. The interpretation of this zero effects should be done cautiously.
On one side, not finding negative effects is encouraging since it would reflect only very
short term gains of attending a preprimary (for example, they only prepare the children
with sufficient skills to pass the first grade). The most probable explanation for not
finding impacts in higher grades is changes in class composition. This will be addressed
in greater detail in section 5.3.
These results suggest that there are modest effects of opening a preprimary on
primary school progression and that they are concentrated in the first grade. These results
contrast to previous evidence from Argentina and Uruguay that documented sizeable
effects of attendance to preprimary on test scores in primary and school progression
(Berlinski et al., 2008; Berlinski et al., 2009).10 In Argentina, attending one year
preprimary increased test scores in Math and Spanish in third grade about 0.23 standard
deviations. In Uruguay, attending preschool was associated with an increase in the
probability of attending school at age 15 of 27 percentage points. Still, large differences
in the estimated impacts across the studies should be expected given the great variation in
the underlying economic and social structure. For example, average mothers’ education
9 In all regressions in the paper standard errors are clustered at the school level.
in the Uruguay study amounted to 9.8 years whereas in the communities included in our
study average education for women 20 to 40 years old is only 3.2.
Previous studies for the US have stressed that the impacts of attending a preschool
will be a function of the quality of maternal time at home versus the quality of the
stimulation in the center-based care. As mentioned, education levels for mothers in the
context analyzed are very low which would suggest a small cost for children of not
receiving home stimulation, at least in terms of skills related to school readiness.
However, several reports suggest that the quality of preprimary education in Guatemala is
quite low (Rubio, 2001; UNICEF, 1996).
In table 5, alternative specifications are used to test the robustness of the main
estimates. Column 1 presents the baseline model (note that each coefficient corresponds
to separate regression). Time-varying controls, obtained from extrapolating data between
the 1994 and 2002 population census, are added in column 2. To increase the similarity
between the treatment and comparison groups, trimming and propensity score
reweighting techniques are used in column 3. To do so, the probability of receiving a
preprimary is predicted as a function of pre-treatment school and community
characteristics and drop communities with probability of treatment higher than 0.75 or
lower than 0.15. Next, observations are re-weighted in the comparison group applying a
factor of PropScore/(1-PropScore) where PropScore refers to the estimated probability
of treatment and estimate the basic specification in the trimmed and reweighted sample.
Finally, column 4 presents results when the sample is enlarged to include primary schools
that have a preprimary constructed between 1993 and 1998. The main findings are robust
4.2 Heterogeneous impacts
This subsection explores heterogeneous impacts across different groups defined
by gender, school infrastructure quality, average adult education, and proportion of
indigenous population in the community. Results are presented in Table 6. The first two
Columns present results for males and females respectively. In this particular case, the
data is restructured in such a way that the unit of observation is now the
school-grade-year-sex. The positive and statistically significant effect of constructing a preprimary is
almost three times larger for females than males (3.7 percentage points versus 1.5). Such
a large difference between genders indicates that the overall effects estimated are driven
mainly by the impact preprimary construction has on females. As noted, the literature that
evaluates preschool programs in the US emphasizes that impacts are typically larger for
girls (Oden et al., 2000; Anderson, 2008; Cascio, 2009). However, the referred studies
about attendance to preprimary in Argentina and Uruguay did not find differential effects
across gender.
Gender inequality in Guatemala is amongst the highest in Latin America
(Hausmann et al. 2008). Anecdotal evidence suggests that indigenous girls fare worse
than boys in terms of cognitive development. This could be explained by the cultural
context as young girls are kept close to their mothers while they work, while boys are
free to explore and play. This difference in stimulation environment at home may explain
the larger effects of attending preschool for girls.
As noted, the modest effects found might be explained by the low quality of
preprimary education in this context. Though a direct test of this hypothesis is unfeasible,
community as a proxy for the quality of preprimary education. Using data from the 2005
Census Infrastructure, a quality score is constructed based on ranking the type of material
and its condition, averaged over all categories (i.e. ceiling, roof, walls, floor). The sample
was then divided by the median into two groups: low and high quality. There are no
differential impacts across these two groups (columns 3 and 4). However, this proxy is
quite crude and, additionally, it can be correlated with the quality of home stimulation
which makes isolating the differential impacts of preprimary of varying quality difficult.
Columns 5 and 6 present the impacts when dividing the sample according to the
median fraction of indigenous population in the community. Similarly, in columns 7 and
8 the sample is divided using the median average education in the community. In both
cases, there is no evidence of differential impacts by indigenous status or education.
Finally, assume that ability development in preprimary is a function of quantity
and quality of stimulus. Holding quality constant, it is plausible to assume that receiving
more stimuli during early childhood should be correlated to improved learning. This can
be tested indirectly by looking at class size. In smaller classes, a child receive higher
direct exposure to the teacher, therefore receiving more stimulus than a child in a large
classroom. This is tested in columns 9 and 10. Indeed, there are higher effects for small
classrooms in comparison to large ones in the same magnitude as the difference between
5. Robustness
5.1. Testing for Differential Pre-Intervention Trends
Identification of the parameter of interest relies on the assumption that, in the
absence of the treatment, outcomes in the intervened primary schools would have
evolved in a similar fashion as those from the comparison group. Although this
assumption cannot be tested directly, some evidence on its validity can be provided by
studying pre-intervention trends (Heckman and Hotz, 1988). In order to test differences
in trends the baseline model is estimated replacing the treatment variable (PS) by the
interaction of a dummy that takes the value of 1 if the school ever has a preprimary
constructed (0 if not), with year dummies. This interaction will give you the average
difference between both groups every year.
Figure 2 plots the coefficient of the interaction of the eventually treated dummy
with year dummies with the respective 95% confidence intervals. The number of
accumulated preprimaries is shown in the bars in the background. For first grade (Panel
A) there are no significant differences during the pre-intervention period. In 1998 the first
wave of preprimaries are constructed and the difference is still zero. This is expected
since the first cohort of exposed children do not enter primary until the year after. This is
confirmed by the discrete positive jump in the following year. Remember that before a
preprimary is constructed there are children under the age of 7 enrolled in first grade.
Suppose that all of these children repeat the first grade. The positive impacts found could
be purely the mechanical result of moving these children out of the first grade. If this
were true, then the positive jump observed in 1999 should actually be seen the previous
For second grade (Panel B), the differences are not statistically significant
although a small positive gradient is observed 2 years after the first preprimaries are
constructed. For third grade (Panel C) there is no suggestive evidence of differences
between both groups.
5.2. Testing for Contemporaneous Changes in Primary School Quality
It is possible that primary schools that have a preprimary annexed in the sample
also receive other contemporaneous interventions that may potentially change the quality
of education that the school provides. This could generate a bias in the estimated
coefficient because it would pick up the effect of these other changes in school inputs that
are taking place at the same time when the preprimary is opened. Again, this cannot be
tested directly but evidence about it may be provided. To that end, this subsection tests
whether the introduction of a preprimary was correlated with changes in outcomes in
grades that should not have been exposed given the timing of the opening. For example,
if in certain school a preprimary was opened in year T, it should not affect outcomes in
grade 2 in year T+1. For this exercise, the coverage variable is defined as:
where is the year the preschool is constructed, independent of the grade. All
observations corresponding to the years exposed cohorts potentially reach each grade are
dropped (e.g. T+2 and later years for grade 2). Taking these changes into account, the
baseline model is re-estimated. Results are presented in Table 7. There are no statistically
significant coefficients for all grades and all specifications suggesting that
5.3. Preprimary Opening and Age-Composition
As explained previously, it is plausible that the opening of a preprimary in a
community may change the composition of the cohort of students that enters first grade.
In particular, changes in the age composition of students in first grade may produce
changes in the outcomes analyzed making the attribution of the estimated impacts solely
to the intervention under analysis difficult. In fact, 7.1% of children in treatment
communities during the pre-intervention period attend first grade before reaching the age
of 7. Hence, it can be expected that in the absence of preprimary, some children would
attend first grade before reaching the age of seven will attend preprimary and start
primary at the adequate age.
In 1995, primary schools started reporting enrollment by age. Taking advantage
of this, the impact of preschool construction on the percentage of children under the age
of 7 and enrollment in first grade are estimated. The coverage indicator is now defined as
, where is the year the preschool is constructed. Table 8 presents the
estimates for the baseline model using data from 1995 to 2006. The effect of constructing
a preschool is statistically relevant and reduces the proportion of children under the age
of 7 in first grade by 3.1 percentage points (columns 1 and 2). At the same time,
enrollment is reduced by 1.2 children and is statistically significant (columns 3 and 4).
Hence, the introduction of preprimary may have impacted the age structure of the cohort
entering first grade but, quantitatively, the effect is relatively small.
Since age composition and enrollment is changing in first grade as a cause of
preprimary construction, the next step is to explore whether the estimates of preprimary
change in age composition of students. Though the age composition of first grade is also
affected by the direct effect of the intervention on students’ progression and hence it is
endogenous, this channel could be biasing the results in a substantive way. The original
model is re-estimated controlling for the proportion of students under the age of 7 in first
grade (and lag it for second and third grade). Estimates are presented in Table 9. The
results are not sensitive to controlling for composition. They are consistent throughout
specifications and grades. This is tentative evidence that the channel of varying age
composition in entering primary school does not seem to be affecting seriously the
results.
So far, one interpretation of the modest effects of preprimary construction has
been low quality of education in Guatemala. An alternative explanation is changes in
class composition attenuating the effects. The problem of changing class composition is
aggravated for higher grades. The optimal way to analyze this problem would be to
define the data at the cohort level and take advantage of the administrative data
disaggregated by grade-age. This approach is followed in Bastos et al (2011) where larger
impacts associated with the construction of preprimaries are found, in line with the
existing evidence documented in other developing countries.
5.4 Testing the “island assumption”
One of the central aspects of this study is the assumption that the schools in the
final sample analyzed are isolated and the possibilities of spillovers (or changes in school
composition) are minimal. For example suppose there are two nearby communities (A
community. If a preprimary opens in A and the potentially “good” students from B were
changed to A by their parents, the positive effects found could be attributed to attracting
better students from other communities and not to the program. Two different tests are
proposed.
First, the sample is restricted to schools that do not have another school at a
distance of 1 or 2 kilometers. Note that these distances are measured as straight lines and
do not accurately reflect distance between two locations because of the mountainous
geography of the country and poor transport infrastructure. The estimates are presented
in Table 10. When restricting to unique schools in a 1-kilometer radius the point estimate
and statistical significance do not change. When increasing the radius to 2 kilometers,
sample size decreases substantially but point estimates are similar in magnitude and
significant at the 10% level. This first test assumes that being at a larger distance from
another school decreases the probability of spillovers.
The second test proposed tackles the case in which children from B attend
preprimary at A and later return to B for primary. To do so, the treatment of the closest
treated school in a 2-kilometer radius is assigned to each control school. The sample is
then restricted to control schools only and the baseline regression is estimated using the
newly assigned treatment variable. The results for this exercise are presented in Table 11.
If children were to attend preprimary in a different school and then return to their
community, it is to expect that effects will be captured by the newly assigned treatment
variable. The coefficients are not statistically relevant, suggesting that there are no
6. Conclusion
Many developing countries are considering expanding preprimary coverage as a
way to improve human capital accumulation. Great part of the attractiveness of this
policy option is that it can be accomplished expanding primary schools “downwards”,
which in many cases involves limited infrastructure investments and can be relatively
easily accommodated within existing government structures. Evidence from the US,
Uruguay and Argentina suggest large returns. However, whether these results can be
directly extrapolated to significantly poorer populations require very strong assumptions.
This paper aims to contribute to fill this gap by exploiting a large-scale expansion
in preprimary coverage in Guatemala between 1998 and 2005. School-level
administrative data for public rural primary schools are used to estimate the impacts of
opening a preprimary on primary school progression using a differences-in-differences
approach. Modest impacts are found: the intervention increases promotion rates in first
grade by 2.4 percentage points. No significant impacts are found for higher grades,
though this should not be interpreted as not having any longer-term impacts.
These results are reconciled with existing evidence by pointing to potential
significant differences in the quality of the education provided. However, the most likely
explanation for the modest effects is the impossibility of disentangling the effects
between potentially exposed and not exposed cohorts. These are indistinguishable within
each grade in the way this study addresses the empirical identification. A study by Bastos
et al (2011) tackle this issue by defining the unit of observation at the cohort level and
Future studies that use individual-level data and experimental designs may
provide more definitive answers regarding the impacts of expanding preprimary
coverage. Still, evidence from large-scale expansions most surely will be generated using
non-experimental approaches that exploit significant policy shift as the one examined
here. Together, they can inform about effective ways to increase human capital in less
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-‐500 0 500 1,000 1,500 2,000 2,500 3,000 3,500 4,000 4,500
Figure 2
Difference between eventually treated and control schools
-‐0.05 -‐0.04 -‐0.03 -‐0.02 -‐0.01 0 0.01 0.02 0.03 0.04 0.05
Panel A - 1st grade
-‐0.05 -‐0.04 -‐0.03 -‐0.02 -‐0.01 0 0.01 0.02 0.03 0.04 0.05
1993 1994 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 2005 2006
-‐0.05 -‐0.04 -‐0.03 -‐0.02 -‐0.01 0 0.01 0.02 0.03 0.04 0.05
1993 1994 1995 1996 1997 1998 1999 2000 2001 2002 2003 2004 2005 2006
