Income growth, school enrolment and the gender gap in schooling: evidence from rural Pakistan.
Jacoby, Hanan G. ; Mansuri, Ghazala
Household panel data document a remarkable closing of the gender
gap in school enrolment in rural Pakistan between 2001 and 2004. During
this 3-year period, there was an 8 point increase in the percentage of
girls entering school, while the corresponding increase for boys was
less than 2 percentage points. More than half of the rise for girls can
be explained by the substantial increase in household incomes, whereas
comparatively little is accounted for by increased school availability.
Unpacking these enrolment trends and their determinants requires solving
the classic period-age-cohort identification problem. The paper shows
how to do so using auxiliary information on the distribution of school
entry ages.
JEL Classification: 015, 040, I 25, 121
Keywords: School Enrolment, Gender, Income Growth, Gender Gap
1. INTRODUCTION
Large gender gaps in schooling persist in much of South Asia and
yet are still not well understood. How much of the lower female
enrolment and attainment relative to males can be explained by
differences in the gender-specific returns to education [e.g., Behrman,
el al. (1999)], by poverty, or by other barriers to schooling that
differentially affect girls is the central question in formulating and
targeting policies to address the gender gap in educational outcomes.
Pakistan, historically, has had one of the largest education gender
gaps in the world, being especially pronounced in rural areas [Alderman,
et al. (1996)]. While this gap has been closing over time, it remains
high. Moreover, there is substantial variation in the gender gap within
the country, with the two largest provinces providing a dramatic
contrast. Girls' enrolment has been substantially higher in Punjab
than in Sindh, even though the difference in boy's enrolment across
these two provinces has been slight. How much of this cross-sectional
variation in the gender gap in schooling can be attributed to the
greater poverty in Sindh relative to Punjab?
Recent economic trends in Pakistan can help answer this question.
Rural incomes grew robustly from 2001-04, largely due to external
factors, such as the easing of drought and increased remittances in the
aftermath of 9/11. This income growth was thus not driven by
technical progress that might have also altered the relative
returns to education or the shadow price of child (or adult) time.
Furthermore, the percentage growth in rural incomes between 2001 and
2004 was of the same order of magnitude as the baseline cross-sectional
income differential between rural Punjab and Sindh. Our principal
objective is to estimate the extent to which household income explains
gender-specific enrolment patterns in rural Pakistan.
To be sure, there were other salient developments over this same
period, notably the continuing construction of rural schools. Alderman,
et al. (1996), in their analysis of a cohort of rural Pakistanis born in
the 1960's, find that lack of local schools for girls was the main
source of the gender gap in cognitive skills. To assess the relevance of
this conclusion for recent cohorts, we also consider the role of school
availability. Of course, new school construction may reflect increasing
local demand for education, which itself could be a function of income
growth. Given the lag in school construction, however, the establishment
of schools after 2001 should largely reflect income growth (or other
trends) prior to 2001.
A large and expanding literature examines the impact of income
shocks on transitory (year-to-year or season-to-season) changes in
school enrolment or attendance [e.g., Duryea, et al. (2007); Jacoby and
Soufias (1997)]. Less empirical attention has been paid, however, to
longer-run processes underlying trends in school entry decisions (i.e.,
ever enrolled). Glewwe and Jacoby (2004) use household panel data to
show that income growth led to a rise in school enrolment in Vietnam in
the mid-1990s. Their paper does not focus on school entry, but rather
conflates entry and dropout behaviour, nor does it consider gender
differentials in enrolment trends. By contrast, our interest is in
whether a child was ever enrolled in school, an important decision
margin in a setting where a large fraction of children, particularly
girls, never go to school.
In order to unpack enrolment trends and their determinants using
data on cohorts of young children one must first solve the classic
period-age-cohort effect identification problem. Because of the linear
relationship between year, age, and cohort, it is generally impossible
to separate their independent effects, even with panel data. Our
approach uses auxiliary information on the distribution of the age of
school entrants to back out the change in probability of ever enrolling
in school during childhood. Once this age effect is 'purged',
period and cohort effects can be separately estimated without having to
make any ad hoc identifying assumptions.
Using this method, we find an 8 percentage point increase in the
proportion of girls who ever enrolled in school between 2001 and 2004.
This is an average increase across al! cohorts among children aged 5-12
in 2001 that could potentially have enrolled in school in response to
changing economic conditions', i.e., The corresponding figure for
boys is between 1 and 2 percentage points and is not statistically
significant. Important cohort effects are also found for girls, but not
for boys. Practically all of the movement in girls' school
enrolment over the sample period occurred in Sindh; the 2001-04
cross-cohort enrolment increase for girls is 13 percentage points there,
but only 2 percentage points in Punjab. Thus, in rural Sindh, the gender
gap in school entry fell by about 9 percentage points in just 3 years.
Increases in household income explain around sixty percent of the
overall increase in girls' school enrolment, whereas the
establishment of new schools plays only a minor role. It is possible
that policy efforts to increase enrolment among girls such as Tawana
Pakistan or the middle school stipends program for girls may account for
some of the increased enrolment. Male work migration rates from Sindh
also rose in the post 2001 period. Mansuri (2006) has shown a
substantial impact of migration on school enrolment, particularly for
girls.
The paper presents in Section I a simple description of enrolment
trends in rural Pakistan, followed in Section 11 with a more
sophisticated decomposition into period, age, and cohort effects.
Section 111 then analyses the underlying determinants of the observed
enrolment trends.
2. DATA AND TRENDS IN SCHOOL ENROLMENT
The data for this analysis is sourced from the Pakistan Rural
Household Surveys (PRHS) of 2001 and 2004. PRHS-01 is a representative
survey of rural Pakistan, consisting of around 2800 households in all
four provinces (Punjab, Sindh, NWFP, and Balochistan). PRHS-04 follows
up households in the two most populous provinces, Punjab and Sindh, to
form a panel of about 1600 households.
For the purposes of obtaining descriptive statistics that are
comparable across years, we treat the panel sample as a repeated
cross-section, selecting all individuals aged between 7-18 years in each
year. This leaves us with 1374 households contributing 3495 children in
2001 and 3734 children in 2004 (households need not contribute children
in both years). Note that, for now, our sample is not restricted to
children of household members. Doing so would exclude quite a few
married women under the age of 19. For example, in 2001, 24 percent of
17 year old girls and 34 percent of 18 year-olds were already married;
the corresponding figures in 2004 are 17 percent and 27 percent. Since
girls who marry early are much less likely to have ever been enrolled in
school, excluding them would overstate the proportion of 16-18 year-old
girls ever enrolled. Selective marriage is not a concern in the
subsequent econometric analysis where we focus on a sample of younger
children.
Figure 1 shows the proportion of children by age-gender group ever
enrolled in school (including pre-school) in 2001 and 2004. There appear
to have been substantial gains for girls, both absolutely and relative
to boys. A provincial breakdown of the same numbers in Figure 2 reveals
that the biggest changes occurred in Sindh province, which also had far
lower base (i.e., 2001) in girls' school enrolment than Punjab. As
we discuss next, however, comparisons of proportions ever enrolled, even
for a given age, confound year and cohort effects and hence must be
interpreted carefully.
[FIGURE 2 OMITTED]
3. DECOMPOSING ENROLMENT TRENDS
In examining trends in proportions of children ever enrolled in
school, one faces the classic period-cohort-age effect identification
problem [see, e.g., Hall, et al. (2005) for a recent discussion]. The
problem arises from the need to focus on children who are young enough
to still be entering school over the relevant period. To fix ideas, we
first describe the three effects in question:
Period effect: The change in enrolment of a given cohort over time
captures shifts in the economic and policy environment. Period effects
are only relevant for cohorts that could potentially have entered
primary school in response to these shifts, which means for children no
older than 12 in the base year.
Cohort effect: Differences in enrolment across cohorts in a given
year may reflect longer-term secular trends in enrolment. For example,
since we know that period effects and age effects (see below) are zero
for children 13 and older, we can infer from figure 1 that there has
been a sizeable cohort trend in girls' enrolment, which may have
resulted in higher likelihood of later cohorts to be enrolled.
Age effect: As a child ages the odds of ever enrolling in school
increase, or, at least, cannot decrease. In the context we study, most
children enter school by age 9, with a very small percentage enrolling
between age 10 and 12. Thus, age effects are only relevant for children
up to age 12.
Consider, now, the unrestricted dummy variable regression (linear
probability model), using two rounds of data from 2001 and 2004,
[e.sub.it] = p x I(year = 2004) + [summation over (j)][c.sub.j] x I
(cohort = j) + [summation over (k)] [a.sub.k] x I(age = k) + [u.sub.it]
(1)
where [e.sub.it] is an indicator for whether the child was ever
enrolled in school. Since cohort = age -3 x I (year = 2004), it is
evident that the period effect (p), cohort effects (c), and age effects
(a) are not separately identified. This identification problem cannot be
avoided by selecting a single age group, since in this case it would be
impossible to estimate the cohort effect (a given cohort consists of
children at two different ages in the two rounds of the survey).
Generally speaking, without further ad hoc restrictions on the
coefficients in (1), little can be said about the period effect [see
Hall, et al. (2005)]. We propose an identification strategy that makes
use of auxiliary information, possibly even from a different data set.
The advantage of our strategy is that it eschews arbitrary parameter
restrictions.
3.1. Purging the Age Effect
Consider a sample consisting of children age k-5, ..., K. Given the
innocuous normalisation [a.sub.5] = 0, we may write the age effects (the
coefficients in Equation (1)) as
[a.sub.k] = E([e.sub.it] | age = k)- E([e.sub.it] | age = 5) (2)
Suppose now that we have information on the age of school entrant
AE for a (possibly different) sample of children. Since Pr([e.sub.it] =
1 | age) = Pr(AE [less than or equal to] age), age effects may be
written as
[a.sub.k] = Pr(AE [less than or equal to] k) - Pv(AE [less than or
equal to] 5) (3)
Thus an estimator for [a.sub.k] is simply the difference in
proportions of children who entered school at or before age k and those
who entered at or before age 5. This calculation is best performed on a
sample of older children to avoid the censoring problem. In particular,
for children younger than 10 there is still a nontrivial probability
that those not yet enrolled in school may enter at a later date. We also
estimate the [[??].sub.k] separately for boys and girls, but, with
enough data, one could do so with respect to other characteristics, such
as province.
Given the [[??].sub.k], one can calculate [[??].sub.it] =
[K.summation over (k=5)][[??].sub.k]I(age = k) and replace the dependent
variable in (1) by [[??].sub.it] = [e.sub.it] - [[??].sub.it] proceeding
from there as though age effects were identically zero. In other words,
the regression
[e.sub.it] = p x I(year = 2004) + [summation][c.sub.j] x
I([cohort.sub.it] = j) + [u.sub.it] (4)
is equivalent to (I). Clearly, the parameters p and c are now
separately identified.
It may not be immediately obvious why the procedure just outlined
'works'? One might think that, if there are indeed cohort
effects in [e.sub.it], these should be present in Pr(AE [less than or
equal to] k) as well, and thus our age effects correction cannot be
applied uniformly across cohorts. Note, however, that the estimate of
[a.sub.k] essentially 'differences out' Pr([e.sub.it] = 1). To
see this, observe that, if no child ever enrols in school beyond age 12,
then Pr(AE > 12) = Pr([e.sub.it] = 0), implying Pr (AE [less than or
equal to] k) = Pr([e.sub.it] = 1) - Pr(12 [greater than or equal to] AE
> k). Consequently, [a.sub.k] = Pr(12 [greater than or equal to] AE
> 5) - Pr(12 [greater than or equal to] AE > k) contains no
information on the overall probability of ever enrolling in school.
What is being assumed, however, is that the distribution of school
entry ages conditional on eventual enrolment is stationary, or at least
changes slowly. In other words, we are assuming that it is reasonable to
impute the [a.sub.k] estimated retrospectively using a sample of 11-15
year olds in 2004 to 8 year-olds in 2004. (1) Though it seems unlikely
that the distribution of AE would change substantially within such a
short time, cohort effects in [[??].sub.k] can be investigated formally.
In Table 1, we calculate the gender-specific [[??].sub.k]
separately for 11-14 year-olds and for 15-18 year-olds and then test
whether the differences are significantly different from zero across the
two cohorts. The bootstrap t-tests reveal no significant differences at
any enrolment age. Thus, there is no noticeable shift in the
distribution of enrolment ages across cohorts. This is true even though
(as Figure 1 shows), there is a very substantial cohort effect in
enrolment for girls.
[FIGURE 1 OMITTED]
3.2. Estimating the Period Effect
Having dealt with the age effect, we now consider the period effect
in greater detail. In order to distinguish period and cohort effects, we
must follow the same cohorts over calendar time. Our empirical analysis
thus utilises the following sample structure:
[TABLE OMITTED]
In principle, one can use data from such a sample to estimate a
full set of interactions between cohort and year; i.e.,
[MATHEMATICAL EXPRESSION NOT REPRODUCIBLE IN ASCII] (5)
Equation (5) provides for a separate period effect for each cohort,
[[alpha].sub.j04] - [[alpha].sub.j01]. Imposing the (testable)
restriction of a common period effectdelivers the Equation (4).
Identification of period and cohort effects from Equations (4) (or
(5)) does not require panel data. The decomposition could just as well
be done using repeated cross sectional data and estimated using ordinary
least squares. However, for comparability with the subsequent analysis
(which does require household panel data), we estimate Equation (4)
using household fixed effects. The choice between OLS and household
fixed effects, at any rate, is of little consequence for the
decomposition of year and cohort effects.
Note, finally, that, although we could do so in principle, we do
not follow individual children over time; we only follow households.
Thus, a given household might contribute a completely different set of
children to the sample each round. Given our interest in the cumulative
outcome "ever been enrolled", following individuals is not
particularly useful. Since we do not, therefore, we remove individual
fixed effects, the cohort effects do not drop out from Equation (4) as
they otherwise would [see, e.g., Hall, et al. (2005)] and thus they can
still be identified.
3.3. Results of the Decomposition
Given the imperative to maximise the number of cohorts followed
over time, our sample for the decomposition differs from that underlying
Figures 1 and 2. As already mentioned, we select only 5-12 year-olds in
2001 and 8-15 year-olds in 2004, giving a total estimation sample of
4705 (child-year) observations contributed by 1001 panel households. Two
additional restrictions underlie this sample: First, we only choose
children of household members, although for the age range we consider
this is of little import since very few girls have yet married. Second,
our sample excludes households that do not contribute at least one child
in each survey round.
Table 2 reports the decomposition of enrolment trends into period
and cohort effects, after netting out age effects. All coefficients are
allowed to differ by sex. For purposes of comparison, specifications (1)
and (2) use the 'raw' enrolment variable, [e.sub.it], and do
not control for cohort, allowing only gender-specific period effects and
intercepts. The difference between the two regressions is that the first
is estimated by OLS, and the second by household fixed effects. As
already indicated, including household fixed effects is of practically
no consequence at this stage of the analysis.
Our adjustment for age effects, starting with specification (3),
has a big impact on the estimated coefficients. This should be expected,
given our sample structure. Children are 3 years younger on average in
2001 than in 2004 and for this reason alone are less likely to have
enrolled in school. Not correcting for age effects thus greatly
exaggerates the period effect. In specification (3) the period effect
for boys essentially vanishes, while that for girls falls by about half
as compared to specification (2).
Specifications (4) and (5) add cohort effects, in the first case by
including an unrestricted set of cohort dummies, and in the second case,
with a linear cohort trend. The linear trend cannot be rejected in
favour of the unrestricted dummies. While there is no significant cohort
trend for boys, there is a negative trend for girls. That is, the later
a girl was born the more likely she was to have been enrolled in school.
The inclusion of cohort trends, however, does not affect the estimated
period effect for either boys or girls. The insignificant F-test in
Table 2 also indicates that a completely unrestricted model (cohort-year
interaction dummies) fits the data no better than a restricted (common)
period effect.
Looking at the behaviour of the female dummy coefficient across
specifications (3)-(5), there are signs of a co-linearity problem. The
female dummy and its interaction with the cohort trend are highly
correlated with each other. So, it might be difficult to distinguish the
effect of being a girl per se versus the effect of being a girl of
successively later vintage. One way to avoid this problem is not to
estimate the female effect in the first place. This can be accomplished
by replacing household fixed effects with household-sex fixed effects,
which absorb the female dummy (effective sample size falls a bit because
there are some households contributing only a single girl or boy that
must be dropped). Specifications (6) and (7) thus include household-sex
fixed effects, while allowing for unrestricted and linear cohort trends.
Once again, the linear trend cannot be rejected, while the remaining
coefficients are virtually unaffected by the inclusion of household-sex
fixed effects. Later we use specification (7) to deal with a similar,
but even more severe, co-linearity problem.
4. EXPLAINING THE PERIOD EFFECT
The next step is to quantitatively assess the contribution of
different economic factors to the period effects in enrolment. Our
empirical approach is to re-estimate Equation (4), replacing the year
dummy with a vector of time-varying regressors. Specifically, we focus
on income growth and school construction.
4.1. Income Growth
Our measure of income is per capita household expenditures. (2) The
2001 and 2004 PRHS surveys have essentially identical household
expenditure modules, so the resulting expenditure aggregates are
perfectly comparable across years after controlling for inflation.
Figure 3 displays the distributions of log per capita expenditures by
year and province based on the panel sample. (3) Household consumption
grew substantially in both provinces; by around 28 percent on average in
Punjab and by 23 percent in Sindh. As of 2004, the average household in
Sindh had achieved almost the same income level as the average household
in Punjab in 2001.
[FIGURE 3 OMITTED]
In a cross-section, household expenditures and child school
enrolment are likely to be jointly determined and may thus be positively
correlated for reasons having little to do with the increased
affordability of schooling as income rises. Specifically, given positive
schooling costs, any change (shock) in school enrolment independent of
changes in wealth will be associated with a change in consumption.
Having no direct way to handle such feedback, (4) we argue next that it
should not cause significant bias.
Consider the stripped down regression model
[e.sub.it] = [beta]log([C.sub.it]) + [u.sub.it] (6)
with cohort effects suppressed and the period effect captured only
by [C.sub.it], per-capita expenditures on all goods other than
schooling. Conceptually, we would like [C.sub.it] to represent ex-ante
consumption; i.e., to reflect the resources available to the household
prior to any change in enrolment. However, what we observe is ex-post
consumption (or changes therein), which we denote by [C'.sub.it].
It is reasonable to suppose that [C'.sub.it] = [C.sub.it] -
[gamma][e.sub.it], where [gamma] > 0, since enrolling a child in
school reduces the resources that could otherwise be spent on the
consumption of other goods, either because of direct education costs or
the forgone income from the child's labour.
Assume now that total annualised per-child enrolment costs are
proportional to exante consumption; i.e. [gamma] = [delta][C.sub.it].
Thus, wealthier households pay proportionally more for tuition, books,
uniforms, etc. and/or their children's time has a higher
opportunity cost.
Given this, the relationship between ex-post (observed) consumption
and ex-ante consumption is ln([C'.sup.it]) = ln([C.sub.it]) + ln(l
- [delta][e.sub.it]). Substituting into (6) gives
[e.sub.it] = [beta]ln([C'.sub.it]) = [beta]ln(1 -
[delta])[e.sub.it] + [u.sub.it] (7)
The least squares estimate of [beta] thus converges in probability
to [[beta].sub.0]/1 + [[beta].sub.0]ln(1 - [delta]), which for [delta]
not too large and 0 < [[beta].sub.0] < 1 is approximately
[[beta].sub.0](1 + [[beta].sub.0][delta]). So,
[[??].sub.OLS] - [[beta].sub.0]/[[beta].sub.0] [congruent to]
[[beta].sub.0][delta] (8)
which indicates that the bias in the least squares estimate is
positive and, in percentage terms, is roughly equal to the true value of
[beta] times [delta]. In all of the empirical specifications below, none
of which correct for feedback, the (over) estimates of p never exceed
0.3. We can be assured, therefore, that [[beta].sub.0] < 0.3. Thus,
in order for the feedback bias in these estimates to exceed 10 percent,
the value of 8 would have to be greater than 0.33; in other words,
enrolment costs per child would have to account for at least a third of
ex-ante consumption! More realistic values of 8 imply a negligible bias
in [[??].sub.OLS].
Household expenditures may also be endogenous with respect to
school enrolment decisions due to measurement error in expenditures.
Noise in household expenditure data will result in the usual attenuation
bias, which, in contrast to the case of feedback bias just discussed,
can be quite substantial. To correct for this, we need an instrument
correlated with household consumption expenditures, but not with the
measurement error in this variable. A natural candidate is the
village-year (leave-one-out) mean of expenditures as calculated from the
full sample (i.e., including households that do not contribute children
to the panel sample). As we will see, this instrument performs extremely
well in terms of first-stage explanatory power.
4.2. School Construction
The 2004 PRHS includes a census of schools within each village. In
addition to knowing the type of school (primary, middle or boys only,
girls only, or mixed), we also have the date the school was established.
Using this information, we can construct indicators for whether a
girls' (boys') primary (middle) school was present in the
village at the time of each survey. The same can be done for schools of
given type within the settlement where the household resides, since most
villages have multiple settlements. Due to mobility constraints,
especially for girls, it may matter more that the appropriate school is
located in the same settlement rather than merely in the same village.
(5) On the other hand, establishing the very first girls' school in
an entire village may have a greater effect on enrolment than adding the
tenth school, even though that school happens to be in the same
settlement.
Because we include household fixed effects, identification of the
impact of school availability on enrolment comes from schools that were
established since 2001. Given that the panel sample covers only 93
villages with 274 settlements, there may not be enough new schools in
the data to estimate the effects of interest. Indeed, this is a
particular problem for boys' schools, as Table 3 indicates. For
example, not a single one of our sample villages that did not have a
boys' primary school prior to 2001 received one in the subsequent 3
years, although two settlements within these villages did get a new
school. Likewise, there was a paucity of new middle school construction
in these villages. Thus, the percentage of boy observations in our
sample for which there is a change in school availability between 2001
and 2004 never exceeds one. For girls' schools the situation is
somewhat better, so there may be hope of identifying school availability
effects for girls. (6)
4.3. Main Results
Table 4 displays the determinants of the period effects. In other
words, the gender-specific period effects in specification (5) of Table
2 are replaced here with log per capita expenditures interacted with a
male and female dummy, as well as with girls' primary school
availability in the village interacted with a female dummy. Given the
lack of variation (see Table 3), we do not attempt to estimate school
availability effects for boys.
The first specification is estimated using household fixed effects;
the second deals with measurement error in expenditures using as
instruments village leave-out means interacted with the gender dummies.
Shea partial [R.sup.2]s for the two first-stage regressions are quite
high; 0.19 for the boy-expenditure interaction and 0.16 for the girl
interaction. The second-stage expenditure coefficients behave exactly as
one would expect with measurement error. The female coefficient, already
positive and significant in the OLS, increases substantially in
magnitude. The male income effect, meanwhile, remains insignificant
across specifications. There is also some evidence that, for girls, the
addition of a girls' primary school in the village increases
enrolment.
One worry, however, is the alarming increase in the female dummy
variable coefficient, becoming unrealistically large in specification
(2). The problem, again, is colinearity; this time between the female
dummy and the female dummy interaction with log per capita expenditures.
Mechanically, these two variables must be highly correlated, which they
are, and instrumenting expenditures only exacerbates the problem. As
before, our solution is to purge the female dummy altogether by
including household-sex fixed effects. Comparing specifications (3) and
(4), then, yields a similar conclusion about the influence of
measurement error in the expenditure coefficient, except that the
estimated income effect is only about two-thirds as large as before
(0.185 vs. 0.262). The primary school availability effect for girls more
than doubles in magnitude, however.
The last two columns in Table 4 explore alternative specifications
of the school availability effect for girls. In specification (5), we
control for the presence of a middle school for girls in the village.
While greater middle school availability does increase the likelihood of
ever enrolling a girl, the effect is not significant and the coefficient
is far less than the corresponding one for girls' primary schools.
Specification (6) replicates specification (4) using girls' primary
school availability at the settlement level. Recall from Table 3 that
under this second definition of primary school availability somewhat
more girls in our sample experience a change in availability over the
2001-04 period (2.6 percent versus 1.6 percent). The resulting primary
school coefficient, however, is little changed.
By way of summary, we calculate the fraction of the period effect
explained by changes in the time-varying covariates. This exercise is
only relevant for girls, since period effects are negligible for boys.
The second to last row in Table 4 shows that, for the preferred
specifications (household-sex fixed effects with correction for
measurement error), we can explain more than two-thirds of the period
effect in girls' enrolment. The figures in the last row show that
almost all of this is due to income growth; very little of the period
effect is explained by growth in school availability, which is not
surprising given that there is hardly any change in school availability
in our sample.
4.4. Provincial Differences
We now turn to the question raised at the beginning: As we have
seen, between 2001 and 2004, average income in Sindh rose to about the
level of Punjab in 2001. Girls' school enrolment in Sindh followed
a similar pattern, also rising to about the level observed in Punjab in
2001. Of course, this may just be coincidence; the fact that these
trends line up by no means implies that the income rise in Sindh was
entirely responsible for the increase in girls' enrolment.
To investigate the question, we present a province-level analysis
in Table 5. By far the largest period effect for girls is in Sindh: In
2004, the proportion of girls who had ever enrolled in school was 13
percentage points higher than in 2001. Looking at province-specific
results in specification (2), we see that the income effect is also by
far the largest (and only significant) for girls in Sindh. The primary
school availability effect, by contrast, is important only in Punjab;
more precisely, it is only estimable in Punjab, because there was no
change in school presence in any of the Sindh villages in our sample.
Even though girls' school enrolment in Sindh appears much more
responsive to income changes than in Punjab, income growth explains less
than half of the period effect in Sindh (see bottom of Table 5). This
suggests that factors other than income must be responsible for at least
half the convergence in girls' enrolment between Pakistan's
two largest provinces. By the same token, it is unlikely that the 2001
gap in girls' enrolment between Punjab and Sindh can be mostly
explained by Punjab's greater wealth.
A final question to consider, as far as Sindh is concerned, is
whether the response of girls' enrolment to income growth depends
on school availability? In particular, for around 6 percent of girls in
the Sindh subsample, no (girls') primary school existed in their
village in 2001. Since they would have had no school to go to, it would
be very surprising if the enrolment of these girls rose with household
income. That this indeed did not happen is confirmed by the results in
the final column of Table 5. The response of enrolment to income growth
for girls without a primary school in 2001 is not significantly
different from zero (p-value = 0.15), whereas it remains significantly
positive for girls who did have access to a village primary school. (7)
5. CONCLUSIONS
Recent years have seen a marked closing of the gender gap in school
enrolment in rural Pakistan. This paper has shown how to use panel data
to isolate changes in school entry attributable to shifting economic
conditions. Using this approach, we have established that income growth
has played an important role in drawing an increasing number of girls
into school. Meanwhile, very little of the observed enrolment changes
can be explained by new school construction.
Despite the enrolment gains observed in the 2001-2004 period, the
overall gender gap in schooling remained significant and the findings of
this paper suggest that the much lower girls' school enrolment
observed in Sindh as compared to Punjab cannot be attributed entirely to
the large income differences between the two provinces. A recent paper
that focuses specifically on this residual gender gap [Jacoby and
Mansuri (2013)], finds that much of the residual gender gap can be
explained by social constraints. In particular, it finds that social
stigma greatly discourages school enrolment among low-caste children,
with low-caste girls, the most educationally disadvantaged group, being
the worst affected. However, it also shows that low-caste households who
can escape stigma invest at least as much in schooling as high caste
households, indicating similar returns to schooling across caste groups.
These results suggest that, from a policy perspective, it may be
important to deliberately target gender specific social barriers to
schooling in addition to any policies that target schooling demand
through transfers.
REFERENCES
Alderman, If, J. Behrman, D. Ross, and R. Sabot (1996) Decomposing
the Gender Gap in Cognitive Skills in a Poor Rural Economy. Journal of
Human Resources 31:1, 229-54.
Behrman, J., A. Foster, M. Rosenzweig, and P. Vashishtha (1999)
Women's Schooling, Home Teaching, and Economic Growth. Journal of
Political Economy 107:4, 682-714.
Duryea, S., D. Lam, and D. Levinson (2007) Effects of Economic
Shocks on Children's Employment and Schooling in Brazil. Journal of
Development Economics (Forthcoming).
Glewwe, P. and H. G. Jacoby (2004) Economic Growth and the Demand
for Education: Is there a Wealth Effect? Journal of Development
Economics 74:1, 33-51.
Hall, B., J. Mairesse L. Turner (2005) Identifying Age, Cohort, and
Period Effects in Scientific Research Productivity: Discussion and
Illustration using Simulated and Actual Data on French Physicists.
Cambridge, MA. (NBER Working Paper 11739).
Jacoby, H. G. and G. Mansuri (2010) Watta-Satta: Exchange Marriage
and Women's Welfare in Rural Pakistan. American Economic Review
100, 1804-1825.
Jacoby, H. G. and G. Mansuri (2013) Crossing Boundaries: How Social
Hierarchy Impedes Economic Mobility. The World Bank. (Under Review).
Jacoby, H. G. and E. Skoullas (1997) Risk, Financial Markets, and
Human Capital in a Developing Country. Review of Economic Studies 64:3,
311-336.
Mansuri, Ghazala (2006) Migration, School Attainment and Child
Labour. The World Bank. Washington, DC. (Policy Research Working Paper#
3945).
Khan, A. (1998) Female Mobility and Social Barriers to Accessing
Health and Family Planning Services: A Qualitative Research Study in
Three Punjabi Villages. Islamabad: Ministry for Population Welfare,
London School of Tropical Hygiene and Medicine and Department for
International Development, British Government.
(1) There is no way to calculate the [[??].sub.k] directly for
cohorts just entering school in 2004 precisely because many have yet to
enrol. It is also worth noting that age of school entrants was only
asked in PRHS-04, not in the 2001 survey. This, however, is of little
relevance for our procedure.
(2) Glewwe and Jacoby (2004) rationalise the use of household
expenditures as a measure of the shadow value of wealth in the context
of a dynamic model of human capital accumulation wherein child school
enrolment and consumption are household decision variables. Thus, after
properly accounting for endogeneity, the partial correlation between
enrolment and consumption reflects a well-defined wealth effect on the
demand for schooling.
(3) The panel sample may not be adequately representative of the
rural population of the two provinces. In particular, 260 households
from whom expenditure data were gathered in 2001 were not followed up in
2004. This sample loss was mainly due to administrative problems. A
regression of 2001 log per capita expenditures on a province dummy and a
dummy for whether the household does not appear in PRHS-04 reveals that,
on average, base-year expenditures are 10 percent lower for households
lost in 2004. However, this entire effect is due to 71 households from 4
villages (3 in Punjab, 1 in Sindh) that could not be revisited due to
security concerns. Otherwise, the lost households are no different in
terms of baseline wealth than those that were followed-up.
(4) In principle, it might be possible to instrument consumption
changes with household characteristics that predict whether income grew
over the relevant time period. For example, households with relatively
more un-irrigated land would have been more affected by the 2001
drought, or households with more migrants in 2001 would have benefited
more from the post-9/11 increase in foreign remittances. In practice,
however, such instruments performed poorly in our data. This approach
would also require a first-difference specification in household means
of the enrolment variable as in Glewwe and Jacoby (2004).
(5) On mobility constraints for girls see Khan (1998), Jacoby and
Mansuri (2010) and Jacoby and Mansuri (2013).
(6) Primary school availability changes little in part because by
2001 nearly every village, and indeed many settlements, already had one.
Specifically, in 2001, 99 (75) percent of the boys and 94 (69) percent
of the girls in our sample had a primary school for their respective
gender in their village (settlement).
(7) The same exercise for primary schools within the settlement in
2001 yields similar, but statistically weaker, results. In this case, 26
percent of girls in the sample had no primary school in their settlement
in 2001.
Hanan G. Jacoby <hjacoby@worldbank.org> and Ghazala Mansuri
< gmansuri@worldbank.org> are at the Development Research Group,
World Bank, Washington, DC, USA, respectively.
Table 1
Changes in Age of Enrolment Distribution by Cohort
[[??].sub.k]
Bootstrap
11-14 15-18 t-test
k cohort cohort Difference (p-value)
Boys
6 0.177 0.206 -0.029 0.219
7 0.279 0.314 -0.035 0.206
8 0.325 0.372 -0.047 0.104
9 0.355 0.390 -0.034 0.238
10 0.374 0.407 -0.033 0.260
11 0.391 0.409 -0.018 0.544
12 0.395 0.411 -0.016 0.583
Sample Size 588 567
Girls
6 0.114 0.101 0.013 0.525
7 0.183 0.190 -0.006 0.800
8 0.231 0.228 0.003 0.916
9 0.250 0.236 0.014 0.611
10 0.268 0.248 0.020 0.469
11 0.279 0.248 0.031 0.266
12 0.292 0.250 0.042 0.142
Sample Size 545 416
Notes: See text for definition of [[??].sub.k] Bootstraps use
1000 replications each.
Table 2
Decomposition of Enrolment Trend into Period and Cohort Effects
(1) (2) (3) (4)
Male x 2004 0.114 0.115 0.017 0.017
(0.015) (0.015) (0.014) (0.014)
[0.000] [0.000] [0.231] [0.220]
Female x 2004 0.156 0.152 0.080 0.080
(0.016) (0.016) (0.016) (0.016)
[0.000] [0.000] [0.000] [0.000]
Female -0.237 -0.234 -0.134 -0.055
(0.022) (0.021) (0.020) (0.039)
[0.000] [0.000] [0.000] [0.158]
Male x Cohort
Female x Cohort
Fixed Effects No HH HH HH
Age Effects (Adjusted) No No Yes Yes
Cohort Effects No No No Unres.
F-test p-value * 0.779
Total Sample (Flouseholds) 4705 4705 4705 4705
(1001) (1001) (1001) (1001)
(5) (6) (7)
Male x 2004 0.017 0.014 0.013
(0.014) (0.014) (0.014)
[0.223] [0.339] [0.353]
Female x 2004 0.080 0.077 0.077
(0.016) (0.016) (0.016)
[0.000] [0.000] [0.000]
Female 0.002 -- --
(0.057)
[0,965]
Male x Cohort -0.001 -0.003
(0.005) (0.005)
[0.860] [0.605]
Female x Cohort -0.017 -0.019
(0.005) (0.005)
[0.000] [0.000]
Fixed Effects HH HH-sex HH-sex
Age Effects (Adjusted) Yes Yes Yes
Cohort Effects Linear Unres. Linear
F-test p-value * 0.218 0.375 0.405
Total Sample (Flouseholds) 4705 4587 4587
(1001) (985) (985)
Notes: Standard errors adjusted for clustering on household
in parentheses; p-values in square brackets.
* In specifications (4) and (6) the 14 restrictions tested
are: all period effects are equal across cohorts for males
and females; In specifications (5) and (7) the 12
restrictions tested are: gender-specific cohort dummies,
which can be collapsed into gender-specific linear cohort
trends.
Table 3
Changes in School Availability 2001-2004
Primary Schools Middle Schools
Boys
No. of Villages 0 (0.0) 1 (1.0)
No. of Settlements 2 (0.7) 1 (1.0)
Girls
No. of Villages 2 (1.6) 2 (3.6)
No. of Settlements 6 (2.6) 3 (3.2)
Note: Percent of sample observations for that gender residing
in relevant village or settlement in parentheses.
There are a total of 93 villages and 274 settlements.
Table 4
Determinants of Period Effects in School Enrolment
(0 (2) (3)
Male x log(pcexp) 0.017 -0.003 0.013
(0.019) (0.046) (0.021)
[0.356] [0.954] [0.527]
Female x log(pcexp) 0.072 0.262 0.068
(0.021) (0.061) (0.023)
[0.001] [0.000] [0.003]
Female x girl's primary 0.183 0.158 0.385
school (0.077) (0.081) (0.135)
[0.018] [0.052] [0.004]
Female x girl's middle -- -- --
school
Female -0.633 -2.538 --
(0.244) (0.637)
[0.010] [0.000]
Male x cohort 0.000 -0.001 -0.002
(0.005) (0.005) (0.005)
[0.953] [0.869] [0.685]
Female x cohort -0.018 -0.019 -0.019
(0.005) (0.005) (0.005)
[0.000] [0.000] [0.000]
Fixed effects HH HH HH-sex
4628 4628 4508
Total sample (households) (987) (987) (970)
% period effect (female)
explained by growth in
Income + schools 26 84 30
Income only 22 81 22
(4) (5) (6)
Male x log(pcexp) 0.042 0.042 0.042
(0.050) (0.050) (0.050)
[0.406] [0.406] [0.406]
Female x log(pcexp) 0.185 0.170 0.186
(0.068) (0.068) (0.067)
[0.006] [0.012] [0.006]
Female x girl's primary 0.366 0.368 0.289
school (0.132) (0.132) (0.097)
[0.005] [0.005] [0.003]
Female x girl's middle -- 0.132 --
school (0.093)
[0.157]
Female -- -- --
Male x cohort -0.002 -0.002 -0.002
(0.005) (0.005) (0.005)
[0.685] [0.685] [0.685]
Female x cohort -0.019 -0.019 -0.019
(0.005) (0.005) (0.005)
[0.000] [0.000] [0.000]
Fixed effects HH-sex HH-sex HH-sex
4508 4508 4508
Total sample (households) (970) (970) (970)
% period effect (female)
explained by growth in
Income + schools 67 68 68
Income only 59 55 60
Notes: Standard errors adjusted for clustering on household
in parentheses; p-values in square brackets. Specifications
(1) and (3) are estimated by fixed effects. Specifications
(2), (4)-(6) are estimated by fixed effects-IV using
interactions with the village-year leave-one-out mean of log
(pcexp) as instruments. Specifications (1 )-(5) define
school availability at the village level, whereas
specification (6) does so at the settlement level.
Table 5
Province-level Decomposition of Enrolment Trends
Punjab
(1) (2)
Male x 2004 -0.009 --
(0.019)
[0.624]
Female x 2004 0.020 --
(0.019)
[0.306]
Male x log(pcexp) -- 0.005
(0.070)
[0.942]
Female x log(pcexp) -- 0.061
(0.082)
[0.457]
Female x log(pcexp) x
No girl's primary school in 2001
Female x girl's primary -- 0.386
school (in village) (0.136)
[0.004]
Male x cohort 0.003 0.004
(0.007) (0.007)
[0.603] [0.550]
Female x cohort -0.016 -0.016
(0.007) (0.007)
[0.022] [0.024]
Total sample 2374 2329
(households) (524) (514)
% period effect (female)
explained by growth in
Income + schools 147
Income only 77
Sindh
(1) (2) (3)
Male x 2004 0.040 -- --
(0.021)
[0.057]
Female x 2004 0.133 -- --
(0.024)
[0.000]
Male x log(pcexp) -- 0.071 0.071
(0.071) (0.071)
[0.314] [0.314]
Female x log(pcexp) -- 0.261 0.287
(0.098) (0.104)
[0.008] [0.006]
Female x log(pcexp) x -0.521
No girl's primary school in 2001 (0.194)
[0.007]
Female x girl's primary -- -- --
school (in village)
Male x cohort -0.010 -0.010 -0.010
(0.008) (0.008) (0.008)
[0.206] [0.230] [0.230]
Female x cohort -0.021 -0.022 -0.022
(0.008) (0.008) (0.008)
[0.008] [0.005] [0.004]
Total sample 2213 2179 2179
(households) (461) (456) (456)
% period effect (female)
explained by growth in
Income + schools 44 40
Income only 44 40
Notes: Standard errors adjusted for clustering on household
in parentheses; values in square brackets. All
specifications include household-gender fixed effects.
Specifications with log (pcexp) interactions, are estimated
by IV to correct for measurement error.
