WPS8050
Policy Research Working Paper 8050
The Misallocation of Pay and Productivity
in the Public Sector
Evidence from he Labor Market for Teachers
Natalie Bau
Jishnu Das
Development Research Group
Human Development and Public Services Team
May 2017
Policy Research Working Paper 8050
Abstract
This paper uses a unique dataset of both public and private explain no more than 5 percent of the variation in TVA.
sector primary school teachers and their students to present Finally, there is no correlation between TVA and wages in
among the first estimates in a low-income country of (a) the public sector (although there is in the private sector),
teacher effectiveness; (b) teacher value added (TVA) and and a policy change that shifted public hiring from perma-
its correlates; and (c) the link between TVA and teacher nent to temporary contracts, reducing wages by 35 percent,
wages. Teachers are highly effective in our setting: Moving had no adverse impact on TVA, either immediately or after
a student from the 5th to the 95th percentile in the public 4 years. The study confirms the importance of teachers
school TVA distribution would increase mean student in low income countries, extends previous experimental
test scores by 0.54 standard deviations. Although the first results on teacher contracts to a large-scale policy change,
two years of experience, as well as content knowledge, are and provides striking evidence of significant misalloca-
associated with TVA, all observed teacher characteristics tion between pay and productivity in the public sector.
This paper is a product of the Human Development and Public Services Team, Development Research Group. It is part
of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy
discussions around the world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org.
The authors may be contacted at jdas1@worldbank.org.
The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development
issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the
names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those
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Produced by the Research Support Team
T HE M ISALLOCATION OF PAY AND P RODUCTIVITY IN THE
P UBLIC S ECTOR : E VIDENCE FROM THE L ABOR M ARKET FOR
T EACHERS∗
NATALIE BAU† J ISHNU DAS‡
∗
Natalie Bau gratefully acknowledges the support of the CIFAR Azrieli Global Scholarship, the National Science
Foundation Graduate Research Fellowship, and the Harvard Inequality and Social Policy Fellowship. Jishnu Das
acknowledges funding from RISE. We are also grateful to Christopher Avery, Deon Filmer, Asim Khwaja, Michael
Kremer, Nathan Nunn, Roland Fryer, Owen Ozier, Faisal Bari and seminar participants at the World Bank, NBER
Education Meetings, CERP, NEUDC, IADB, the University of Auckland, and the University of Delaware for helpful
comments. The ﬁndings, interpretations, and conclusions expressed in this paper are those of the authors and do not
necessarily represent the views of the World Bank, its Executive Directors, or the governments they represent.
†
University of Toronto and CIFAR. (email: natalie.bau@utoronto.ca)
‡
World Bank. (email: jdas1@worldbank.org)
1 Introduction
How to recruit and reward teachers is one of the most contentious questions in education today.
Some believe that the best way to improve the quality of teachers is to hire the brightest college
graduates by offering high salaries.1 Others argue that public school teachers are overpaid, and
with increasing ﬁscal stress in many countries, teacher salaries are a natural target for retrenchment
(Biggs and Richwine, 2011). Understanding the characteristics that make an individual a good
teacher and whether the same characteristics are also highly rewarded by the outside labor market
is key to this debate. If, for instance, the brightest college graduates can earn high salaries in other
professions but are not better teachers, they may be the wrong population to target for recruitment.
This question has received considerable attention in the United States, but sparse data has impeded
similar investigations in low income countries.
We examine both the question of what makes a good teacher and the link between wages and
productivity using a unique dataset that we collected between 2003 and 2007 from the province
of Punjab, Pakistan as part of the Learning and Educational Achievement in Pakistan Schools or
LEAPS project. These data contain test-score information on matched teacher-child pairs, permit-
ting teacher value-added (TVA) estimation for 1,533 public school teachers and 975 private school
teachers from 574 public and 345 private primary schools, observed mainly in grades 3, 4 and 5.
These data allow us to estimate the association between teacher characteristics and teacher wages
in both sectors. We are also able to combine these data with an unexpected regime change at the
beginning of the data collection period, which led all new hires in the public sector to receive
temporary contracts with lower wages. By contrasting the TVA of teachers hired under the old
and the new regime, we assess whether the change adversely affected TVA, either for those hired
immediately after the change or those hired several years later.
The main results are as follows. First, teachers matter, and the variation in teacher quality is
greater when we include both the public and private sectors. A 1 standard deviation (sd) increase
in public sector TVA leads to a 0.16sd increase in mean student test scores, and a 1sd increase
in overall TVA leads to a 0.21sd increase in test scores. This implies that moving a student from
the 5th to the 95th percentile of the public sector TVA distribution increases test scores by 0.54sd,
which can be compared to an average annual test score gain of 0.41sd in our sample. Although ob-
served teacher characteristics explain no more than 5% of the variation in TVA – a common result
in the literature on teacher effectiveness – we do ﬁnd that the ﬁrst two years of teaching experi-
ence are associated with a signiﬁcant increase in TVA. Since we are able to examine experience
1 An inﬂuential report by McKinsey, for instance, discussed the need to hire top graduates (Auguste et al., 2010):
“Given the real and perceived gaps between teachers’ compensation and that of other careers open to top students,
drawing the majority of new teachers from among top-third students would require substantial increases in compensa-
tion” (p. 7).
2
effects for the same teacher over time, this result is arguably causal. Consistent with recent work
by Bold et al. (2017) in Africa, we also ﬁnd that higher content knowledge is associated with sig-
niﬁcantly higher TVA, a correlation that emerges clearly once we account for measurement error
using multiple test scores from the same teacher.
Second, there is no link between TVA and wages in the public sector.2 Public sector wages
reward seniority and education – both of which have small associations with TVA – but not TVA
directly. Although this “zero-gradient” result is widely believed to be true, to our knowledge this
is the ﬁrst direct empirical test in a low income country. Using similar data from private schools,
we compare the gradient in the “market” with that in the public sector. Rewards to seniority are
one-ﬁfth as high in the private sector and, strikingly, a 1sd increase in TVA increases wages by
11%. Even in the absence of a formal testing regime, TVA is somewhat observable and can be
rewarded, but the public sector does not have a mechanism to do so.
Third, lowering the wages of public sector teachers has no effect on the TVA of new entrants.3
We compare the TVA of teachers hired just before and after a change in the hiring regime that
moved all new hires to temporary contracts with signiﬁcantly lower wages. In our data, 93%
of new hires in 1997 were permanent teachers and by 2002, 89% were contract teachers, who
received salaries that were 35% lower, not counting further cost savings from beneﬁts such as
pensions.4 Instead of a decline, we typically ﬁnd a positive, though not consistently signiﬁcant,
impact of contract status on TVA. When we compare contract and permanent teachers with more
similar levels of experience, we ﬁnd larger and more signiﬁcant positive effects. It is possible
that a worsening macroeconomic outlook following 1998 increased the attractiveness of teaching
relative to other professions, compensating for the contractual change (for example, see Nagler
et al. (2015)). However, we also do not ﬁnd evidence that the pool of new teachers worsened over
time (as the economy improved) with similar TVA estimates for later and earlier hires.5
2 Here, we assume that TVA is a useful measure of productivity for teachers. We recognize that teachers have other
functions that we do not capture, and how these are rewarded is an important agenda in its own right. Nevertheless,
children’s test scores remain a key component of educational performance in any system, especially since they are a
strong predictor of adult outcomes (for example, see Chetty et al. (2014b)).
3 Determining whether wages are “too high” is typically difﬁcult since researchers must determine how teachers are
compensated relative to their outside options. To do this, they must adjust for different schedules (summer vacation),
education levels, cognitive ability and the type of teacher, and different adjustments lead to different conclusions about
the relative size of teacher compensation. Weissman (2011) is a non-technical summary of the studies and these issues.
4 We arrive at 35% by regressing log teacher salaries on teacher characteristics, including seniority, as well as an
indicator variable for contract status. Thus, we report the difference between contract teacher and non-contract teacher
wages after accounting for any differences in observable teacher characteristics.
5 The main threat to identiﬁcation is the systematic allocation of contract teachers to students who were likely
to learn more. We test for such systematic sorting and ﬁnd no evidence that contract teachers were systematically
allocated to better performing schools or students. Furthermore, there is no correlation between students’ test score
trends and future assignment to a contract teacher, either at the school or at the student level. We further account for
unobserved selection of students or teachers to schools by comparing contract and permanent teachers within the same
school.
3
We investigate two possibilities that could lead to this result: either (1) teachers hired prior to
the policy change possessed attributes that were rewarded in the outside labor market, but these
attributes are not correlated with TVA, or (2) there is a signiﬁcant wage premium in the public
sector even conditioning on teacher characteristics. The weight of the evidence favors the latter
as the more plausible explanation. Average education levels and test scores of new hires, both of
which are arguably rewarded in the non-teaching labor market, did not decline after the regime
shift. Moreover, the signiﬁcant wage premium in public sector teaching jobs is also seen in a
comparison of teachers’ wages in public and private schools. In 2003, teacher salaries in the
public sector were 5 times higher than those in the private sector (Andrabi et al., 2008) and by
2011, they were 8 times as high. When private sector wages are one-ﬁfth as high, decreasing the
public wage by one-third does not affect the quality of new entrants; the outside option is never
more attractive than the public sector in our data.
Our paper contributes to an important and growing literature on the estimation of TVA and its
correlates. Studies from the U.S. and Ecuador demonstrate (a) the importance of teachers; (b) low
correlations between observed characteristics and TVA (Staiger and Rockoff, 2010) and; (c) the
positive effects of the ﬁrst two years of teacher experience on TVA (Rockoff, 2004; Chetty et al.,
2014a Rivkin et al., 2005, Araujo et al. (2016)).6 These ﬁrst estimates from a large sample in a
low-income country demonstrate the external validity of these ﬁndings to an environment where
the variation in observed characteristics is arguably much greater than in the U.S.7 In addition,
we are also able to extend these results to teachers in private schools and to show that content
knowledge and TVA are highly correlated once we account for measurement error. It could be
that, at the very low levels of learning that we see in our sample, both among children and among
teachers, content knowledge becomes increasingly important.
The main empirical challenges in estimating TVA arise from the lack of experimental variation
and the fact that much of our sample is from small, rural schools with a single classroom per
grade. Although this is a common scenario in Pakistan – in the census of primary public schools
for Punjab, average class sizes for grades 3, 4 and 5 in 2005 were only 17, 16, and 13 – it does not
permit grade-speciﬁc, within school-year TVA estimates since we typically do not observe multiple
teachers teaching the same grade in the same school in the same year. We assess whether our TVA
6 In perhaps the ﬁrst study of teacher and classroom effects outside of a high income country, Araujo et al. (2016)
present estimates of the variance of teacher effects in Ecuador after randomly allocating students to teachers and
also ﬁnd that observed characteristics explain little of the variation in students’ outcomes, even after including direct
measures of classroom effort.
7 In our data, 49% of public school teachers and 74% of private school teachers do not have a bachelor’s degree,
and (self-reported) mean days absent per month range from 0.5 at the 10th percentile to 5 at the 90th percentile of the
absentee distribution in the public sector and 0 at the 10th percentile and 4 at the 90th percentile in the private sector.
For comparison, the absence rate of an average teacher in the U.S. is 5%, and is only 3.5 percentage points higher for
schools whose proportion of African American students (a marker associated with disadvantage in the United States)
is in the 90th percentile (Miller, 2012).
4
estimates are biased due to selective sorting of students to teachers in several ways, and in our most
important test, we examine whether a teacher’s TVA predicts test score gains among a sample of
children who switch schools. We ﬁrst show that the child’s future teacher’s TVA after she switches
schools does not predict her current teacher’s TVA, suggesting little systematic sorting leading to
persistence in the quality of children’s teachers. We then show that the gain in test scores for a
child who switches schools is precisely predicted by the TVA of the teacher that she is matched to,
suggesting that our estimated TVA indeed captures variation in teacher quality. This out of sample
validation test, similar in spirit to that of Chetty et al. (2014a), who use teacher switching instead,
suggests that we can extend TVA computations to small schools with single grade classrooms.
Our results also add to a literature that highlights the misallocation in public resources be-
tween teachers’ wages and other inputs in low-income countries (Pritchett and Filmer, 1999). In
Kenya and India, Duﬂo et al. (2011) and Duﬂo et al. (2014) and Muralidharan and Sundararaman
(2013) show that contract teachers cost less, but the test-score gains of children assigned to con-
tract teachers are higher.8 Our study demonstrates that the ﬁndings of Duﬂo et al. (2011) and Duﬂo
et al. (2014) and Muralidharan and Sundararaman (2013) are widely applicable and relevant for a
large-scale policy change by the government. We never ﬁnd evidence that a large-scale policy re-
ducing teachers’ salaries negatively affected teacher quality. Additionally, our results suggest that
shorter experiments that compare inexperienced contract teachers and permanent teachers may un-
derestimate the effectiveness of contract teachers due to the large TVA gains that we observe over
the ﬁrst two years of teaching.9 Our ﬁndings complement recent work in Indonesia by De Ree
et al. (2015), who show that a doubling of teachers’ salaries has no effect on student learning.
Their study, also with the government, examines the intensive margin of teacher effort while our’s
focuses on the extensive margin of teacher hiring.
The misallocations that we identify are striking. A literature from the OECD typically ﬁnds
public sector premia of 5 to 15%, with some portion of the gap explained by differential motivation,
sector-speciﬁc productivity and the selection of workers (Disney and Gosling, 1998; Dustmann and
Van Soest, 1998; and Lucifora and Meurs, 2006). In contrast, in our study, public sector wages
are 5 times as large as private sector wages, and within the public sector, a decline in wages of
8 Duﬂo et al. (2011) and Duﬂo et al. (2014) also show that contract teachers with higher performance were more
likely to be rewarded with tenure in later years, and thus career concerns provide additional incentives to exert effort. In
India, Muralidharan and Sundararaman (2013) allocate a contract teacher to randomly chosen schools. They show that
schools where contract teachers were assigned gained more in test scores. Using observational data, they suggest that
there is an independent contract-teacher effect beyond the reduction in student teacher ratios caused by the additional
teacher. A recent paper by Bold et al. (2013) repeats the experiment in Duﬂo et al. (2014) with a NGO and the
government. They are able to replicate Duﬂo et al.’s (2014) results when the NGO implements the policy, but are
unable to ﬁnd similar effects with government implementation.
9 Alternatively, comparisons based on the performance of the average permanent and marginal contract hire could
conﬂate differences due to experience or cohort effects with differences in contract status (for instance, an average
permanent hire is older and more experienced in our data).
5
(at least) 35% has no negative impact on productivity as measured by TVA.10 The much higher
wage premium in Pakistan is consistent with the ﬁndings of Finan et al. (forthcoming), who use
household survey data from 32 countries to show that the wage premium in the public sector
is higher in poorer countries. Taken as a group, these studies all point to large and signiﬁcant
misallocations in the pay of public sector teachers in low-income countries, which we are able to
demonstrate in the context of a large-scale change in the public sector recruitment of teachers.11
The remainder of our paper is organized as follows. Section 2 describes the setting and context,
and Section 3 discusses the data. Section 4 discusses TVA estimation, the results of regressions of
TVA on teacher characteristics, and the robustness of the TVA measures. Section 5 discusses the
link between teacher quality and teacher wages, and Section 6 concludes.
2 Setting and Context
The data are from rural Punjab, Pakistan, the largest province in the country with an estimated
population of 100 million. The majority of children in the province can choose to attend free public
schools, or they can pay to attend private school, and at the primary level, one-third of enrolled
children choose to do so.12 Although funding for public schools has traditionally been small, in
recent years, the government of Punjab has ratcheted up education budgets from 468 million dollars
in 2001-2002 to 1.680 billion dollars in 2010-2011 (Ishtiaq, 2013). Much of this expenditure is
on recurring budget items, and, similar to other low-income settings, teachers’ salaries account for
80% of spending (UNESCO Islamabad, 2013).13 In Pakistan, teachers are part of the civil service
and salaries are determined through the Basic Pay Scale that allocates teachers to ‘grades’ based
on their position (primary vs. middle or secondary school teacher and regular teacher vs. head
teacher) and provides a basic salary that depends on grade and experience. Appendix Figure A1
shows the most recent, ofﬁcial Basic Pay Scale in Punjab province.14 In addition to this Basic
10 Since we do not include future liabilities such as pensions in this accounting, the wage difference is a lower
bound in our study.
11 We must acknowledge that, although we get close to the natural experiment of a wholesale reduction in wages,
if contract teachers believed that their chances of obtaining a permanent contract would increase with their effort, the
policy change may have affected both remuneration levels and career incentives. Separating the two effects would
require a separate experiment. If the career incentives channel is important, our results would show that temporary
contracts induced a combination of teacher effort and quality that can yield the same learning at a lower cost, at least
for some years, an issue we return to in Section 5.4 below.
12 Religious schools, or madrassas, account for 1-1.5% of primary enrollment shares, and their market share has
remained constant over the last two decades (Andrabi et al., 2006).
13 Bruns and Rakotomalala (2003) show, in a study of 55 low-income countries, that teacher salaries account for 74
percent of recurring spending by the government on education.
14 The columns of the ﬁgure give the initial salary and pay increments for an additional year of experience and the
rows denote the grade of the civil servant. Primary school teachers are grade 9, middle school teachers are grade 14,
secondary school teachers are grade 16, and head teachers are grade 17.
6
Pay Scale, teachers receive additional allowances for housing, medical expenses and conveyance,
and these allowances can vary (Idara-e-Taleem-o-Aagahi, 2013). One feature of teachers’ wages
that we emphasize is that these are not ’lock-step’ schedules with zero ﬂexibility, since teachers
teaching at similar levels may receive different allowances, and there is some ﬂexibility in the
salary band.
Whether public sector teachers’ wages in Pakistan are ‘adequate’ depends on the comparison.
Comparisons with Indian states show that both Pakistani and Indian teachers earn, on average, 5-7
times GDP per-capita (Siniscalco, 2004 and Aslam, 2013). Comparisons with other professions
again suggest similar levels of remuneration relative to other professionals. Each of these has
obvious problems. Comparisons across countries require that teachers are efﬁciently compensated
in the “benchmark” country. Comparisons across professions are subject both to selection concerns
and differences in the job proﬁles across occupations.15
Teacher salaries in the private sector provide an alternative benchmark. Andrabi et al. (2008)
show that teachers’ wages in private schools were one ﬁfth of teacher salaries in public schools in
2003-2004, and public school salaries have only grown relative to private school salaries since then
(Figure 1). Similar wage gaps have been documented in Colombia, the Dominican Republic, the
Philippines, Tanzania, Thailand, and India (see Jimenez et al., 1991; Muralidharan and Kremer,
2008). These large wage premiums may reﬂect a lack of accountability and the strength of teach-
ers’ unions rather than greater productivity. Absenteeism is high in the public sector, and ﬁring
is rare since teachers are protected by permanent contracts (Chaudhury et al., 2006). In our sam-
ple, public school teachers self-reported absences of 2.6 days per month compared to 1.9 days per
month for private school teachers. Recent research accounting for selection bias in both Pakistan
(Andrabi et al., 2010) and India (Muralidharan and Sundararaman, 2015) shows that attending
private schools, despite a lower per-student cost, improves student outcomes.
Unfortunately, a direct public-private comparison of the wage gap is also confounded by the
large differences in observed teacher characteristics between the two sectors. Appendix Table
A1 shows the large differences in training (90% versus 22% in the public relative to the private
sector), education (51% hold a bachelor’s degree versus 26%), gender (45% female versus 77%),
and local residence (27% local versus 54%). Private school teachers also report 11 years less
teaching experience on average. Using an Oaxaca-decomposition exercise, Andrabi et al. (2008)
argue that controlling for observed characteristics explains little of the wage gap between public
and private school teachers, but there is currently little direct evidence on the link between pay and
productivity in the public sector.
15 Comparisons from the Pakistan Labor Force Survey show that the wages of teachers were 80% of those of
“professionals,” and 110% of all professions combined (Aslam, 2013). These comparisons are fraught with selection
concerns as most formal sector jobs are in urban areas or also in the public sector, with the same wage setting rules.
7
2.1 Natural Experiment
Instead of relying on comparisons across countries or professions, we provide a direct test of the
appropriateness of teacher remuneration: if remuneration is truly benchmarked to outside options,
any decline should decrease teacher quality. If quality does not decline, two possibilities remain:
either the wrong teachers were being hired (those with characteristics that are correlated with high
wage outside options but not correlated with TVA), or public sector salaries are too high. Here ‘too
high’ only means that a reduction in salaries does not affect teacher quality and has no implications
for what constitutes a “fair wage.”
The move to hiring teachers on temporary contracts with a decline in remuneration came about
as follows. In the mid-1990s, the Government of Punjab started exploring changes in hiring prac-
tices, responding to both reports of low accountability and performance, and concerns about the
budgetary implications of high wages and beneﬁts for public sector employees. As these delib-
erations were gathering steam, unanticipated nuclear tests in 1998 led to international sanctions
and a worsening of the budgetary position of the province, providing the ﬁnal impetus for changes
in public sector hiring practices and leading to a much wider use of contract teachers in public
schools. Figure A2 shows that while the number of teachers hired each year varies, correspond-
ing to the practice of “batch” hiring in the province (Bari et al., 2013), the period following the
sanctions (1998-2001) is a uniquely long period of low hiring. After normal hiring resumed in
2002, almost all teachers in the province were hired on untenured, temporary contracts and re-
ceived, as we will show empirically, 35% lower wages than permanent teachers with similar levels
of experience.16
Separating the effects of tenure insecurity and lower compensation is challenging in our study,
but some institutional details may shed light on the different mechanisms. Cyan (2009) notes that
the institution of contract hiring was supported by a more centralized hiring process that relied on
a point system based on employee qualiﬁcations, as well as interview performance. The policy
also dictated that contract employees would undergo increased performance evaluation, and in
surveys, 45% of contract teachers said that performance evaluations were linked to their contract
renewal (Cyan, 2009). Performance evaluation may have increased teacher effort: 74% of surveyed
contract teachers said that they were made to work more than regular teachers, and absenteeism
and disciplinary infractions appeared to be lower among contract teachers. Importantly, as of 2009,
there was no formal process for regularizing the contract teachers who were typically employed
on 3-5 year contracts. Consistent with this, 71% of teachers said that they did not think their jobs
offered them an opportunity for “professional growth,” and 95% of teachers reported working on
a temporary contract for more than three years. Therefore, in 2009, it seems that most contract
16 Contract
arrangements in Punjab became more common from 2000-2001 on (Hameed et al., 2014) and in 2004,
the Government of Punjab announced its Contract Appointment Policy (Cyan, 2009).
8
teachers did not expect to be regularized in the future. This sets a time-frame for the wage savings
from temporary contracts if all temporary contracts were to be converted to permanent in 4 to 7
years, the latter for those hired in 2002. In reality, it wasn’t until 2012 that continued agitation by
existing contract teachers led many to be converted to permanent status, receiving concomitantly
higher wages thereafter.
Our natural experiment allows us to conduct a simple but important exercise to understand the
effects of changes to teacher hiring policies. By examining what happens to teacher quality when
the government decreases salaries by more than one-third for all incoming teachers, we can directly
assess how large-scale contract teacher policies affect the quality of new entrants, as measured by
their effect on student outcomes, with the caveat that the reform jointly affected incentives and
remuneration, rather than remuneration alone.
3 Data
We use data collected across four rounds (2003 to 2007) of the Learning and Educational Achieve-
ment in Punjab Schools Survey (LEAPS). The original sample includes 823 schools (496 public)
in 112 villages of 3 districts in the province of Punjab, with an additional 335 (111 public) schools
entering the sample over the next four years.17 The project was designed as part of a study of
the rise of private schooling and, as a result, all the villages included in the study were randomly
selected from a list frame of villages with at least one private school when the study began in 2003.
As these villages tend to be larger and wealthier, the sample is representative of 60% of the rural
population in the province of Punjab.
For our purposes, two parts of the data collection are key. First, a teacher roster was com-
pleted for all teachers within the school in each year of the survey. This roster included socio-
demographic data on teachers (gender, age, educational attainment) and in the fourth round, month-
level data on when the teacher began teaching. We use variables from the teacher roster to look at
the differences between contract and permanent teachers in demographic characteristics, salaries,
and subject knowledge. Appendix Table A1 provides summary statistics for these characteristics
for both public and private school teachers across the four rounds of the survey.18
Our data collection reveals that most schools in our sample have 1 or fewer teachers per grade;
we only observe multiple teachers teaching in a grade in 26% of public schools and 29% of private
17 The three districts were chosen on the basis of an accepted stratiﬁcation of the province into the better performing
north and central regions and the poorly performing south.
18 At times, we wish to compare teachers in terms of measures that were collected over multiple survey rounds,
such as school facilities or teacher absences. To normalize these measures, we regress them on year ﬁxed effects and
teacher or school ﬁxed effects, depending on the level at which the characteristic is observed. We then use the teacher
or school ﬁxed effect as the teacher-level measure. This process is analogous to how we combine test score data from
multiple years to calculate teacher value-added measures.
9
schools. In Table 1, we report the number of teachers observed teaching each combination of
grades 3, 4, and 5 in both public and private schools. Because teachers teach multiple grades, it is
possible for a teacher to be observed teaching two or more grades even if they are observed once.
For example, 8 public school teachers and 3 private school teachers are only observed once, but
teach grades 3, 4, and 5 simultaneously. We report the teacher counts for both the full sample and
a restricted sample that excludes teachers who ever appear to teach the same class in concurrent
years (that is, more than 25% of their students in year t also were taught by them in year t − 1).
While many teachers are only observed once, which can happen if a teacher quits teaching (this
occurs frequently after marriage in the private sector), transfers to another school, or starts teaching
in 2007, a large number of teachers are observed two or more times, even when teachers who teach
essentially the same students in subsequent years are excluded (615 total public school teachers
observed teaching grade 3, 4, or 5 and 81 total private school teachers).
In the second part of our data collection, to assess learning outcomes, LEAPS tested children in
the survey schools. English, Urdu, and mathematics tests were administered to children in grades
3-6 between 2004 and 2007. In the ﬁrst year of data collection, only classrooms with grade 3
students were tested. In subsequent years, those children were followed to new classrooms, and an
additional cohort of 3rd graders was added in year 3 and followed in year 4. Appendix A discusses
the implementation and scoring of these tests. Here we note that (a) the tests were low-stakes
and designed by researchers to maximize precision over a range of abilities in each grade and (b)
scores could be equated across years using a set of linked questions in each year together with Item
Response Theory as in Das and Zajonc (2010). These test equating methods allow us to score all
children in all years on the same scale in a comparable fashion. Appendix Table A1 documents
test score gains by year over the four rounds of testing in the panels of public and private school
students.
On the day that children were tested, we also asked teachers to take the same test as the children
so that they could assess the test themselves.19 One worry is that these tests, designed to assess
learning by third to ﬁfth graders, are uninformative due to ceiling effects. Appendix Figures A3
and A4 show the histograms of teacher test scores in public and private schools, and although
there are ceiling effects, particularly in math, where 14% of public teachers achieve the maximum,
there is also a great deal of variation. Equated to the child test score distribution, the mean public
teacher test score is 3.04sd higher, but the 5th percentile of teachers was only 1.91sd higher than
the average tested child. As the process of testing teachers was repeated each year, whenever we
observe teachers multiple times, we have multiple observations of the teacher test score, which we
19 Since the test administered to teachers was the same as the test administered to students, unlike other measures
of teacher knowledge, such as the commonly-used Praxis test, this measure is ideal for assessing teachers’ command
of the content knowledge required for the classrooms in which they were teaching.
10
will use to adjust for measurement error. Appendix Table A2 correlates teacher content knowledge
with teacher characteristics for public school teachers.20 Teacher characteristics only explain 7%
of the variation in content knowledge, and reassuringly, having a bachelor’s degree is robustly
correlated with content knowledge. However, the correlation is relatively small (0.2 to 0.3sd),
which could either reﬂect the quality of the degree or ‘learning on the job’ among those without a
degree.21
Teacher quality is identiﬁed following the TVA literature (Rockoff, 2004; Chetty et al., 2014a;
and Kane and Staiger, 2008) by regressing student test scores on a function of their lagged test
scores, round, grade, and teacher ﬁxed effects. Teacher value-added is the estimated teacher ﬁxed
effect. The panel structure of the data, where both students and teachers are observed multiple
times, is important for identiﬁcation: to be included in the value-added calculations, students must
be observed at least twice across consecutive years, since they require a lagged test score to control
for selection. To separate correlation in student outcomes within years from TVA, at least some
teachers must also be observed across years so that round ﬁxed effects are identiﬁed. To estimate
the variance of teacher value-added, we cannot simply take the variance of these value-added
estimates, both because it would be biased by sampling bias and because we cannot separately
identify classroom-level shocks from teacher value-added for teachers who are only observed once.
While this does not bias our estimates when teacher value-added is an outcome variable, as long
as classroom shocks are uncorrelated with the independent variables in the regression, it would
bias estimates of the variance of teacher effects. Therefore, to estimate the variance of teacher
value-added, we focus on the sample of teachers who are observed at least two times in the data.
We observe a total of 1,756 public school teachers in at least one round of the data linked to
22,857 unique public school students and 1,346 private school teachers linked to 9,741 unique
students. Appendix Figures A5 and A6 document this variation in public and private schools.
However, we are only able to estimate TVAs for 1,533 of the public teachers and 975 of the private
teachers. This is primarily because the TVA estimation does not include students if they were not
observed in the prior year. In particular, this means that we cannot calculate TVAs for teachers
who were only observed in the ﬁrst round of the data. Table 2 provides more information on the
sources of variation for the TVA calculations in both public and private schools. When we correlate
TVAs with teacher characteristics, our sample is further reduced to 1,383 public and 294 private
teachers. This is because detailed data on when a teacher started teaching, which allows us to
include our experience controls, was only collected in the fourth round of the LEAPs study. One
limitation of these data is that we cannot identify the association between teacher gender and TVA
20 The regressions for private school teachers yield qualitatively similar results.
21 Interestingly,
gender is another covariate that consistently predicts teacher knowledge. Being a female teacher is
associated with 0.15sd lower mean content knowledge.
11
in public schools when we include school ﬁxed effects. This is because public schools in Pakistan
are not co-educational, and less than 5% of public schools (29) have both a male and a female
teacher during the sample period. As a result, we do not report the association between female and
value-added in the public sector when we control for school ﬁxed effects.
To account for unobservable variables, we can also demean TVA estimates at the school level.22
Since we do not observe teachers in more than one school, we cannot separately identify pure
school effects as opposed to a school simply having better teachers on average. Therefore, the
demeaned TVAs should be interpreted as a within school ranking of teacher quality. Demeaning
at the school level requires that more than one teacher was observed in the school over the course
of the study. TVAs for teachers in the 158 public schools and 86 private schools where only one
teacher was ever observed with tested students are left out of the within-school TVA sample; these
teachers account for 2,357 child-year observations (1,771 unique children) in public schools and
936 child-year observations (414 unique children) in private schools.
4 Teacher Value-Added
4.1 Teacher Effectiveness: Estimating the Variance of Teacher and Class-
room Effects
To measure the variance of teacher and classroom effects in our data, we closely follow Araujo
et al. (2016), extending their methodology to produce the ﬁrst estimates, to our knowledge, from
a low-income country. These are policy-relevant measures since the variances of classroom and
teacher effects are indicative of how much test scores would increase if a student moved to a 1sd
better classroom or teacher. To measure the variance of these effects, we ﬁrst generate estimates of
classroom effects (in our sample, equivalent to a teacher-year effect) by estimating the regression
yit = ∑ βa yi,t −1 I (grade = a) + δ jt + αt + µg + υit , (1)
a
where yit are test scores in math, Urdu, and English for a student i in year t , βa is the grade-speciﬁc
effect of lagged test scores, αt is a year ﬁxed effect, µg is a ﬁxed effect for grade g, and δ jt is
the classroom effect, which includes both idiosyncratic classroom-level shocks, such as having a
22 In practice, we present our estimates for both TVAs that are and are not demeaned at the school level. De-meaning
at the school level means (1) that we can only consider teachers who teach in multi-teacher schools and (2) that our
measures of teacher quality are essentially within-school rankings of teacher quality. If schools try to equalize marginal
products across teachers (e.g. by reallocating resources that substitute for quality toward less effective teachers or
giving more effective teachers larger class sizes), estimating teacher quality within schools may lead us to under-
estimate the true variation in teacher quality.
12
more disruptive student in the classroom in a given year, and the teacher effect. Since teachers do
not change schools in our sample, we cannot separately identify school-speciﬁc effects. Instead,
to estimate the variance of the classroom effects, following Araujo et al. (2016), we de-mean our
estimates of δ jt at the school-level. While demeaning at the school-level may be less attractive
than demeaning at the school-year-grade level, it is a necessity in many low-income countries, like
Pakistan, where there is often only 1 teacher and 1 class per grade in the modal school. Appendix
Figure A7, which plots the distribution of grade sizes in Punjab in 2005, illustrates this fact. To
estimate the variance of δ jt , we cannot simply taking the variance of our estimates of δ jt , since
these estimates have sampling error, upwardly biasing the empirical variance. Instead, we derive
the sampling bias, accounting for the de-meaning procedure, and subtract it from the empirical
variance of the classroom effects.23 This provides us with an unbiased estimate of the variance of
the classroom effects.
To measure the variance of teacher effects, we can exploit the fact that we observe teachers in
multiple classrooms over time. Following Araujo et al. (2016), Hanushek and Rivkin (2012), and
McCaffrey et al. (2009), we take advantage of the fact that the variance of the teacher effects is
Cov(λ jt , λ j,t +1 ), where λ jt is the true de-meaned classroom effect for teacher j in year t . However,
the fact that we observe λ jt , rather than λ jt and that our estimates of school-level means include
multiple observations of the same teacher complicate this approach. If a teacher is associated with
an abnormally high estimated class-effect in one year, this will lead us to infer that her effect is
lower in another year, mechanically inducing a negative correlation between our de-meaned esti-
mates. To ensure that this does not affect our results, when we estimate the variance of the teacher
effects, we de-mean δ jt by subtracting the school-level mean of δ− jt . Even with this correction,
Cov(λ jt , λ j,t +1 ) is an overestimate of the variance of the teacher effects since correlation in the
estimation error in the school means will positively bias the covariance estimate. In Appendix
B, we derive this bias. Then, we arrive at our estimates of the variance of the teacher effects by
subtracting the bias term from Cov(λ jt , λ j,t +1 ).24
Table 3 reports our estimates of the effect of moving to a 1sd better classroom or teacher on test
scores for math, English, and Urdu. In the ﬁrst row, we include the entire sample in the estimation
procedure. In the second row, we restrict the sample to teachers where less than 25% of students
in their class are the same as the students they taught in the previous year to ensure that our results
are not biased by teachers teaching the same students repeatedly. In the ﬁnal row, we restrict our
sample to public school teachers. In the full sample, moving to a 1sd better classroom increases
mean test scores by 0.31sd and moving to a 1sd better teacher increases test scores by 0.21sd.
23 Ourde-biasing procedure exactly follows the one described in Appendix D of Araujo et al. (2016).
24 Thevariances of the teacher effects we estimate are almost identical to the variances of the teacher effects that
we estimate when follow the methodology of Chetty et al. (2014a).
13
Restricting the sample to teachers who teach different students from year to year leads to similar
estimates (Row 2). In Row 3, when we restrict the sample to teachers in public schools, we ﬁnd that
a 1sd better teacher increases test scores by 0.16sd. This estimate suggests that moving a student
from a teacher in the ﬁfth to the ninety-ﬁfth percentile of the public school TVA distribution would
lead to a 0.54sd increase in mean test scores. Our estimates of the variance of the classroom and
teacher effects are larger than the estimates in Ecuador (Araujo et al., 2016), and our estimates of
the variance of teacher effects are on the high end of estimates in the United States (see Chetty
et al. (2014a) and Rockoff (2004)). Given these estimates, teacher quality appears to be at least
an important determinant of student outcomes in low-income countries like Pakistan as it is in the
United States, if not more so.
4.2 Estimating Teacher Effects
Following Rockoff (2004), we estimate TVA as a teacher ﬁxed effect. This method is similar
to the methods of Kane and Staiger (2008), Sass et al. (2014), Chetty et al. (2014a), and Chetty
et al. (2014b), but unlike some of these approaches, the ﬁxed effect approach allows us to estimate
TVA even for teachers who are only observed once in the data. To compute TVA, we estimate the
following regression on our full set of teachers (public and private), including all child-year test
score observations:
yit = β0 + ∑ βa yi,t −1 I (grade = a) + γ j + αt + µg + εit ,
a
where yit is student i’s test score in year t , γ j is the teacher ﬁxed effect, αt is the round ﬁxed effect,
and µg is the grade ﬁxed effect. Then, γ j is the TVA, equivalent to the underlying unexplained
variance in test score gains associated with students having the same teacher. As is conventional
in the TVA literature, we control for year-speciﬁc and grade-speciﬁc shocks, as well as lagged
test scores, which are allowed to affect students in different grades differently. These account for
students’ prior human capital attainment and the selection of students to teachers.
Like Chetty et al. (2014a) and Kane and Staiger (2008), we do not include child ﬁxed effects to
account for additional unobservable selection of students to teachers (Sass et al., 2014). Identiﬁca-
tion with child ﬁxed effects would be based on a smaller sample of 7,696 unique children (one-third
of the sample) who are observed with multiple teachers over time. More worryingly, measurement
error in how teacher codes are entered into the data will lead to false switchers – students who
appear to be switching teachers but actually are not. Even with a small number of false switchers,
this could lead to large biases in the estimation of TVA by inducing spurious correlations between
14
the TVA of teachers with similar ID numbers.25
We also do not use empirical Bayesian methods to estimate TVA. The empirical Bayes ap-
proach proposed by Kane and Staiger (2008) relies on the assumption that TVA is time invariant.26
However, past work shows that teacher effectiveness non-linearly increases with experience in the
ﬁrst 1-2 years of teaching (Rockoff, 2004; Chetty et al., 2011), and we will conﬁrm that this is
the case in Pakistan as well. This violation of the assumptions of time invariance or stationarity is
likely to be particularly problematic among Pakistan’s inexperienced teacher labor force. Among
teachers observed in 2007, 13% of public school teachers and 54% of private school teachers had
less than 3 years of experience. In our context, controlling for teacher experience would likely be
necessary for the assumption of time invariance or stationarity to be valid. Unfortunately, expe-
rience is collinear with year hired, which in our setting, is highly correlated with contract status
due to the sharp change in the hiring regime. Virtually all teachers with 0-5 years of experience
are contract teachers, and virtually all teachers with more than 5 years of experience are perma-
nent teachers. Since we cannot ﬂexibly control for experience without subsuming the temporary
contract effect, our estimates of γ j utilize the full sample of students and teachers, averaging over
teacher effectiveness at different experience levels.
Nevertheless, while we cannot fully non-parametrically control for experience effects, later in
this paper, we control for whether teachers had less than 3 years of experience in 2007, implying
that they had low levels of experience throughout the data collection period, to separate experience
effects from the effects of other teacher characteristics on the TVA estimates. This method exploits
non-linearity in the experience effect identiﬁed in both the literature and our Pakistani data.27
Our ﬁxed effect approach allows us to identify TVA for teachers who are only observed once
in the data, as long as we observe their students at least twice. While we cannot separately identify
teacher and classroom effects for these teachers, as long as the classroom-level shock is exogenous
to our treatments of interest, we can still use this combined measure of teacher and classroom
25 Suppose that 1% of teacher IDs are randomly entered incorrectly. This will have little impact on TVA estimates
that utilize the full sample. But if only 10% percent of students change teachers each year, when identifying variation
comes only from the test scores of students who change teachers, these incorrect entries account for 9 percent of the
variation. In other words, when we restrict the sample to students who change teachers, we always include incorrect
ID entries, but we shrink the number of correct ID entries, increasing the percentage of the variation that is driven by
students with incorrectly entered IDs. For more details, see Appendix C.
26 Chetty et al. (2014a) relaxes time invariance and allows for drift in TVA but still assumes stationarity.
27 Our TVA estimates do no capture teachers’ heterogeneous effects on different students. In reality, such hetero-
geneity may be important for students’ outcomes. For instance, Bau (2015) shows that schools in Pakistan can have
different effects on the outcomes of more and less advantaged students. Relatedly, Aucejo (2011) shows that teachers
responded to the incentive structure of No Child Left Behind in the United States by increasing the outcomes of their
lower ability students at the expense of higher ability students. In other examples, Muralidharan and Sheth (2016),
Antecol et al. (2015), Dee (2007), and Hoffmann and Oreopoulos (2009) measure the effects of the teacher-student
gender match. If teachers have heterogeneous effects on students, our TVA measures can be thought of as capturing
the effect of a teacher on the average student.
15
effects to study the effects of the contract teacher policy on TVA. Additionally, since we focus
on TVA as an outcome variable, decreasing classical measurement error in our TVA estimates (as
methods like empirical bayes do) should not affect our estimates of interest.
Implementing the procedure described in this section results in TVA estimates for 1,533 public
sector teachers and 975 private school teachers. In the next sections, we ﬁrst examine TVA’s
correlations with teacher characteristics. We then use the TVA estimates to assess the link between
productivity and wages, both in terms of the gradient (do higher TVA teachers earn more?) and the
intercept (does lowering wages reduce average TVA?).
4.3 Teacher Value-Added Results
4.3.1 Teacher Characteristics and TVA
Using our TVA estimates, we estimate the association between TVA and student performance and
the link between TVA and observed teacher characteristics for public school teachers using the
following speciﬁcation:
TVA j = β0 + ΓX j + αd + ε j ,
where TVA j is a teacher j’s average value-added over math, Urdu, and English; X j consists of
teacher characteristics, including an indicator variable for some training, an indicator variable for
having a bachelor’s degree or greater, an indicator variable for having 3 or more years of experience
in 2007, an indicator variable for female, an indicator variable for whether a teacher is local, an
indicator variable for whether a teacher has a temporary contract, controls for age and age squared,
and in some speciﬁcations, controls for a teacher content knowledge; and αd is a district ﬁxed
effect. In some speciﬁcations, we also include a school ﬁxed effect.
Table 4 presents the results from this speciﬁcation. Column 1 reports the means of the co-
variates of interest. Columns 2 and 3 report regression results without controlling for teachers’
own test scores, and Columns 4-7 include different measures of teachers’ test scores with the goal
of reducing measurement error in teacher content knowledge. Like in the United States, we are
never able to explain more than 5% of the variation in mean TVA.28 Presaging our discussion of
wages and productivity in later sections of the paper, we ﬁnd no signiﬁcant, positive correlation
between TVA and two key characteristics – education (measured as whether a teacher has a Bach-
elor’s degree) and whether the teacher has some training. In fact, for training, the point estimate
is negative and marginally signiﬁcant when we also include content knowledge. Nevertheless, two
correlations are statistically signiﬁcant and are of particular interest.
28 We arrive at 5% by ﬁrst regressing mean TVA on district or school ﬁxed effects, then regressing mean TVA on
the ﬁxed effects and the teacher characteristics, and then calculating the difference in the adjusted R2 ’s.
16
First, content knowledge, measured as teacher test scores averaged over test scores in all sub-
jects, is signiﬁcantly correlated with estimated TVA (Columns 4 and 5). Columns 6 and 7 reduce
measurement error by instrumenting for the teacher’s ﬁrst cross-subject average test score with
her second.29 Our preferred IV speciﬁcation suggests that a 1sd increase in teacher test scores
increases TVA by 0.30-0.33sd, which is higher than the effects estimated by Metzler and Woess-
mann (2012) (0.1sd in Peru) but similar in magnitude to the effects estimated by Bold et al. (2017)
(0.23sd-0.54sd in Africa). At ﬁrst, it may seem surprising that teacher knowledge is statistically
signiﬁcantly correlated with mean TVA estimates while having a BA or better is not. However,
recall from Appendix Table A2 that having a bachelor’s degree is only associated with a 0.22sd
(see Column 8) increase in a teacher’s average test score. Based on the IV results, the implied
effect of a bachelor’s degree would be about 0.06sd, which is not signiﬁcantly different from the
estimated effect of 0.04sd (see Column 3 of Table 4). Our effect size is also substantially larger
than the effect of IQ (0.04sd) estimated by Araujo et al. (2016). We can speculate that this is driven
in part by the large variation in teacher knowledge levels in Pakistan, where a standard deviation
in the teacher test score distribution in math is nearly as large as a standard deviation in the student
test score distribution (0.87 vs. 1) and a teacher at the 5th percentile scores below a student at the
95th percentile in math on a test designed for primary school students.
Second, experience in the ﬁrst two years of teaching also increases TVA. Columns 2-7 treat
each teacher as a single observation, but unlike the other characteristics in these regressions, ex-
perience is not time invariant. Since we observe teachers multiple times at different levels of
experience, we can use our panel data to better identify experience effects for public school teach-
ers. In Column 8, an observation is a student-year, and we regress mean test scores on teacher
experience and lagged student test scores, controlling for teacher ﬁxed effects, which capture any
time invariant teacher characteristics, using the following speciﬁcation:
mean test scorei jt = β0 + β1 I (exp j ≤ 1) + β2 mean test scorei j,t −1 + γ j + εi jt ,
where i denotes a student, j denotes a teacher, and t denotes a year. I (exp j ≤ 1) is an indicator
variable equal to 1 if a teacher j has 0 or 1 years of experience in time t , and γ j is a teacher ﬁxed
effect. Then, we report β1 , our coefﬁcient of interest. The results in Column 8 suggest that the
experience effect is large: the outcomes of students of teachers with only 0 or 1 years of experience
are 0.3sd worse than those of other students. In Appendix Table A3, we expand this speciﬁcation
to include controls for 0-1, 2, 3, and 4 years of experience. We ﬁnd very large experience effects in
the ﬁrst year: students of a teacher with 0-1 years of experience have test scores between 0.55sd (in
29 The inclusion of teacher test scores causes the sample size to fall since not all teachers took the test.
Instrumenting
for teachers’ ﬁrst test scores with their second test scores further reduces the sample since even fewer teachers took
the test twice.
17
English) and 0.72sd (in math) lower than students of teachers with 5 or more years of experience.
In the second year, the penalty is lower, ranging from -0.47sd for Urdu to (a marginally statistically
signiﬁcant) -0.26sd for English, and by the third year, there are no further signiﬁcant experience
effects.30 Note that because we are comparing the outcomes of the students of the same teacher
over time, these effects are more likely to have a causal interpretation relative to the associations
between TVA and time invariant teacher characteristics.
Appendix Table A4 replicates the regressions of TVA on teacher characteristics for private
school teachers. We ﬁnd almost exactly the same pattern of effects, with only teacher content
knowledge (after correcting for measurement error) and teacher experience consistently affecting
the mean TVAs. As in the public sector, teacher characteristics explain little of the variation in
mean TVAs in the private sector.
4.4 TVA Robustness
Our TVA estimates control for lagged student test scores and allow the effect of lagged student test
scores to depend on the student’s grade to account for the non-random assignment of students to
different teachers. However, if these lagged tests scores do not sufﬁciently account for selection,
our TVA estimates may be biased. We ﬁrst assess the extent of the bias by checking whether adding
additional controls for student and school characteristics alters our TVA estimates. In the new
estimates, we control for the student’s household assets index,31 gender, and parental schooling, as
well as two indices of school facilities that vary over time and time-varying school-level student-
teacher ratios. Even though the new TVAs use substantially more information about students’
socioeconomic status and school-level inputs (jointly, the controls explain 10% of the variation in
mean test scores), they are highly correlated with the old TVAs with correlations of .98 in English,
.97 in math, and .97 in Urdu (see Appendix Table A5).
Our next test relies on an out of sample prediction test following Chetty et al. (2014a). We
focus on children who switched schools and test whether the TVA of a switcher’s new teacher
predicts her test score gains after switching schools, controlling for lagged test scores. If TVA is a
meaningful measure of teacher quality, a teacher’s TVA should predict her student’s learning gains.
The speciﬁc regression speciﬁcation is:
test scorei jt = β0 + β1 TVA j + β2test scorei j,t −1 + αs + εi jt , (2)
30 Estimates of the effects of 1, 2, 3 and 4 years of experience are qualitatively similar for private school teachers,
and follow the same pattern, with large, negative non-linear effects from 0 or 1 years of experience.
31 We create an asset index by predicting the ﬁrst factor of a principal components analysis of indicator variables for
ownership of beds, a radio, a television, a refrigerator, a bicycle, a plow, agricultural tools, tables, fans, a tractor, cattle,
goats, chicken, watches, a motor rickshaw, a scooter, a car, a telephone, and a tubewell following methods discussed
by Filmer and Pritchett (2001).
18
where test scorei jt is the test score of a student i with a teacher j in year t , which can be in math,
Urdu, or English or the the average across all three, TVA j is the value-added of a student’s teacher
in the relevant subject, and αs is a school ﬁxed effect. The sample consists of students who are in a
new school in period t . Because we limit the sample to school-switchers, β1 will not be inﬂuenced
by common shocks at the school-level that are correlated over time.32
Our test proceeds in two steps. We ﬁrst ensure that β1 is not biased by selection between
students and teachers. If students who learn quickly are more likely to sort to certain teachers,
even when they switch schools, then these teachers will appear to have a higher TVA, and these
high TVAs will also be related to students’ outcomes. We follow Rothstein (2010) and test whether
the TVA of a student’s future teacher after a school switch predicts the TVA of her current teacher
(Table 5). Across all subjects, there is no evidence of a correlation between current and future
TVAs, suggesting that when children switch schools, the allocation to speciﬁc teachers mimics
random sorting.
Table 6 reports the estimates from equation 2 and conﬁrms that TVA in a subject is highly
predictive of the students’ test score gains in that subject. For average test scores, a 1sd increase
in TVA increases mean student test score gains by 0.852sd, and this coefﬁcient is signiﬁcant at the
1% level. In fact, for mean test scores, we cannot reject that the true coefﬁcient is 1, as would be
the case if we had estimated the “true” TVA. These results suggest that our TVA estimates are very
predictive of real student gains from teacher quality.
5 Teacher Productivity and Teacher Wages
Before moving to the link between TVA and wages, it is useful to have a a simple framework to
interpret the results. Appendix D provides the formalization of a model where each teacher has
a productivity θ j drawn from a bounded distribution F , with a maximum of θmax and a minimum
of θmin . In the public sector, teachers receive a wage w pub set exogenous by the government, and
the public sector hires randomly from its applicants. In the private sector, due to free entry, private
schools make zero proﬁts and a teacher receives her productivity, θ j . A decline in w pub can then
have one of three potential effects. If w pub is very low relative to the private sector, no teachers
enter the public sector either before or after the wage change. If w pub > θmax both before and after
the decline, then all teachers apply to the public sector in both cases, and jobs in the public sector
are rationed. If w pub is between θmin and θmax after the decline, more productive teachers sort into
the private sector relative to before. In this case, lowering public wages will decrease the quality
32 Focusing on children who switched schools ensures that our test will not ﬁnd spurious correlations between future
and current TVAs due to the fact that school-grade level shocks to the current teachers’ students’ outcomes will effect
the lagged test scores used to calculate the future teachers’ TVAs as described by Chetty et al. (2015).
19
of new entrants. The ﬁnal two cases are illustrated in Figures A8 and A9.
Since our empirical strategy allows us to identify the average productivity of teachers hired
under higher and lower wages, we can directly test which of the ﬁgures is more applicable to
the Pakistani educational system. If the results are in line with the predictions of Figure A8, it
suggests that the government can reduce teachers’ salaries without reducing student learning and
without fear of causing shortages. However, we caution that the regime change we evaluate is
more complex than the model presented here, since it may have also increased the returns to effort
through career concerns.
5.1 Teacher Productivity and Teacher Wages
We now examine the association between wages and TVA. In Table 7, we regress log salaries
separately on public and private teacher characteristics (Column 1) and then include mean TVA in
the regression (Columns 2-4) using the speciﬁcation:
log(salary j ) = β0 + ΓX j + αd + ε j ,
where log(salary j ) is the log of the mean salary of teacher j, and X j consists of the same teacher
characteristics as in equation 2. As before, αd is a district ﬁxed effect, and some speciﬁcations
(Columns 3, 4, and 6) also include school ﬁxed effects.
In public schools, receiving some training is associated with a 52% increase in teacher salaries
and having a bachelor’s degree is associated with a 26% increase.33 In addition, seniority is heavily
rewarded in the public sector, with every additional year of age resulting in a 5.8% (no school ﬁxed-
effects) to 6.3% increase in wages (with school ﬁxed effects). Recall that the ﬁrst two years of
teaching experience have a large effect on TVA. While we cannot include both experience and age
non-parametrically in this Mincerian regression, we can include an indicator variable for whether
the teacher had more than 3 years of experience in the ﬁnal round for which data was collected.
We ﬁnd no additional effect of experience beyond the seniority effect. Similarly, teacher content
knowledge (Column 4) has small and insigniﬁcant effects on teacher salaries. Unsurprisingly,
teachers with temporary contracts make 35% less than teachers with permanent contracts.
Strikingly, every attribute that the public sector appears to reward has no signiﬁcant effect on
TVA. When we add mean TVA to the regressions (Columns 2-4), the coefﬁcient is small, insignif-
icant, and negative. Moreover, adding mean TVA has no effect on the adjusted R2 , suggesting that
mean TVA does not explain any of the variation in salaries. We infer that higher quality teachers
do not appear to be rewarded with higher salaries in the public sector, consistent with our theo-
33 Almost all public school teachers have at least some training. Therefore, the large association between training
and salaries relies on 44 individuals (3% of the sample) who have no training.
20
retical framework. This ﬁnding would be of limited interest if salaries were entirely determined
through a ‘lock-step’ schedule. However, in fact, there is substantial room for salaries that reﬂect
performance, as the adjusted R2 after our extensive controls never exceeds 0.71.
Perhaps TVA cannot be rewarded because it is difﬁcult to observe or verify. Using our data
on private schools, we replicate the speciﬁcations in Columns 2 and 3 for private school teachers
in Columns 5 and 6. The differences in compensation schemes in Column 5 are striking. As
has been noted before (Andrabi et al., 2008), the private sector pays teachers according to their
outside option, penalizing women and teachers who are locally resident. The private sector also
rewards training and education (in similar ways for education but less so for training). However,
the premium on seniority is much lower and TVA is highly correlated with salaries. A 1sd increase
in TVA is associated with a 11% increase in wages, and this coefﬁcient is statistically signiﬁcant
at the 5% level.
In Column 6, we replicate the regression in Column 5 including school ﬁxed effects. The in-
clusion of school ﬁxed effects eliminates the positive relationship between mean TVA and salaries.
There are two possible reasons for this: (1) across school TVA estimates are biased because un-
observably better students attend more expensive schools or (2) the link between teacher pay and
TVA is driven by the fact that better teachers are sorting into higher-paying, better private schools.
While either explanation is possible, given that we ﬁnd little evidence of bias in our across school
TVA estimates in Appendix Table A5 or Tables 5 and 6, we believe that the second explanation
is more likely, indicating that high-performing private schools pay higher wages to attract better
teachers.
Our results suggest that teacher compensation in the public sector does not reward more pro-
ductive teachers, but it is unlikely that this is because teacher productivity is impossible to observe.
In the private sector, more productive teachers work at schools where they earn substantially more
than less productive teachers. Our framework points to the next natural question: would a decline
in public sector wages lower the average quality of public school teachers? To answer this ques-
tion, we now estimate the effects of the contract teacher policy, which lowered wages by 35%, on
the characteristics of individuals entering the teaching profession and on TVAs.
5.2 Methodology
While our TVA measures do not appear to be biased, we cannot simply regress TVA or other
teacher characteristics on a teacher’s contract status to estimate the effect of a contract teacher
policy since contract status is not randomly assigned. The 2% of teachers hired and retained on
temporary contracts prior to 1998, as well as the 17% hired on permanent contracts after 1998, are
likely to be highly selected. Instead, the hiring regime change in 1998 allows us to instrument for
21
contract status using the budgetary shock. Moreover, because the shock changed contract status for
much of the labor pool, our natural experiment allows us to understand the effect of a large-scale
contract teacher policy on teacher labor supply.
To estimate the effect of the contract regime on what types of individuals become teachers, on
which schools and students those individuals are assigned, and on teacher productivity, we ﬁrst
estimate the ordinary least squares regression:
y j = β0 + β1 TempContract j + β2 month hired j
+ β3 month hired j × Post j + αd + ε j , (3)
where y j are the characteristics of teacher j, including her TVA, her students, and the school
to which she is assigned. TempContract j is an indicator variable equal to 1 if a teacher has a
temporary contract and 0 otherwise, month hired j is the time a teacher was hired, measured at the
month level, Post j is an indicator variable equal to 1 if a teacher was hired in or after 1998, and
αd is a district ﬁxed effect. We include time trends in teacher quality to account for the fact that
most of the variation in contract status is driven by whether teachers were hired before or after the
budgetary shock. Moreover, we exclude the small number of (likely highly selected) teachers hired
during the hiring freeze from our sample. For some outcomes, like number of teachers in a school,
student-teacher ratios, and school facilities, we have extreme outliers, likely due to data entry error
and misreporting, that lead to very skewed distributions. To ensure that our results are not sensitive
to these outliers, we exclude the top and bottom 1% of observations for these variables.
Even so, the estimates of β1 from this OLS regression are likely to be biased for several reasons.
First, as we discussed before, it does not account for the selection in contract status for the teachers
who were hired on temporary contracts before 1998 and the teachers who were hired on permanent
contracts after 2002. Second, we typically observe teachers hired on a temporary contract with
fewer years of experience in our data since these teachers are hired later. Since the effects of
experience on student learning are highly non-linear, linear time trend controls that span the entire
sample are unlikely to fully account for these experience effects. However, as we decrease the
bandwidth of the sample, including fewer hiring years around the policy change, we partially
control for experience effects by including fewer contract teachers who are only observed with
very low levels of experience. For example, restricting the sample to a two year bandwidth ensures
we only observe relatively experienced contract teachers since 2004 (round 1) is not included in
the TVA estimation (lagged test scores are not available) and the two year bandwidth sample is
restricted to teachers hired in 2002 and 2003. On the other hand, when we include teachers hired
in 2006 and 2007, we include contract teachers in the sample who are only observed with 0 or 1
22
years of experience.
In our main speciﬁcation, we account for the sources of bias using a fuzzy regression discon-
tinuity design comparing teachers hired right before and after the budgetary shock. This approach
is analogous to an instrumental variables regression that incorporates time trends and includes a
subset of the sample around the budgetary shock. Therefore, to estimate β1 without selection on
contract status, we instrument for TempContract j with the indicator variable Post j . The ﬁrst stage
of this two stage least squares strategy is then:
TempContract j = δ0 + δ1 Post j + δ2 month hired j
+ δ3 month hired j × Post j + αd + µ j . (4)
Following Lee and Lemieux (2010), who discuss regression discontinuities with discrete data, such
as time, we cluster our standard errors at the month hired level.
We report these regressions in the following sequence. We ﬁrst check for potential biases that
could arise from the systematic allocation of contract teachers to schools and parents; our main
concern is that contract teachers may have been assigned to children who learned faster. We then
estimate the effect of temporary contracts on TVA to examine the effect of the policy change on
teacher productivity. Finally, we examine whether the policy affected the composition of teachers,
by looking at the differences in teacher characteristics before and after the regime change.
5.3 Results
5.3.1 Existence of a First Stage
The ﬁrst panel of Figure 2 shows the discontinuous effect of being hired after 1998 on contract
status. Being hired after 1998 is associated with an 80 percentage point increase in the probability
that a teacher is hired on a temporary contract. Each point in the ﬁgure is the average of the outcome
variable for teachers hired that month (ranging from 1 to 182 teachers). The second panel shows the
similar discontinuity in salaries, with regression equivalents in Table 8. Each coefﬁcient in the table
is the result from separate regressions of the form speciﬁed either in equation 3 (OLS) or equation 4
(fuzzy RD with a four-year bandwidth or three-year bandwidth such that the sample includes 1994-
1997 and 2002-2005 or 1995-1997 and 2002-2004). In the OLS regression (Row 1, Column 1),
temporary contract status is associated with a 28% decline in a teacher’s salary, which is somewhat
less dramatic than the fuzzy RD estimates of 44-54% (Row 1, Column 3 and 5). These effect sizes
are also consistent with the effect of temporary contracts in the Mincerian regression (35%), which
accounts for observable characteristics of teachers but not unobservable characteristics that may
23
be related to contract status. For brevity, we only present two RD bandwidths here (3 and 4 years).
However, the negative effect of temporary contracts on log teacher salaries is signiﬁcant at the 1%
level for all the remaining bandwidths that we tested (5-10 years) with effect sizes ranging from
69-83%.
5.3.2 Effect of the Policy on Allocation of Teachers to Schools
Figure A10 plots school facilities (as indices), student-teacher ratios and the number of teachers
against the year a teacher started teaching with regression equivalents in Table 9. Both the ﬁg-
ure and the regression results show that contract teachers were assigned schools with fewer extra
facilities. Rows 3 to 9 present the coefﬁcients for the components of the extra facilities index sep-
arately, and the effect of contract status on the extra facilities index is driven by schools with fewer
libraries, who are less likely to have computers or electricity. In addition, Figure A10 and the ﬁnal
three rows of Table 9 suggest that parental education (particularly father’s education) was lower
for children assigned to contract teachers. The index of assets appears to be somewhat higher,
but this is statistically insigniﬁcant. These results are consistent in both across- and within-school
regressions. Given the large number of outcome variables we consider and the fact that we do
not ﬁnd consistent effects for most outcomes, we only focus on two bandwidths for the RD of the
allocation of teachers to schools and students (3 and 4 years). However, when we turn to our key
outcome of interest – our measure of teacher productivity – we present results for a wider range of
bandwidths.
5.3.3 Were Contract Teachers Assigned to Lower Ability Children?
The fact that contract teachers were assigned to smaller schools with fewer extra facilities and
lower levels of parental education could suggest that they were teaching children whose learning
was systematically lower. If this is indeed the case, our TVA estimates for contract teachers may be
negatively biased. Fortunately, the panel structure of our data set allows us to directly test whether
higher or lower ability students were selectively matched to contract teachers, which is ultimately
the main plausible source of bias in the TVA estimates. We therefore test directly whether contract
teachers were assigned to schools with higher ability students by testing whether student test score
trends predict a school being assigned a contract teacher. In Table 10, we ﬁrst test whether time
trends are the same for schools that never received contract teachers and schools that eventually
received them. We estimate
yit = β0 + β1 yearit + β2 I (Received Contract Teacher)s +
β3 I (Received Contract Teacher)s × yearit + ΓXit + εit ,
24
where yit is the outcome variable, mean student test scores, I (Received Contract Teacher)s is an
indicator variable equal to 1 if a school ever hired a contract teacher and 0 otherwise, yearit is the
survey year, and Xit is a vector of controls consisting of district ﬁxed effects and lagged student
test scores. The sample does not include any student-year observations from schools that have
contract teachers in the survey year (or received one in a past year). As Column 1 shows, test
scores are not different on average between schools that did and did not receive contract teachers.
Moreover, there is little difference in pre-trends in test scores between public schools that do and
do not receive contract teachers. If anything, the pre-trends for schools that later received contract
teachers are negative.
Next, we assess whether test-scores gains predict receiving a contract teacher at the student
instead of the school level. Column 2 shows that, within schools, there is no signiﬁcant difference
between the test scores or test score trends of students who will and will not eventually receive
contract teachers. Finally, Column 3 tests whether yearly test score gains predict having a con-
tract teacher. It shows that, across schools, a student’s average test score gains before receiving a
contract teacher are not predictive of whether he or she later receives a contract teacher. In sum-
mary, despite the fact that contract teachers were assigned to children with less educated fathers
and schools that were smaller, there is no evidence to suggest that learning among children who
later received a contract teacher was systematically different.
5.3.4 Effect of Contract Status on Student Test Scores
Table 11 now presents the results of the OLS and RD speciﬁcations of mean TVA on contract
teacher status, and the ﬁnal two panels of Figure 2 are the graphical representations of the reduced
form of the regression discontinuity speciﬁcations. Since TVA is our main outcome of interest, we
report the instrumented results for the full sample and for bandwidths of 2-7 years around the policy
change. The OLS effect of teacher contract status on mean TVA both across and within schools is
small and the sign varies (-0.004 and 0.024). However, this estimate may be downwardly biased by
selection of teachers hired before 1998 into contract teacher status and the relative inexperience of
contract teachers during the years students were tested. To account for these effects, we estimate
the fuzzy RD in Rows 2 to 8 of Table 11. The smaller bandwidths do not include teachers (such as
those hired in 2006 and 2007) who are observed with lower levels of experience. Consistent with
this, estimated effect sizes for contract teachers are larger when the bandwidth is 2, 3, or 4 years
(although the estimates for the 2 year bandwidth, which includes only 227 teachers, are imprecise).
The effect sizes are generally similar within and across schools, with positive effect sizes around
0.2 standard deviations for the smaller bandwidths. Larger bandwidths include contract teachers
observed with lower experience levels, which is likely to negatively bias our estimates, and assume
linear time trends across a larger sample of teachers. While temporary contract teachers no longer
25
have signiﬁcant positive effects for these larger bandwidths, we never ﬁnd evidence of a strong
negative contract teacher effect. Indeed, when we compare teachers in the same schools, regardless
of bandwidth, we never estimate a negative contract teacher effect. Therefore, while there is not
conclusive evidence that the contract policy raised teacher quality, it is very unlikely that the policy
lowered teacher productivity.
We address two additional issues. First, to adjust the analytical standard errors for estimation
error in TVA, we also estimate the RD p-values with a clustered bootstrap procedure (see Appendix
Table A6). The pattern of signiﬁcance for the estimates is similar to the pattern obtained using
analytic standard errors. Second, we test if contract teachers are more effective because they
have smaller class sizes (though student-teacher ratios are not signiﬁcantly different in the RD).
In Appendix Table A7, we repeat the RD analysis after re-estimating the TVAs controlling for
average school-year student-teacher ratios. The results are qualitatively and quantitatively similar.
Overall, we ﬁnd no evidence of a decline in TVA following the regime change and some evidence
that the TVA of contract teachers was higher than the TVA of permanent teachers hired prior to the
regime change.
5.3.5 Effect of the Policy on Teacher Characteristics
Interestingly, and consistent with the idea that salaries may be higher than is necessary to incen-
tivize high quality teachers to enter the teaching profession, we ﬁnd no evidence of a change in
key characteristics of the teacher pool. Figure 3 shows broad trends since 1970 towards greater
feminization, higher education and a greater proportion of younger teachers, but despite yearly
variation in teacher characteristics, there is little evidence of a large trend break following the
policy change.
The remaining rows in Table 8 formally compare the characteristics of contract and permanent
teachers. OLS speciﬁcations containing the full sample appear to reﬂect the general but non-linear
trend that teachers hired later are more educated; having a temporary contract increases the proba-
bility of having a bachelor’s degree by 32 percentage points. However, in the RD design, the effect
of having a temporary contract on bachelor’s degree is no longer signiﬁcant and is substantially
smaller. In fact, there are no robustly signiﬁcant differences between the characteristics of teachers
hired on permanent and temporary contracts. The fact that the change in regime did not lead to
a decline in the fraction of teachers with a bachelor’s degree suggests that the outside options for
these teachers remain below the considerably lower contract teacher wages. Interestingly, the RD
estimates suggest that the fraction of female teachers increased following the establishment of the
policy (and continued to increase in Figure 3), although the coefﬁcient is insigniﬁcant and impre-
cisely estimated. We discuss the potential implications for teacher recruitment below in Section
5.4.
26
5.3.6 Quality of the Teaching Pool Over Time
While applicants hired right after the budgetary shock appear to be similar to applicants hired
previously, the quality of applicants may still have changed over time. In Figure 3, there does seem
to be a reduction in teacher training and an increase in workforce feminization after 2002 (although
both may continue pre-existing trends and being female is not negatively associated with TVA).
To assess whether the quality of new teachers is decreasing over time, we would like to compare
the test scores of the students of contract teachers hired earlier to those hired later. This poses
several problems. First, on average, we observe more recently hired teachers with fewer years of
experience. Thus, we will only compare the outcomes of the students when we see them with
inexperienced contract teachers (teachers with 0 or 1 year of experience) to mitigate the effects
of different levels of teacher experience. A second challenge is that later hires are only observed
with students in later testing rounds. If student test scores are improving over time for unrelated
reasons, and if we do not control for year of testing, the effect of being a later hire will be upwardly
biased. Therefore, we also include a control group of permanent teachers hired before 1998 in our
regression sample, so that we can include testing round ﬁxed effects. We estimate the regression:
yit = β0 + β1 month hired j + β2 Post j + β3 Post j × month hired j
+ ∑ βg yi,t −1 I (grade = g) + αt + εit ,
g
where yit is the test score of a student i in year t , month hired j is the time a teacher j is hired,
with data available at the month-level, Post j is an indicator variable equal to 1 if a teacher is hired
after 1998 and 0 otherwise, yi,t −1 is a student’s lagged test score, g is her grade, and αt is a round
ﬁxed effect. β3 then captures the effect of the month a teacher was hired on student outcomes
for teachers hired after 2002. The coefﬁcient β2 does not have a clear interpretation. Because the
sample is limited to inexperienced contract teachers, β2 here is not analogous to the reduced form
contract teacher effect in the fuzzy regression discontinuity. Instead, it captures a combination of
the contract teacher effect and the inexperience effect. When we estimate this equation, β3 is a
small and insigniﬁcant -0.007 (0.024). Accordingly, there is little reason to believe that over time
teacher quality decreased in response to decreased teacher salaries and teacher tenure.
5.4 Natural Experiment Robustness
In this section, we assess threats to identiﬁcation and our ability to extrapolate the results beyond
the speciﬁc context studied here.
Student Selection. The robustness tests in Section 4.3 indicate that our TVA estimates are not
27
biased by selection of students to teachers. Therefore, it is unlikely that differences in student
quality between contract and non-contract teachers are driving our results. Nonetheless, we can
more formally test whether either observed or unobserved student quality drives the differences in
student outcomes between contract and non-contract teachers. We follow Altonji and Mansﬁeld
(2014), who argue that the classroom level means of observable student characteristics can proxy
for unobservable characteristics related to student outcomes. In revised TVA estimates (Appendix
Table A8), we control for the classroom-level means of two of the most likely determinants of
student-to-classroom and student-to-school sorting – lagged test scores and wealth. The point
estimates are qualitatively and quantitatively similar to those reported previously in Table 11.
Selective Attrition: Assessing Student and Teacher Attrition. Our estimates of the contract
teacher effect may also be biased if the students of contract teachers are differentially more likely
to exit the sample or lower quality contract teachers are more likely to leave schools. 7% of contract
teachers and 8% of permanent public teachers who appear in the data are not observed in the fourth
and ﬁnal round of data collection, while 73% of students observed appear in the fourth round (73%
of those taught by a permanent teacher, as well as 73% of those taught by a contract teacher).
Typically 80% of students observed in one year are observed in the next year.34 Table A9 tests for
both the types of attrition that could bias our estimates. In Column 1, we show that conditional on
the year a student ﬁrst appeared in the panel, the percent of times a student had a contract teacher
has no signiﬁcant effect on whether she appears in the fourth round of the panel. Column 2 shows
that the percent of rounds a student was observed with a contract teacher does not predict the total
number of years she is observed. In the remaining columns, we test for teacher attrition. Column
3 shows that the mean TVA of a contract teacher does not signiﬁcantly predict whether she was
present in the fourth round of the panel, and Column 4 shows that it does not predict the number
of years a teacher was observed (conditional on the year she started teaching). Overall, we ﬁnd no
evidence of either differential attrition of the students of contract teachers or differential attrition
of contract teachers by quality.
Permanent vs. Temporary Income. While the majority of contract teachers did not expect to be
normalized in 2009 (Cyan, 2009), contract teachers did win a court case in 2012 which led many
teachers to be tenured and receive salaries commensurate with permanent teachers. Therefore,
teachers may have entered contract teacher teaching with the expectation that the salary reductions
were temporary. If this is the case, to interpret our results, we must determine how much initial
34 Students do not appear in the sample in a given year for a variety of reasons: they may be absent on the day of the
test, they may have dropped out of primary school, or they may have moved on to a secondary school and are therefore
no longer tested. For example, a student who was in 3rd grade in round (2004) will be in 6th grade and may no longer
be in one of the primary schools included in our sample in round 4 (2007). In cases where students were absent on the
day of the test, they typically reappear in the sample in later years; the probability that a student who was observed in
year 1 is observed in year 3 is 74% (as opposed to the 64% we would expect if students never returned to the sample).
28
salary reductions reduced permanent incomes for contract teachers. This exercise requires several
additional assumptions. We assume teachers had rational expectations and that the discount rate is a
conservative 3%. Furthermore, we assume that a teacher expects to work for 40 years. For teachers
hired in 2002, temporary contracts reduced their salaries by 35% for 10 of those 40 years. Even
with this very low discount rate, the contract policy reduces permanent wages for teachers hired
in 2002 by 13%, suggesting that there is still substantial room to lower wages without negatively
affecting teacher quality.
External Validity. In Pakistan, the contract teacher policy was instituted in response to an
economic crisis, which may have also negatively affected teachers’ outside options. Thus, we
should be cautious in applying these results to other contexts where teachers’ outside options are
unchanged. However, there is reason to believe that lowering teacher salaries, even in the absence
of an economic crisis, would not result in a decline in productivity. We observe teachers who are
hired as late as 2007, 9 years after the nuclear tests. The results in Section 5.3.6 indicate that these
teachers are no worse than those hired in 2002. The recession in 1998 did not last 10 years; in
fact, according to the World Bank, Pakistan experienced a period of relatively high per capita GDP
growth from 2003-2007 (2.7-5.5% per year). Similarly, in 1997, the unemployment rate according
to the World Bank was 5.8% and by 2007, it was 5.1%. Moreover, in our own data, we do not ﬁnd
that salaries fell for private school teachers hired after 1998. Taken together, these facts suggest
that even if teachers’ outside options fell after the nuclear tests, they had likely recovered by 2007.
6 Conclusion
This paper makes two important contributions to our understanding of the educational production
function in low income countries. First, we provide among the ﬁrst estimates of the correlations
between teacher observable characteristics and teacher quality from a low income country. The
effect of good teachers on student test scores is large, and likely larger than in the U.S. This raises
obvious questions of how teachers should be recruited and the relative beneﬁts of systems with
a probationary period followed by tenure for high performers. Our one result that adds to this
discussion is that tests of content knowledge could potentially improve the quality of new entrants.
Second, this paper builds on work by Duﬂo et al. (2014) and Muralidharan and Sundararaman
(2013) on the quality of contract teachers. Like these papers, which provide clean experimental
estimates of the contract teacher effect, we ﬁnd that contract teachers have as great as and perhaps
moderately higher TVAs than permanent teachers. The large-scale policy change that we study
allows us to assess equilibrium effects of these policies, and we are able to demonstrate the robust-
ness of the previous experiments to such a change in an entirely different context. In fact, given
the large experience effects in the ﬁrst two years of teaching, it is likely that the previous papers
29
underestimated the positive effects of experienced contract teachers.
The effect that we ﬁnd may be linked to the greater hiring of female teachers after the regime
change. One story consistent with our results is that when salaries go down, the number of male
applicants decreases. If female applicants feel that they will not be fairly treated in a recruitment
process (or, indeed, if they are not), the teaching pool will not include educated and high TVA
female teachers. It could be that the lower salaries induced more women to apply and be hired
for these jobs, leaving the quality of new entrants unchanged after the hiring regime change. We
cannot directly test this since applicant data are not kept, but it would be consistent with a number
of patterns that we ﬁnd, and in particular, the lack of any effect of teacher salaries on observable
characteristics, including education levels and test scores.
Our results also suggest that, at least in low income countries, policies that increase wage levels
to attract higher-skilled teachers, like those advocated by Auguste et al. (2010), would be costly
and ineffective. Since higher levels of education are not correlated with TVA and only weakly
correlated with teacher test scores, the best teachers are not those with the greatest education, and
government outlays increase by paying these teachers their outside options in low-income coun-
tries. More remarkably, wages are already so high that even a 35% decline has no impact on the
education levels of new recruits. This paper suggests that public sector compensation could be sig-
niﬁcantly redesigned to better account for the realities of low-income countries. Combining lower
salaries (or salaries that are more strongly tied to teacher productivity) with greater investment
in other school characteristics or student incentives could allow low-income countries to generate
considerable ﬁscal savings.
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34
Tables
Table 1: Variation in Grades Taught by Teachers and Number of Times Teachers are Observed
(1) (2) (3) (4) (5) (6) (7) (8)
Public Sector Private Sector
Observed Observed Observed Observed Observed Observed Observed Observed
Once Twice Three Times Four Times Once Twice Three Times Four Times
Only Grade 3 235 37 14 14 346 35 2 0
Restricted Sample 235 33 8 11 346 32 1 0
Only Grade 4 166 14 1 0 274 8 0 0
Restricted Sample 166 12 0 0 274 8 0 0
Only Grade 5 0 0 0 0 0 0 0 0
Restricted Sample 0 0 0 0 0 0 0 0
Grade 3 and 4 31 235 53 12 29 83 19 6
Restricted Sample 31 31 1 0 29 11 1 0
Grade 3 and 5 13 37 8 0 11 14 6 0
Restricted Sample 13 35 5 0 11 9 1 0
Grade 4 and 5 25 110 18 0 27 31 19 0
Restricted Sample 25 26 1 0 27 10 0 0
Grades 3, 4, 5 8 48 214 83 3 28 25 28
Restricted Sample 8 14 9 1 3 6 2 0
This table reports counts of the number of teachers who are observed teaching only grade 3, only grade 4, only grade 5, only
grades 3 and 4, only grades 4 and 5, and grades 3, 4, and 5 by how many times they were observed. The restricted sample ex-
cludes teachers who are ever observed teaching two classes of students who appear to be the same in two consecutive years (90%
or more of the students in year t were taught by the same teacher in year t − 1).
Table 2: Sources of Variation in Teacher Value-Added Calculations
(1) (2) (3) (4)
Number of Teachers Number of Students Teachers in Schools With Students in Schools
> 1 Teacher With Tested With > 1 Teachers
Students With Tested Students
Public, Rd 1 486 8,340 4 131
Private, Rd 1 303 3,617 0 0
Public, Rd 2 593 9,327 214 3,290
Private, Rd 2 336 3,340 97 846
Public, Rd 3 1007 16,946 884 15,320
Private, Rd 3 579 6,777 524 6,247
Public, Rd 4 1103 15,357 812 12,610
Private, Rd 4 599 5,911 478 5,020
This table presents the breakdown of the data used to calculate within and across school TVAs. Within school
TVAs require teachers to teach in schools where more than one teacher has tested students (such that the mean
school effect is not equal to the sole teacher’s TVA). The sample of students driving variation in the within
school TVAs are the students who attend schools where more than one teacher has tested students.
35
Table 3: Classroom and Teacher Effects
(1) (2) (3) (4) (5) (6) (7) (8)
Math English Urdu Average
Class Teacher Class Teacher Class Teacher Class Teacher
Full Sample 0.321 0.258 0.300 0.190 0.312 0.184 0.311 0.211
Restricted Sample 0.308 0.252 0.277 0.285 0.275 0.270 0.287 0.269
Public Schools Only 0.356 0.199 0.337 0.134 0.351 0.152 0.348 0.162
This table reports the effect of moving to a 1sd better classroom and the effect of moving to a
1sd better teacher on students’ test scores in math, English, and Urdu. Test scores have been
standardized to have a mean of 0 and a standard deviation of 1. In the ﬁrst row, the sample
includes all students and teachers in public and private schools. In the next row, the sample
only includes classrooms where at least 75 percent of students had not been taught by the same
teacher in the previous year. In the ﬁnal row, the sample is restricted to students and teachers in
public schools.
36
Table 4: Relationship Between Teacher Characteristics and Mean Teacher Value-Added for Public School Teachers
(1) (2) (3) (4) (5) (6) (7) (8)
Covariate Mean Mean TVA Mean TVA Mean TVA Mean TVA Mean TVA Mean TVA Mean Test Score
Female 0.445 0.070*** N.A. 0.082*** N.A. 0.086*** N.A.
(0.026) (0.026) (0.032)
Local 0.273 0.025 0.008 0.023 -0.005 0.017 -0.113
(0.025) (0.031) (0.028) (0.048) (0.036) (0.079)
Some Teacher Training 0.904 -0.023 -0.101 -0.093 -0.216* -0.125 -0.598*
(0.055) (0.072) (0.075) (0.126) (0.119) (0.329)
Has BA or Better 0.514 0.054** 0.043 0.012 0.009 -0.066 -0.175
(0.025) (0.031) (0.033) (0.058) (0.046) (0.108)
Had > 3 Years o f Exp in 2007 0.868 0.060 0.076 0.038 0.166* -0.046 0.180
(0.038) (0.052) (0.047) (0.097) (0.072) (0.276)
TemporaryContract 0.229 -0.003 0.049 -0.019 0.055 0.019 0.065
(0.036) (0.048) (0.043) (0.082) (0.057) (0.105)
Mean Teacher Knowledge 3.041 0.090*** 0.018 0.298*** 0.332*
(0.024) (0.038) (0.072) (0.176)
Have 0 or 1 Years Exp. 0.040 -0.305**
(0.135)
37
Lagged Mean Score 0.324 0.717***
(0.013)
Fixed Effects District School District School District School Teacher
Number of Observations 1,383 1,383 919 919 622 622 27,089
Adjusted R Squared 0.224 0.450 3.247 0.727 0.068 0.038 0.721
Clusters 471 471 469 469 440 440 583
F 2.031 1.194 0.230 0.417 73.428 2.741
This table reports estimates of the association between TVA and teacher characteristics. The association between female and TVA in the public sec-
tor cannot be credibly estimated in the presence of school ﬁxed effects because the public sector is not co-educational. Very few public schools (29)
are observed with both male and female teachers over the course of the sample. The ﬁrst column reports the means of the covariates of interest. For
columns 2-7, observations are at the teacher level and characteristics are time invariant. Column 8 identiﬁes within-teacher experience effects, control-
ling for teacher ﬁxed effects, and regressing student outcomes on whether a teacher had 0 or 1 year of experience. Observations for this column are at
the student-year level. The F-statistic is for a F-test of all the covariates in columns 2-5. In columns 6 and 7, it is the F-statistic from the ﬁrst stage of
the instrumental variables regression. Standard errors are clustered at the school level.
Table 5: Does Future Teacher Value-Added Predict Current Teacher Value-Added When Students
Change Schools?
(1) (2)
Coefﬁcient (se) N
Forward Lag of English 0.051 3,231
(0.049)
Forward Lag of English (Within School) -0.023 1,976
(0.056)
Forward Lag of Math -0.076 3,231
(0.061)
Forward Lag of Math (Within School) -0.017 1,976
(0.036)
Forward Lag of Urdu -0.081 3,231
(0.072)
Forward Lag of Urdu (Within School) 0.017 1,976
(0.040)
Forward Lag of Mean Score -0.033 3,231
(0.067)
Forward Lag of Mean Score (Within School) 0.002 1,976
(0.046)
This table tests for bias in the teacher value-added calculations. The
current teacher value-added of students who change schools in the next
period is regressed on the value-added of their future teacher. Obser-
vations are at the child level, and standard errors are clustered at the
teacher level.
Table 6: Out-of-Sample Validation of TVAs
(1) (2) (3) (4)
Math Test English Test Urdu Test Mean Test
Score Score Score Score
Math TVA 0.781***
(0.065)
English TVA 0.857***
(0.068)
Urdu TVA 0.845***
(0.077)
Mean TVA 0.852***
(0.078)
Lagged Score Control Y Y Y Y
Number of Observations 3,822 3,822 3,822 3,822
Adjusted R Squared 0.557 0.542 0.590 0.636
Clusters 1,090 1,090 1,090 1,090
This table tests if TVAs predict the test score gains of school changers who
are allocated to the new teachers. If the TVA estimates perfectly predict the
“true” teacher value-added, these coefﬁcients should be 1. Standard errors are
clustered at the teacher level.
38
Table 7: Relationship Between Mean TVA and Log Salary for Public and Private School Teachers
(1) (2) (3) (4) (5) (6)
Log Salary Log Salary Log Salary Log Salary Log Salary Log Salary
Public Public Public Public PRIVATE PRIVATE
Mean TVA -0.007 -0.028 -0.044 0.111** -0.011
(0.014) (0.025) (0.036) (0.046) (0.049)
Female -0.036*** -0.035*** N.A. N.A. -0.413*** -0.287***
(0.013) (0.013) (0.043) (0.047)
Local -0.052*** -0.051*** -0.049 -0.019 -0.178*** -0.043
(0.019) (0.019) (0.032) (0.044) (0.029) (0.035)
Some Teacher Training 0.518*** 0.518*** 0.392*** 0.838*** 0.165*** 0.127***
(0.141) (0.141) (0.140) (0.317) (0.045) (0.040)
Has BA or Better 0.255*** 0.255*** 0.263*** 0.213*** 0.334*** 0.282***
(0.019) (0.019) (0.028) (0.043) (0.045) (0.042)
Had > 3 Years o f Exp in 2007 0.063 0.064 0.120* 0.117 0.020 0.058*
(0.042) (0.042) (0.064) (0.099) (0.029) (0.031)
TemporaryContract -0.354*** -0.355*** -0.327*** -0.310***
(0.032) (0.032) (0.059) (0.091)
Age 0.058*** 0.058*** 0.063*** 0.039 0.016** 0.022***
(0.015) (0.015) (0.020) (0.029) (0.007) (0.008)
Age2 -0.0005*** -0.0005*** -0.001** -0.0002 -0.0002** -0.0002*
(0.0002) (0.0002) (0.0002) (0.0003) (0.0001) (0.0001)
Mean Teacher Knowledge 0.034
(0.027)
Mean Salary 6,987 6,987 6,987 6,745 1,403 1,403
Fixed Effects District District School School District School
Adjusted R Squared 0.616 0.615 0.662 0.707 0.459 0.768
Number of observations 1,383 1,383 1,383 919 807 807
F 108.304 96.471 35.025 14.450 38.522 16.157
Clusters 471 471 471 469 294 294
This table reports estimates from regressions of log mean teacher salaries in public (columns 1-4) and private
(column 5 and 6) schools on teacher characteristics, including mean TVA (columns 2-6) and average teacher test
scores across subjects (column 4). The association between female and log salaries in the public sector cannot be
credibly estimated in the presence of school ﬁxed effects because the public sector is not co-educational. Very
few public schools (29) are observed with both male and female teachers over the course of the sample. All re-
gressions include either district or school ﬁxed effects, and standard errors are clustered at the school level.
39
Table 8: Effect of the Discontinuity on Teacher Characteristics
(1) (2) (3) (4) (5) (6)
OLS SE RD (3 Year) SE RD (4 Year) SE
Log(Salary) -0.284*** 0.062 -0.554* 0.273 -0.444** 0.205
Bachelor’s 0.318*** 0.032 0.003 0.186 0.109 0.140
Some Training 0.003 0.031 0.013 0.120 0.010 0.096
Local -0.017 0.037 -0.006 0.178 -0.066 0.134
Age Started 0.072*** 0.024 1.193 1.550 0.943 1.116
Single 0.148*** 0.032 -0.006 0.176 0.053 0.136
Female -0.005 0.044 0.288 0.254 0.273 0.190
Mean Teacher Knowledge 0.129** 0.062 0.132 0.245 0.011 0.229
This table presents OLS and fuzzy regression discontinuity results for the effect of tempo-
rary contracts on teacher characteristics. The RD includes either teachers hired 4 years before
1998 and 4 years after 2001 or teachers hired 3 years before 1998 and 3 years after 2001.
Standard errors are clustered at the month hired level for the regression discontinuity results
and the school level for the OLS results. Log(salaries), which were observed multiple times
over several years, were normalized by calculating the teacher ﬁxed effect, controlling for
year ﬁxed effects and de-meaned at the district-level. Each cell is a coefﬁcient estimate (or
standard error estimate) for the temporary contract teacher effect.
40
Table 9: Effect of the Discontinuity on Student Characteristics and School Characteristics
(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11)
Mean OLS SE RD SE RD SE RD SE RD SE
(3 Year) (Within School) (4 Year) (Within School)
School Attributes
Basic School Facilities -0.473 0.066 0.059 0.433 0.270 0.274 0.248
Extra School Facilities -0.607 -0.480*** 0.115 -1.025* 0.582 -0.922** 0.434
Library -0.039 -0.118*** 0.031 -0.350* 0.178 -0.295** 0.125
Computer -0.136 -0.040** 0.017 -0.145* 0.087 -0.170** 0.067
Sports -0.076 -0.117*** 0.026 -0.296 0.188 -0.200 0.153
Hall -0.048 -0.030 0.019 -0.075 0.079 -0.087 0.076
Wall -0.117 -0.029 0.029 0.117 0.101 0.134 0.088
Fans -0.129 -0.085** 0.034 -0.118 0.126 -0.131 0.101
Electricity -0.102 -0.099*** 0.035 -0.218* 0.113 -0.211** 0.087
Number Teachers 0.294 0.438 0.786 -0.295 2.615 -0.772 2.012
Student Teacher Ratio 6.671 1.701 1.127 -1.399 6.273 2.784 5.492
41
Parental Attributes
Student Household Assets -0.236 0.044 0.091 0.693 0.473 0.154 0.316 0.453 0.372 0.236 0.263
Student Mother Education -0.065 -0.077*** 0.023 0.020 0.129 -0.073 0.093 -0.001 0.116 -0.121 0.073
Student Father Education -0.057 -0.042 0.026 -0.130 0.094 -0.154* 0.082 -0.134 0.081 -0.166** 0.071
This table presents OLS and fuzzy regression discontinuity results for the effect of temporary contracts on student and school characteristics. The
4 year RD includes teachers hired 4 years before 1998 and 4 years after 2001. The 3 year RD includes teachers hired 3 years before 1998 and 3
years after 2001. Standard errors are clustered at the month hired level for the regression discontinuity results and the school level for the OLS re-
sults. Characteristics observed multiple times over several years were normalized by calculating the teacher or school ﬁxed effect (depending on the
level at which the characteristic is observed), controlling for year ﬁxed effects. Each cell is a coefﬁcient estimate (or standard error estimate) for the
temporary contract teacher effect.
Table 10: Do Student Test Score Trends Predict Being Taught by a Contract Teacher?
(1) (2) (3)
Mean Test Scores Mean Test Scores Had a Contract Teacher
Year 0.134*** 0.145***
(0.013) (0.013)
I (Received Contract Teacher) 0.048 0.069
(0.078) (0.083)
Year × I (Received Contract Teacher) -0.015 -0.011
(0.023) (0.024)
Mean Test Score Gain -0.014
(0.016)
District FE Y Y Y
School FE N Y N
Grade by Lagged Test Score Interactions Y Y N
Number of Observations 25,296 25,296 15,956
Adjusted R Squared 0.637 0.677 0.037
Clusters 478 478 497
This table tests whether better students are allocated to contract teachers. The ﬁrst column compares trends
in student test scores before the receipt of a contract teacher in schools that did and did not receive con-
tract teachers. The next column compares the test score gains of students within schools who did or did not
receive contract teachers before the receipt of the contract teacher. The ﬁnal regression regresses an indica-
tor for whether a student ever had a contract teacher on their mean test score gains (residualized by testing
round and grade) in the years prior to receiving a contract teacher. In this sample, each student is observed
once. Standard errors are clustered at the school level.
Table 11: The Effect of Teacher Contract Status on TVA
(1) (2) (3) (4) (5) (6) (7) (8)
Mean TVA SE One-Sided T-test N Within School Mean TVA SE One-Sided T-test N
OLS (Full Sample) -0.004 0.042 0.541 1,337 0.024 0.026 0.181 1,278
RD (Full Sample) -0.004 0.052 0.533 1,337 0.056 0.041 0.088 1,278
RD (2 Year) 0.840 0.550 0.068 227 0.360 0.322 0.137 201
RD (3 Year) 0.219 0.241 0.184 376 0.254** 0.123 0.022 336
RD (4 Year) 0.350 0.234 0.070 393 0.193* 0.097 0.026 350
RD (5 Year) -0.074 0.120 0.732 661 0.035 0.057 0.268 604
RD (6 Year) -0.026 0.106 0.598 690 0.040 0.053 0.225 631
RD (7 Year) -0.036 0.106 0.632 692 0.035 0.052 0.250 632
This table regresses mean TVAs on whether a teacher has a temporary contract in all public schools using the ordinary least squares
and 6 fuzzy regression discontinuity speciﬁcations. In the RD speciﬁcations, contract status is instrumented for with an indicator vari-
able for whether a teacher was hired after 1998. All regressions contain linear time trends which are allowed to differ before and after
the budgetary shock and district ﬁxed effects. The table presents instrumental variables (RD) speciﬁcations for the full sample and for
bandwidths of 2-7 years before and after the budgetary shock. Observations are at the teacher level, and standard errors are clustered
at the school level in the OLS speciﬁcation and the month hired level in the regression discontinuity speciﬁcations. Columns 3 and 7
report p-values for a one-sided t-test of whether the temporary contract effect is negative.
42
Figures
Figure 1: Teacher Salaries in Public and Private Schools
Figure 2: Teacher Contract Status, Salary, and Productivity by Year Hired
43
Figure 3: Trends in Teacher Characteristics by Month Hired
44
Appendix
Appendix A describes how our test score data was collected, and Appendix B details the derivation
of the bias term in the estimate of the variance of the teacher effects. Appendix C documents how
data entry errors in teacher ids could lead to greater bias in TVA estimates that control for child
ﬁxed effects. Appendix D provides a theoretical framework to understand the effects of public
sector wage reductions on the quality of teachers entering the public sector.
Appendix A: Test Data
In each round of the LEAPS data collection, we tested students in math, Urdu (the vernacular), and
English. To avoid the possibility of cheating, project staff, with clear instructions not to interfere,
administered the test directly to students. Test booklets were retrieved after class, so there was
no missing testing material. Tests were scored and equated across the four rounds using Item
Response Theory, yielding scores in each subject with a mean of 0 and a standard deviation of
1 (Das and Zajonc, 2010). Item response theory weights questions differently according to their
difﬁculty and allows us to equate tests over years so that a standard deviation gain in year 1 is
equivalent to a standard deviation gain in year 4. The tests could be equated because we included
linking questions across any two years and for some questions, across multiple years.
Table 2 provides more information on the sources of variation for the TVA calculations. In
year one, since only 3rd graders were tested, very few students were observed in schools where
more than one classroom was tested. In future years, some students were held back, others were
promoted, and another sample of 3rd graders was added in year 3, allowing students in a larger
number of classrooms to be tested. Columns 1 and 2 describe the sample used to calculate the
cross-school TVA estimates. Columns 3 and 4 describe the variation used to calculate the within
school TVA measures.
45
Appendix B: Derivation of Bias
In this appendix, we derive the relationship between Cov(λ jt , λ j,t +1 ), where λ jt is our estimate of
the de-meaned class effect associated with teacher j in year t , and our object of interest, Var(γ j ),
which is the variance of the teacher effects. To derive the bias, we assume that εi jt is i.i.d and
homoskedastic with variance σ 2 . Following from equation 1, and given the fact we do not include
the estimates for teacher j in our estimate of the school’s mean,
N
jt Nkt
∑i=1 εi jt ∑kt ∑i=1 εikt 1k= j
λ jt = λ jt + − ,
N jt ∑kt Nkt 1k= j
where i indexes a student, and N jt is the number of students in the class of teacher j in year t . Now,
assume that λ jt = γ j + θ jt , where γ j is the time-invariant teacher effect and θ jt is the idiosyncratic
class-level effect, which is not correlated over time. Then,
Nkt Nkt
∑kt ∑i=1 εikt 1k= j ∑kt ∑i=1 εikt 1k= j
Cov(λ jt , λ j,t +1 ) = Var(γ j ) + Cov , .
∑kt Nkt 1k= j ∑kt Nkt 1k= j
The ﬁrst term on the right-hand side is our term of interest. The second term is the bias, which we
must estimate, and we deﬁne as Φ. To arrive at our estimable expression for the bias, we see that
σ2
E (Φ) = E .
∑kt Nkt 1k= j
46
Appendix C: Incorrect Variation in Teacher Switching Due to
Data Entry Errors
In this appendix, we show how a small amount of data misentry can lead to a large amount of
bias when we include child ﬁxed effects in the TVA estimation. Suppose that 1% of teacher IDs
are randomly entered incorrectly. If 10% of students change teachers each year, when identify-
ing variation comes only from the test scores of students who change teachers, these incorrect
entries account for 9% of the variation. To arrive at this number, note that there are three cases
where a student-year observation will provide identifying variation in a speciﬁcation that includes
child ﬁxed effects: (1) the teacher ID was incorrectly entered, but no switch actually occurred
(probability = 0.01 × 0.9 = 0.009), (2) the teacher ID was correctly entered and a switch occurred
(probability = 0.99 × 0.1 = .099), and (3) the ID was incorrectly entered and a switch occurred
(probability = 0.1 × 0.01 = 0.001). Then the probability that the teacher ID is mis-attributed in an
observation that provides identifying variation is (0.009+00..099
01
+0.001) = 0.09.
In order to assess potential bias more formally, consider a case where students are identical
and TVA is randomly distributed, so there is no correlation between a student’s future teacher’s
TVA and his current teacher’s TVA as long as she changes teachers. Now, also assume that a
student has a probability p of changing teachers each year, and an ID has a probability e of being
incorrectly entered. Then, when the TVA of teacher is calculated for teacher j, it will be a weighted
mean of the teacher’s true TVA and the TVAs of teachers of any students with mis-attributed IDs.
Therefore,
p e
E (TVA j ) = TVA j + TVA j ,
e(1 − p) + p(1 − e) + ep e(1 − p) + p(1 − e) + ep
where TVA j is the mean TVA in the teacher population and TVA j is the estimate of the TVA for
teacher j. This expression formalizes the intuition that the bias decreases in the true probability of
switching p and increases in the error rate e.
47
Appendix D: Theoretical Framework
Suppose there are N teachers and M < N positions in the public sector. Each teacher has a pro-
ductivity θ j drawn from a bounded distribution F , with a maximum of θmax and a minimum of
θmin . In the public sector, teachers receive a wage w pub set exogenous by the government, and the
public sector hires randomly from its applicants. As Section 5.1 shows, public wages are in fact
unrelated to productivity, consistent with this assumption. In the private sector, due to free entry,
private schools make zero proﬁts and a teacher receives her productivity, θ j . Note that this implies
a link between productivity and wages in the private sector, consistent with our ﬁndings in Table
7. For simplicity, teachers can costlessly apply to a public sector job or go directly to the private
T (w pub )
sector. If she applies, a teacher will get a public sector job with probability p = M , where T
is the endogenous number of teachers applying to public positions. If she does not get the public
sector job, she enters the private sector and receives the private sector wage. Since applying to the
public sector is costless, a teacher will always apply for a public sector job if θ j < w pub .
Then, for a given w pub , there are three possible outcomes:
1. w pub < θmin : In this case, even the least productive teacher makes more in the private sector
than they would in the public sector, so no teachers enter the public sector, and there is a
shortage in the public sector.
2. w pub > θmax : In this case, even the most productive teachers would make more in the public
sector, so all teachers apply to the public sector, and the average productivity in the public
θmax
sector is θ min
θ j f (θ j )∂ θ j . Therefore, there is no shortage since there are N > M applicants.
3. θmin < w pub < θmax : Then, there exists θ ∗ = w pub such that all teachers with productiv-
ity greater than θ ∗ do not apply to the public sector and all teachers with productivity
w pub
less than θ ∗ do. Thus, the average productivity of the public sector is θmin θ j f (θ j )∂ θ j <
θmax
θmin θ j f (θ j )∂ θ j . In this case, it is ambiguous whether there is a shortage of teachers since
T = N × F (θ ∗ ) may be less than or greater than M .
The ﬁrst corner case isn’t relevant for our empirical context, since we observe that there are teachers
entering the public sector before and after the wage change. Therefore, when we study the effect
of a decline in w pub to w pub < w pub , we focus on the second two possible equilibria under w pub and
w pub , in which at least some teachers always enter the public sector. First, consider the case where
w pub > θmax . Then, there are two possibilities once wages decline to w pub :
θmax
1. w pub > θmax , and the average productivity in the public sector is still θ min
θ j f (θ j )∂ θ j . In
this case, there is no shortage (T > M ), since all teachers apply for public positions.
48
2. w pub < θmax , and ∃ θ ∗∗ = w pub such that all teachers with productivity greater than θ ∗∗ do
not apply to the private sector and all teachers with productivity less than θ ∗∗ do. Then, the
pub w θmax
new average productivity of the public sector will be θmin θ j f (θ j )∂ θ j < θmin
θ j f (θ j )∂ θ j .
Therefore, under w pub , average productivity in the public sector declines. As before, it is
ambiguous whether there is a shortage.
Now consider the case where θmin < w pub < θmax . Then, under θmin < w pub < w pub < θmax , there
will be a new θ ∗∗ < θ ∗ , where all teachers with θ j > θ ∗∗ do not apply to the public sector. In this
pub w pubw
case, average productivity in the public sector declines from θmin θ j f (θ j )∂ θ j to θmin θ j f (θ j )∂ θ j .
Again, it is ambiguous whether there is also a shortage.
Thus, when we study the effect of the wage decline in our data, there are two empirically
relevant possibilities. The ﬁrst is that the average productivity of entering public school teachers
remains the same after the wage decline, suggesting that both w pub and w pub are greater than θmax ,
and there is no shortage under either wage. The second possibility is that average productivity
of public school teachers declines, suggesting that w pub < θmax , while w pub may be less than or
greater than θmax , and a shortage may occur. Appendix Figures A8 and A9 graph these two cases.
Appendix Figure A8 shows the case where even after the salary reduction public school salaries
are greater than private school salaries for all teachers, so all teachers continue to apply to public
sector positions. Appendix Figure A9 shows the case where the salary reduction leads private
salaries to be greater than public salaries for a subset of teachers. In this case, the most productive
teachers no longer apply to the public sector.
49
Appendix Tables
Table A1: Summary Statistics
(1) (2) (3) (4) (5) (6)
Government Private
Mean SD N Mean SD N
Female 0.449 0.497 3,829 0.768 0.422 4,733
Local 0.273 0.445 3,827 0.538 0.499 4,731
Some Training 0.904 0.294 3,829 0.221 0.415 4,731
BA Plus 0.514 0.500 3,829 0.255 0.436 4,734
Mean Salary 7671 ($129) 3746 ($63) 3,829 1407 ($24) 997 ($17) 4,731
Temporary Contract 0.229 0.420 3,824 0.838 0.368 4,646
Year Started 1,990.80 10.710 3,432 2,002.17 7.749 3,159
Mean Days Absent 2.644 3.297 3,825 1.936 3.368 4,728
Mean Teacher Test Score 3.041 0.569 1,175 2.861 0.606 1,046
Mean School Basic Facilities -0.519 0.831 3,686 0.606 1.353 4,697
Mean School Extra Facilities -0.607 1.401 3,686 0.716 1.033 4,697
Mean Student Household Assets -0.236 0.242 1,699 0.484 1.022 1,311
Mean Student Mother Primary Education 0.298 0.212 1,699 0.378 0.276 1,311
Mean Student Father Primary Education 0.580 0.245 1,699 0.739 0.242 1,311
Mean Change in Math Scores 0.393 0.499 1,533 0.355 0.488 975
Year 2 - Year 1 0.206 0.647 557 0.226 0.546 322
Year 3- Year 2 0.438 0.463 662 0.511 0.403 316
Years 4 - Year 3 0.475 0.561 1,041 0.354 0.490 573
Mean Change in English Scores 0.393 0.474 1,533 0.388 0.461 975
Year 2 - Year 1 0.303 0.652 557 0.187 0.459 322
Year 3- Year 2 0.375 0.454 662 0.408 0.402 316
Years 4 - Year 3 0.462 0.530 1,041 0.389 0.490 573
Mean Change in Urdu Scores 0.444 0.453 1,533 0.423 0.434 975
Year 2 - Year 1 0.306 0.633 557 0.317 0.459 322
Year 3- Year 2 0.444 0.424 662 0.497 0.368 316
Years 4 - Year 3 0.533 0.502 1,041 0.445 0.451 573
Mean Change in Mean Scores 0.410 0.413 1,533 0.372 0.399 975
Year 2 - Year 1 0.272 0.575 557 0.243 0.411 322
Year 3- Year 2 0.419 0.372 662 0.472 0.327 316
Years 4 - Year 3 0.490 0.461 1,041 0.396 0.409 573
This table presents teacher-level summary statistics across 4 rounds of the LEAPS survey (2004-2007). Changes
in test scores are calculated by averaging over the difference between a student’s test scores in time t and time
t − 1. Household assets and school basic and extra facilities are predicted from a principal components analysis of
indicator variables for the presence of different assets, and school facilities and are normalized by year observed.
50
Table A2: Correlations Between Teacher Test Scores and Teacher Characteristics in the Public
Sector
(1) (2) (3) (4) (5) (6) (7) (8)
Math Math English English Urdu Urdu Mean Mean
Female -0.252*** N.A. -0.110* N.A. -0.116*** N.A. -0.159*** N.A.
(0.042) (0.057) (0.039) (0.037)
Local 0.021 -0.047 0.006 -0.089 -0.006 -0.026 0.007 -0.054
(0.043) (0.090) (0.063) (0.115) (0.043) (0.085) (0.038) (0.070)
Some Teacher Training 0.311 0.222 0.281 0.226 0.107 -0.037 0.233 0.137
(0.211) (0.300) (0.214) (0.288) (0.134) (0.180) (0.150) (0.197)
Has BA or Better 0.246*** 0.225*** 0.312*** 0.268*** 0.201*** 0.154** 0.253*** 0.216***
(0.051) (0.085) (0.061) (0.094) (0.042) (0.072) (0.039) (0.061)
Had > 3 Years o f Exp in 2007 -0.040 0.023 0.092 -0.002 0.071 0.206 0.041 0.075
(0.099) (0.184) (0.091) (0.190) (0.069) (0.130) (0.072) (0.134)
TemporaryContract -0.111* 0.110 0.212*** 0.369*** 0.013 0.185 0.038 0.221**
(0.064) (0.135) (0.068) (0.140) (0.056) (0.116) (0.049) (0.102)
Fixed Effects District School District School District School District School
Number of Observations 1,105 1,105 1,105 1,105 1,105 1,105 1,105 1,105
Adjusted R Squared 0.070 0.042 0.062 0.167 0.049 0.114 0.085 0.200
Clusters 19.125 2.637 15.886 5.406 8.121 2.508 20.595 5.979
F 491 491 491 491 491 491 491 491
This table reports estimates of the association between teacher test scores and teacher characteristics. The association between
female and content knowledge in the public sector cannot be credibly estimated in the presence of school ﬁxed effects because
the public sector is not co-educational. Very few public schools (29) are observed with both male and female teachers over the
course of the sample. Observations are at the teacher level and characteristics are time invariant. In cases where a teacher was
tested more than once, the outcome variables are the average across multiple test scores. Standard errors are clustered at the
school level.
Table A3: Non-Linearities in Within-Teacher Experience Effects
(1) (2) (3) (4)
Math Urdu English Mean
Has 0 or 1 Years o f Exp.
-0.722*** -0.677*** -0.548*** -0.589***
(0.269) (0.208) (0.194) (0.197)
Has 2 Years o f Exp. -0.425** -0.470*** -0.256* -0.346**
(0.188) (0.154) (0.149) (0.136)
Has 3 Years o f Exp. -0.112 -0.124 -0.033 -0.080
(0.170) (0.134) (0.146) (0.124)
Has 4 Years o f Exp. -0.076 -0.065 -0.024 -0.070
(0.146) (0.116) (0.105) (0.093)
Teacher FE Y Y Y Y
Lagged Test Scores Y Y Y Y
Number of Observations 26,508 26,508 26,508 26,508
Adjusted R Squared 0.624 0.644 0.647 0.721
Clusters 569 569 569 569
This table tests for non-linearities in the effect of teacher experience on stu-
dent test scores. All regressions control for teacher ﬁxed effects and lagged
student test scores. The sample is restricted to public school teachers. Stan-
dard errors are clustered at the school level.
51
Table A4: Relationship Between Teacher Characteristics and Mean Teacher Value-Added for Private School Teachers
(1) (2) (3) (4) (5) (6) (7) (8)
Covariate Mean Mean TVA Mean TVA Mean TVA Mean TVA Mean TVA Mean TVA Mean Test Score
Female 0.768 -0.006 -0.002 -0.008 -0.037 0.051 -0.496**
(0.029) (0.043) (0.032) (0.061) (0.052) (0.234)
Local 0.538 -0.038* -0.047 -0.037 -0.050 -0.047 -0.234**
(0.023) (0.030) (0.025) (0.048) (0.037) (0.103)
Some Teacher Training 0.221 0.002 0.002 -0.017 -0.045 -0.018 -0.009
(0.026) (0.042) (0.029) (0.065) (0.045) (0.235)
Has BA or Better 0.255 0.055* 0.002 0.062** 0.064 0.031 0.291**
(0.030) (0.044) (0.031) (0.062) (0.054) (0.128)
Had > 3 Years o f Exp in 2007 0.467 0.040 0.034 0.034 0.039 0.053 -0.027
(0.024) (0.031) (0.027) (0.045) (0.056) (0.186)
TemporaryContract 0.838 0.019 -0.002 0.041 0.056 0.029 0.127
(0.032) (0.045) (0.033) (0.066) (0.050) (0.181)
Mean Teacher Knowledge 2.861 0.066*** -0.001 0.232*** -0.084
(0.025) (0.045) (0.069) (0.160)
Have 0 or 1 Years Exp. 0.194 -0.301***
(0.075)
52
Lagged Mean Score 0.275 0.682***
(0.028)
Fixed Effects District School District School District School Teacher
Number of Observations 808 808 561 561 198 198 27,089
Adjusted R Squared 0.104 0.295 0.123 0.239 0.099 -0.100 0.720
Clusters 294 294 289 289 174 174 347
F 1.707 0.687 2.960 0.697 37.653 0.419 317.594
This table reports estimates of the association between TVA and teacher characteristics for private school teachers. The ﬁrst column reports the means
of the covariates of interest. For columns 2-7, observations are at the teacher level and characteristics are time invariant. Column 8 identiﬁes within-
teacher experience effects, controlling for teacher ﬁxed effects, and regressing student outcomes on whether a teacher had 0 or 1 year of experience.
Observations for this column are at the student-year level. The F-statistic is for a F-test of all the covariates in columns 2-5. In columns 6 and 7, it is
the F-statistic from the ﬁrst stage of the instrumental variables regression. Standard errors are clustered at the school level.
Table A5: Correlation Between TVA Speciﬁcations
(1) (3)
Across Schools Within Schools
English 0.977 0.955
Math 0.969 0.951
Urdu 0.963 0.944
English, math, and Urdu TVAs are calculated
with and without individual level controls for
gender, age, household assets, basic and ex-
tra facilities indices, and student-teacher ra-
tios. Each cell of the table gives the corre-
lation between the TVA estimated with the
parsimonious speciﬁcation and the TVA esti-
mated with the detailed speciﬁcation.
Table A6: Bootstrapped Regression Discontinuity Results
(1) (2) (3) (4) (5)
Bandwidth (Years) Mean TVA P-value Within School, Mean TVA P-value
Full Sample -0.004 0.213 0.056* 0.062
2 0.840** 0.030 0.360 0.186
3 0.219 0.248 0.254* 0.058
4 0.350* 0.076 0.193** 0.048
5 -0.074 0.809 0.035 0.347
6 -0.026 0.625 0.040 0.325
7 -0.036 0.668 0.035 0.347
This table replicates the fuzzy regression discontinuity estimates of the effect of
temporary contract status on TVA using a bootstrap procedure to estimate the p-
values to account for estimation error. The bootstrap was clustered at the month
hired level. The estimates are based on 10,000 random samples of the data. The
coefﬁcients reported are the same coefﬁcients as in Table 11.
53
Table A7: Regression Discontinuity Results Including Student-Teacher Ratio Controls
(1) (2) (3) (4) (5)
Bandwidth (Years) Mean TVA Se Within School, Mean TVA Se
Full Sample -0.016 0.056 0.054 0.041
2 0.716 0.526 0.354 0.311
3 0.267 0.276 0.279** 0.138
4 0.225 0.211 0.208* 0.106
5 -0.059 0.108 0.041 0.058
6 -0.009 0.098 0.045 0.054
7 -0.011 0.096 0.040 0.054
This table replicates the fuzzy regression discontinuity estimates of the effect
of temporary contract status including controls for school-year student-teacher
ratios. Standard errors are clustered at the month hired level.
Table A8: Regression Discontinuity Results Controlling for Classroom Mean Characteristics
(1) (2) (3) (4) (5)
Bandwidth (Years) Mean TVA Standard Error Within School, Mean TVA Standard Error
Full Sample 0.013 0.0614 0.079** 0.039
2 1.215* 0.598 0.786* 0.423
3 0.272 0.261 0.263* 0.138
4 0.348 0.237 0.188* 0.108
5 -0.112 0.145 0.020 0.058
6 -0.051 0.125 0.035 0.056
7 -0.054 0.123 0.033 0.054
This table replicates the fuzzy regression discontinuity estimates of the effect of temporary con-
tract status on TVA. TVA estimates include controls for the mean household asset index of a
classroom and mean lagged student test scores in the classroom. Standard errors are clustered at
the month hired level.
54
Table A9: Tests for Selective Attrition of Students and Teachers
(1) (2) (3) (4)
Student Attrition Teacher Attrition
Present In Year 4 Years Observed Present In Year 4 Years Observed
Percent o f Rounds Observed with aContract Teacher -0.015 -0.038
(0.019) (0.028)
Mean TVA 0.026 0.015
(0.070) (0.142)
Year Student Entered Panel FE Y Y N N
District FE Y Y Y Y
Year Teacher Started FE N N Y Y
Number of Observations 22,596 22,596 298 298
Adjusted R Squared 0.157 0.503 0.057 0.203
Clusters 512 512 200 200
This table examines whether the students of contract teachers selectively leave the sample and whether lower quality contract
teachers selectively leave the sample. The outcome variables are an indicator variable for whether a student was in the sample in
round 4, the number of rounds a student was observed, an indicator whether a teacher was in the sample in round 4, and the num-
ber of rounds a teacher was observed. In the ﬁrst two columns, the sample is all tested public school students. In the second two,
it is all contract teachers. Standard errors are clustered at the school level.
55
Appendix Figures
Figure A1: Basic Pay Scale for Pakistani Civil Servants
Figure A2: Number of Teachers Hired Per Year in the Sample
56
Figure A3: Teacher Test Scores in Public Schools
Figure A4: Teacher Test Scores in Private Schools
Figure A5: Number of Rounds Public School Teachers and Students are Observed
57
Figure A6: Number of Rounds Private School Teachers and Students are Observed
Figure A7: Third Grade Sizes in Public Schools in Punjab
Figure A8: Case I: w pub , w pub ≥ θmax
58
Figure A9: Case II: w pub < θmax
Figure A10: School and Parent Characteristics by Teacher Month Hired
59