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Examining The Link Between Teacher Wages And Student Outcomes: The Importance Of Alternative Labor Market Opportunities And Non-Pecuniary Variation


Abstract and Figures

Researchers using cross-sectional data have failed to produce systematic evidence that teacher salaries affect student outcomes. These studies generally do not account for non-pecuniary job attributes and alternative wage opportunities, which affect the opportunity cost of choosing to teach. When we employ the methodology used in previous studies, we replicate their results. However, once we adjust for labor market factors, we estimate that raising teacher wages by 10% reduces high school dropout rates by 3% to 4%. Our findings suggest that previous studies have failed to produce robust estimates because they lack adequate controls for non-wage aspects of teaching and market differences in alternative occupational opportunities. © 2000 by the President and Fellows of Harvard College and the Massachusetts Institute of Technolog
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Susanna Loeb and Marianne E. Page*
Abstract Researchers using cross-sectional data have failed to produce
systematic evidence that teacher salaries affect student outcomes. These
studies generally do not account for non-pecuniary job attributes and
alternative wage opportunities, which affect the opportunity cost of
choosing to teach. When we employ the methodology used in previous
studies, we replicate their results. However, once we adjust for labor
market factors, we estimate that raising teacher wages by 10% reduces
high school dropout rates by 3% to 4%. Our  ndings suggest that previous
studies have failed to produce robust estimates because they lack adequate
controls for non-wage aspects of teaching and market differences in
alternative occupational opportunities.
I. Introduction
DISCUSSIONS about school policy often focus on the
relationship between school resources and student
performance, but empirical studies of this relationship have
failed to produce systematic evidence that added resources
lead to improvements in standard measures of student
achievement. In comprehensive summaries of empirical
research, Hanushek (1986, 1997)  nds that student out-
comes are not consistently related to either teacher salaries
or per pupil expenditures. Using national, longitudinal data
sets, recent papers by Grogger (1996), Betts (1995), and
Altonji (1988) have produced similar results.
These  ndings are at odds with a handful of studies that
indicate that schools and teachers matter. Altonji (1988), for
example,  nds that schools may account for up to 8% of
permanent wage variance, and a recent analysis by Han-
ushek, Kain, and Rivkin (1998) suggests that at least 7% of
the variance in students’ test scores may be explained by
variation in teacher quality. Several recent studies have also
produced evidence of a relationship between measurable
teacher characteristics and student outcomes. Ferguson
(1991), for example,  nds that in Texas teacher performance
on a statewide certi cation exam is positively related to
student outcomes, and Ehrenberg and Brewer (1994)  nd
that the selectivity of the college a teacher attends positively
in uences test score growth.
These  ndings add a new dimension to the puzzle: if
teacher quality affects student achievement, then why do
studies that regress measures of student outcomes on teacher
wages produce such weak results? In the broader labor
market, Murnane, Willett, and Levy (1995) have shown that
one measure of worker ability—individual test scores—is
positively associated with wages, but studies of this relation-
ship in the teacher labor market produce mixed results.1One
ostensible explanation for the lack of an empirical relation-
ship is that teacher wages are unrelated to teacher quality,
because school district administrators are unable to identify
the most quali ed teachers from the pool of teacher appli-
cants. The problem with this explanation is that, even if
school districts are unable to identify teacher quality, one
would expect the supply of high-ability teachers to increase
with teacher wages. Therefore, even with random selection
from the pool of potential teachers, the average quality of
teachers should increase as the opportunity cost associated
with becoming a teacher falls.
An alternative explanation is that teacher wages do
matter, but that the empirical approaches employed to assess
these effects have not adequately isolated the elasticity of
interest. For example, even if districts can attract more-
skilled teachers by offering higher wages, it may be difficult
to identify a positive relationship between wages and student
outcomes using cross-sectional variation across school dis-
tricts, because different school districts face different teacher
supply curves in quality-wage space, due, for example, to
cross-sectional differences in non-pecuniary job attributes.
Most existing studies use cross-sectional variation to iden-
tify the effect of teacher wages.
In this study, we consider the potential importance of
controlling for alternative labor market opportunities and
non-pecuniary school district characteristics when trying to
assess the degree to which teacher wages affect student
outcomes. If these factors in uence the average quality of
teachers and are correlated with wages, then failure to
incorporate them into regression analyses will make it
difficult to identify the existence of teacher wage effects. We
develop an empirical model of the relationship between
teacher wages and student outcomes, measured by students’
Received for publication September 11, 1998. Revision accepted for
publication October 5, 1999.
* Stanford University and University of California at Davis, respectively.
We would like to thank Kelly Bedard, John Bound, Charlie Brown, Jill
Constantine, Paul Courant, Julie Cullen, Tom Downes, David Figlio,
George Johnson, Shiela Murray, Steve Rivkin, and seminar participants at
U.C. Berkeley, U.C. Davis, The City University of New York, Cornell
University, Duke University, The Federal Reserve Bank of Chicago,
University of Illinois, University of Michigan, University of New Mexico,
RAND, Stanford University, Swarthmore College, The Urban Institute,
Vanderbilt University, University of Washington, The College of William
and Mary, The World Bank, Yale University, and AEFA for their helpful
suggestions. We would also like to thank Jennifer Zanini for her careful
research assistance.
1Ballou and Podgursky (1997)  nd that relative wages have no effect on
the SAT scores of teachers, but Figlio (1997)  nds that, within local labor
markets, there exists a signi cant positive relationship between teacher
salaries and teacher quality, measured by undergraduate college selectivity
and subject matter expertise. In another paper, Figlio (1996) controls for
district-speci c effects and  nds that raising teacher salaries increases the
probability of hiring more-quali ed teachers only in non-unionized
districts. Manski (1987)  nds that salaries do not affect the ability
distribution of new teachers but that they do affect the size of the teaching
pool, and Murnane et al. (1991)  nd that increased salaries increase teacher
The Review of Economics and Statistics, Augu st 2000, 82(3): 393–4 08
r2000 by the P resident and Fellows o f Harvard College and the Massachusetts In stitute of Technology
educational attainment, that incorporates non-wage at-
tributes associated with teaching together with alternative
labor market opportunities. When we estimate this model we
produce statistically signi cant, robust estimates of the
effects of teacher wages on high-school dropout rates and
college attendance rates, which suggest that raising the
wages of teachers by 50% will reduce high-school dropout
rates by more than 15% and increase college enrollment
rates by approximately 8%. We also employ the methodol-
ogy used in previous studies and are able to replicate their
results. Our comparison suggests that previous studies have
failed to  nd robust effects because they have not adequately
controlled for interdistrict variation in the non-pecuniary
aspects of teaching and market differences in alternative
occupational opportunities.
In the next two sections, we discuss the most common
empirical models that have been used to estimate teacher
wage effects, outline our empirical approach, and compare it
to the approaches used in existing studies. Section IV
provides descriptive statistics on the evolution of teacher
wages over time, which helps clarify why it may be
important to control for alternative wage opportunities. In
sections V and VI, we present the results of our analysis of
the effect of teacher wages on student outcomes. In the  nal
section, we conclude with policy implications.
II . A Br ief O ver view o f t he Sch ool P r odu ctio n F u nct ion
Liter ature
Hanushek’s 1986 and 1997 summaries demonstrate that
empirical assessments of teacher wage effects have mostly
failed to provide evidence that teacher wages matter. Only
nine of the sixty teacher salary studies cited in his 1986
paper, for example, produced wage coefficient estimates that
were both positive and statistically signi cant. One interpre-
tation of the literature is that teacher wages are unrelated to
student outcomes. Another possibility is that teacher wages
appear to be unimportant because the empirical strategies
that have been employed to assess their effects miss some
important features of the teacher labor market. Most of the
empirical models that have been used to estimate teacher
wage effects are based on permutations of the following
Yis 5a1 b 1Ws1Zsb21Xisb31 e is (1)
where Yis is an outcome measured for student iwho attends
school s(usually the student’s test score), Wsis the log of the
average wage paid to teachers at school s,Zsis a vector of
factors common to all students attending school s(such as
the average socioeconomic composition of enrollees), and
Xis is a vector of other factors that are speci c to student i
(such as family background). Assuming that teacher salaries
impact student outcomes because of their effect on teacher
quality, bˆ1can be interpreted as an estimate of the slope of
the supply curve for teachers in quality-wage space.
Equation (1) is typically estimated using cross-sectional data
so that bˆ1is identi ed from variation in both outcomes and
salaries across schools (or school districts) at a point in time.
Relying only on cross-sectional variation, however, may
produce misleading estimates. The most commonly acknowl-
edged problem is that, because parents often choose schools
based on their perceived quality, teacher wages are endog-
enous. Parents with a high demand for education quality will
spend more on teachers but may also educate their children
more at home. This type of endogeneity is likely to bias
wage estimates upward.2Researchers have invested a great
deal of energy into overcoming this problem, and we will
return to this issue shortly.
Because this source of endogeniety is likely to bias
estimates of b1upward, it cannot account for the fact that
most studies have not produced evidence that teacher wages
matter. Two additional factors have been largely ignored in
the literature, and they might lead to underestimates of
teacher wage effects. First, like other workers, teachers are
likely to care about both the pecuniary and non-pecuniary
returns to teaching. Holding all else equal, we would expect
to  nd that districts that pay higher wages are able to attract
higher-quality teachers, but all else is not equal. Non-
pecuniary job characteristics such as school safety, the
length of the school year, and the level of parental involve-
ment, also vary across school districts, and this muddies the
degree to which cross-district variation in teacher wages
represents variation in the opportunity cost associated with
teaching in a particular district. In addition, federal and state
governments provide targeted funds for low-income schools
with relatively low-achieving students (see Cullen (1997)
for evidence of this trend in Texas schools), and these funds
may be used to supplement teacher wages. If cross-district
differences in non-pecuniary characteristics produce compen-
sating differentials, then estimates of teacher wage effects
that do not control for these characteristics will suffer from a
negative omitted-variables bias. Antos and Rosen (1975),
Kenny and Denslow (1980), and Levinson (1988) provide
evidence that compensating differentials for teachers may be
substantial, particularly in urban areas. Even the most
comprehensive data sets provide limited information on
non-wage attributes, and, therefore, most cross-sectional
estimates of b1may be subject to this bias.3
The second factor that might lead to underestimates of
teacher wage effects is that existing analyses rarely account
for teachers’ alternative wage opportunities. If school dis-
tricts that pay teachers high salaries are located in areas in
which wages paid to other professionals are also relatively
2When schools are locally  nanced, parents can also directly affect
teacher wage levels through their support of local property taxes. This
phenomenon will also lead to estimates of teacher wage effects that are
biased upward.
3The Schools and Staffing Survey contains substantial information on
school characteristics, but it does not contain information on student
outcomes. Also, an exceptional data set based on Texas schools includes
substantial district attribute information as well as student measures. Using
this data set, Ferguson (1991)  nds signi cant and robust teacher wage
high, then the geographic variation in teacher wage levels
that is typically used to identify teacher wage effects may not
accurately re ect geographic variation in the opportunity
cost associated with choosing to teach. Many estimates of
school production functions are based on cross-sectional
data from a single state and will inherently control for
alternative labor market opportunities if a state comprises
one labor market.4But, if a state has multiple markets or if
researchers use data gathered from multiple states, then
studies should also address the possibility that alternative
job opportunities vary across these markets.5The teacher
wage variables that have been used in multiple-state studies
are not typically measured relative to other workers’ wages,
and therefore may be unreliable indicators of the true
variation in the opportunity cost of teaching. (See Ehrenberg
and Brewer (1994), Jencks and Brown (1975), and Ribich
and Murphy (1975) as examples.)6As a result, estimates of
b1will be biased.
Figure 1 illustrates how failure to account for these factors
compromises our ability to estimate the magnitude of
teacher wage effects. What we wish to estimate is b1, the
slope of the supply curve in quality-wage space, but
variation in non-wage attributes and non-teaching opportuni-
ties across school districts implies that different districts face
different supply curves. Because data from a cross section of
school districts provides only one observation point on each
supply curve, the best- t regression line through these
observations may be substantially different from the true
The purpose of this study is to control for variation in
non-pecuniary attributes and alternative wage opportunities
so that the relationship between teacher wages and student
outcomes can be identi ed by variation in demand along a
single supply curve. We do this by using panel data to
control for cross-sectional differences in non-wage character-
istics, and by replacing teacher wages with the wages of
teachers relative to the wages of other college-educated
workers in the surrounding area. Although the endogeneity
of teacher wages is not the focus of our study, we will also
address this estimation problem by applying a two-staged,
least-squares procedure using a novel instrument, which can
be exploited only because our wage measures take alterna-
tive labor market opportunities into account.
III. Accounting for Non -Pecuniar y Job At tributes
One way of controlling for cross-sectional differences in
non-pecuniary attributes is to make use of variation across
multiple dimensions. Panel data allow us to include district-
or state-level  xed effects, which capture everything, includ-
ing non-wage characteristics, that are constant over time. A
number of recent studies (Hoxby, 1996; Heckman, Layne-
Farrar, & Todd, 1995; Card & Krueger, 1992; Andrews,
Fayissa, & Tate, 1991) have made use of panel data to
identify the effect of wages on student outcomes, and all
produce estimates that are positive and statistically signi -
None of these studies fully address the issues raised in
section II, however, and so it would be premature to
generalize their results. For example, Hoxby uses real
average teacher salaries rather than relative salaries and,
thus, does not control for changes in alternative job opportu-
nities that are not correlated with district-speci c trends,
such as those produced by local economic shocks.7The
studies by Andrews et al. and Card and Krueger do use
relative wage measures, but the Andrews et al. study is based
on data from a single state and the Card and Krueger study
focuses on birth cohorts from the 1920s, 1930s, and 1940s,
so their results may not be applicable to the current U.S.
population. Additionally, the Card and Krueger study, which
uses state-level data, includes only a few state-speci c,
time-varying characteristics. Two characteristics that are
omitted from their regressions but that are correlated with
both teacher wages and student outcomes are the poverty
rate and the fraction of the state’s population who are
immigrants. Several researchers have suggested that Card
and Krueger’s results are driven by omitted-variables bias
4See Beiker and Anschel (1973), Borland and Howsen (1992), Cohn
(1968), Deller and Rudnicki (1993), Dolan and Schmidt (1987), Dynarski,
Schwab, and Zampelli (1989), Ferguson (1991), Fowler and Walberg
(1991), Keisling (1967), Raymond (1968), Sander (1993), Sander and
Krautmann (1991), Sebold and Dato (1981), and Stern, 1989.
5See Akin and Gar nkel (1977), Altonji (1988), Betts (1995), Dynarski
(1987), Ehrenberg and Brewer (1994), Grogger (1996), Jencks and Brown
(1975), Johnson and Stafford (1973), Morgenstern (1973), Perl (1973),
Ribich and Murphy (1975), and Wachtel (1976). While a number of these
papers (Akin and Gar nkel, Dynarski, Johnson and Stafford, Morgenstern,
and Wachtel) use data over multiple years, they do not include state
controls in their analyses and are thus largely identifying using cross-state
6Expenditure studies also need to adjust for alternative labor markets
because wages make up such a large portion of operating costs.
7The focus of Hoxby’s paper is somewhat different from our own.
Hoxby’s analysis centers on the effect of teachers’ unionization on school
inputs and student performance.
which may be affected by their use of state-level data. Betts
(1995), Grogger (1996), Hanushek, Rivkin, and Taylor
(1996), and Loeb and Bound (1996) have all shown that
omitted-variables biases may be exacerbated when state-
level data are used instead of district-level data, although, in
theory, aggregation could either lessen or exacerbate this
Although it is encouraging that estimates based on panel
data are statistically signi cant and in the expected direc-
tion, it is unclear whether the difference in results between
these studies and earlier cross-sectional analyses is due to
anomalies associated with the recent studies or to systematic
differences in approach. Our goal is to shed light on these
questions by directly comparing cross-sectional and panel
data estimates and by directly comparing estimates based on
real versus relative wage measures. We also consider the
possibility that Card and Krueger’s results are driven by
aggregation biases by applying an IV procedure.
IV. Wa ge Tr end s: A De scri ptive An alysis
In order to illustrate why it may be important to include
alternative wage opportunities when estimating teacher
wage effects, we begin by looking at national wage trends
among teachers and non-teachers. We base our descriptive
analysis on a sample of women from the 1964–1995 March
Current Population Surveys (CPS)  les who had completed
sixteen or more years of education8and had worked full
time9during the previous year. Figure 2 plots real annual
earnings and  gure 3 plots weekly wages for female teachers
and non-teachers from 1963 through 1994. We focus on
women here because throughout this period, approximately
70% of elementary and secondary school teachers were
women. Weekly wages are calculated in the usual way, by
dividing annual wage and salary income by the number of
weeks worked.10,11
Both teachers’ and non-teachers’ wages exhibit a down-
ward trend during the 1970s, followed by increases in the
1980s. Throughout these years, wages for teachers remain
above the average wage of non-teachers. However, the
premium associated with teaching decreases substantially
over time. At the beginning of the period, the average
weekly teacher wage was $610 (in 1994 dollars) and the
average weekly wage of non-teachers was $500. Thirty
years later, wages for the two groups are virtually the
Trends in the education and experience of teachers
relative to other college graduates exacerbate the relative
decline in teacher wages. Figures 4 and 5 depict the change
in potential work experience13 and in the percentage of
workers with advanced degrees. Beginning in the early
1970s, both the proportion of teachers with advanced
degrees and teachers’ average experience levels began to
increase at a faster rate than comparable measures for
non-teachers. In 1963, for example, the fraction of teachers
with advanced degrees was below that for non-teachers; by
1994, the proportion of teachers with advanced degrees was
20% higher than the proportion of non-teachers with ad-
vanced degrees.
Even a cursory analysis of these  gures suggests that,
over time, real teacher wage levels have exhibited substan-
tively different trends from the ratio of teacher wages to
non-teacher wages. The diagrams indicate that, although the
8Beginning in 1992, the focus of the education question in the CPS
changed from years of education to degree receipt. Our sample of women
from 1992 forward, therefore, includes only women who indicated that
they had graduated from college.
9The women in our sample may have worked either part of the year or
for the full year.
10 Prior to 1975, the weeks-worked variable was clustered. We use the
average weeks worked for respondents in each cluster over the years with
complete data as our estimate for respondents in the years with clustered
data. We do this separately for teachers and non-teachers.
11 Teachers’ wages and salaries include income from non-teaching jobs
as well.
12 Female teachers’ annual earnings in 1963 were $23,415 (1994 dollars),
whereas female college graduates in other professions had annual earnings
of $19,942. Thirty years later, annual earnings of non-teachers had
surpassed those of teachers: $33,994 to $32,369.
13 Potential experience is de ned as age minus years of education minus
real wages of teachers grew substantially during the period,
the actual opportunity cost associated with teaching (in
terms of the foregone wage) increased. This provides
evidence that using real wage levels in studies of school
input effects is likely to lead to inaccurate estimates of the
true effect of wages on teacher quality and student outcomes.
V. E m pir ica l Ap pr oa ch
Essentially, our goal is to ascertain the slope of the supply
curve for teachers in quality-wage space. The slope of the
supply curve tells us the extent to which districts can
improve student outcomes (through improving the quality of
their teachers) by raising wages. Because real wage varia-
tion across school districts re ects variation in both the
supply and demand for teachers, estimates that rely on
cross-sectional data or that fail to account for alternative
wage opportunities are likely to be misleading.
A. Basic Speci cat ion
Our analysis is based on the following empirical model:
Ys(t110) 5 b 0(t110 ) 1 b 1Wst 1Xs(t110)b21Zstb3
1 h s1µsT1 e s(t110)
where Ys(t110) is a measure of student outcomes in state sat
time (t110),
Wst is the log of the wage for teachers in state sat time t,
Xs(t110) is a vector of control variables speci c to state sat
time (t110),
Zst is a vector of control variables speci c to state sat time
t, and
the error term has three components: a state-speci c,
time-constant component, hs; a state-speci c, constant-time-
trend component, µs(Tidenti es time); and a state-speci c,
time varying component, es(t110).
We regress student outcomes on teacher wages ten years
earlier because it takes time for wage changes to lead to
higher average teacher quality. Even if the quality of new
district hires is very responsive to wage changes, tenured
teachers who entered teaching under a different wage regime
will have little incentive to leave teaching when wages are
increased, and this will result in slow turnover. We also use
ten-year wage lags because the effects of teacher quality
may be greater for students at younger ages (Keisling,
Our estimates are based on state-level data. Individual-,
classroom-, or school-level data may be preferable to
more-aggregate data when school inputs other than teacher
wages are of interest because micro data can provide
more-accurate information than aggregate data on the re-
sources that are available to a particular student. For
example, the classroom-level student/teacher ratio is a more
accurate re ection of the resources available to a given
student than is the district or state average of this variable.
Wages differ from other school inputs, however, because
wage scales are set at the district level and, thus, exhibit no
independent variation at the individual, classroom, or school
level. Within-district analyses of teacher wage effects will
capture only differences in teacher experience and educa-
The school district might, therefore, appear to be the
logical level of aggregation for our analysis. We choose to
use state-level data instead, because very little information
on either district-level teacher quality or district-level stu-
dent outcomes is available for the nation as a whole. The
measures that are available are unreliable. For example,
district-level dropout rates can be estimated for a particular
age group using census data, but, because many dropouts
switch district of residence after dropping out, this measure
is likely to be inaccurate. In addition, district-level data on
teacher wages are available nationally for only independent
school districts, which eliminates all districts in Maryland,
North Carolina, Tennessee, and Virginia, as well as many
districts in other states. The data that are available for
dependent districts is of questionable quality.14 Because of
these problems, we choose to use data at the state level. One
advantage of state-level data is that it may help reduce the
endogeneity problems mentioned earlier if intrastate loca-
tion decisions are more affected by school quality than are
14 Sheila Murray has done extensive work in this area.
interstate location decisions (an assumption that seems
reasonable given that roughly three-quarters of young adults
live in the same state in which they grew up).15
As mentioned in section III, however, using more-
aggregate data has a potential drawback. If the true model
includes an unobserved state component that is correlated
with teacher wages, then failure to include this component in
the regression analysis will lead to coefficient estimates on
teacher wages that are biased.16 Empirical estimates suggest
that aggregation magni es this bias. In addition to including
numerous time-varying, state-speci c control variables, we
address this potential problem by  rst-differencing equation
(7), which eliminates static unobserved state characteristics,
and by including time and state dummies, which capture
time-speci c factors and state-speci c trends. These con-
trols alone may not be adequate, so we will also use a
two-staged, least-squares analysis. Finally, we supplement
our main analysis with an analysis based on district-level
data from California, to further demonstrate that our results
are not driven by the use of state-level data.
B. Non-pecuniary Attributes
We control directly for constant non-pecuniary attribute
differences across states by  rst-differencing equation (2):
Ys(t110) 2Yst 5(b0(t110) 2b0t)1 b 1(Wst 2Ws(t210))
1(Xs(t110) 2Xst)b2
1(Zst 2Zs(t210))b3
1µs1(es(t110) 2est ).
We control for state-speci c time trends (including non-
pecuniary attributes that change at a constant rate) by
including dummy variables for each state. We also include a
number of control variables that vary across states and over
time to help adjust for changes in job attributes that are not
correlated with the time trends. If these control variables
sufficiently capture variation in non-pecuniary attributes,
then we will be able to identify the relationship between
teacher wages and teacher quality by using (unobserved)
variation in demand to trace out the supply curve in
quality-wage space.
C. Alternative Opportunities
We incorporate alternative labor market opportunities into
our empirical model by including relative wage measures.
Although some studies use relative wages to more accu-
rately re ect the opportunity cost associated with teaching,
we have found virtually nothing in the literature that
discusses the appropriate means for constructing these
measures.17 To be useful, relative wage measures must be
based on an appropriate comparison group. Three factors are
particularly important to consider: the contribution of non-
pecuniary job attributes to workers’ utility, the effect of
experience and education on individual productivity, and the
extent of gender differentiation in the labor market.
If all workers care substantially more about wages than
they do about other job attributes, an individual’s rank in the
distribution of wages and in the distribution of productivity
will be identical. We could then measure changes in teacher
quality using changes in the average rank of teacher wages
in the total wage distribution. Because non-wage attributes
are likely to in uence job choice, however, the relationship
between skill and wages in a cross section may be quite
weak and, therefore, teachers’ rank is likely to be an
uninformative measure of quality. But, even if no relation-
ship exists between wages and quality in a cross section, as
long as job attributes remain relatively constant, jobs with
faster-growing wages will attract increasingly higher-quality
workers. We, therefore, use changes in the ratio of average
teacher wages to average non-teacher wages for college
graduates as our relative wage measure. This is not a perfect
measure, because job attributes are likely to change over
time and because the quality of the pool of college graduates
may differ both across labor markets and over time. We
attempt to control for changes in attributes both implicitly,
through the inclusion of state time trends, and explicitly,
through the inclusion of additional variables.18
The second factor to consider is the effect of experience
and education. If the only characteristic that the market
rewards is skill (which may or may not be increased through
education or experience), simple wage comparisons across
groups of workers will provide us with information about
differences in skill across groups. Given that teacher wage
scales are based on education and experience independent of
15 This fraction was calculated using PSID data that were compiled for
another project. The young adults were between the ages of thirty and forty
in 1992, and their state of residence in 1992 was compared to their state of
residence in 1968.
16 If most of the variation in the omitted variable is within states, then
aggregating is likely to reduce the bias due to the variable’s omission, but,
if most of the variation in the omitted variable is between states, then the
aggregation will aggravate the bias.
17 Three recent papers use different measures of teachers’ relative wages
to document changes in the opportunity cost that is associated with
becoming a teacher. Flyer and Rosen (1994) use CPS data from 1967–1980
to calculate the earnings of teachers relative to all college graduates. They
 nd that relative teacher wages increased during the period, but that this
was due to increases in teacher experience and education. When they
impute the expected wage for teachers holding sex, education, race,
metropolitan status, and experience constant, they  nd that teacher relative
wages fell over time, especially during the late 1970s and early 1980s.
Ballou and Podgursky (1997) use the ratio of average teacher pay for both
men and women to a gender-weighted average of the earnings of all
college-educated workers, and  nd that in most states relative teacher
wages rose by more than 10%. Finally, Hanushek and Rivkin (1997)
estimate opportunity costs as the proportion of non-teachers with earnings
less than average teacher earnings, and  nd that the percentage of women
college graduates earning less than teachers fell from a high of 68.7% in
1940 to a low of 45.3% in 1990, with most of the decline occurring before
1970. Although some of this change was due to an increase in the age and
education of non-teachers, the majority was due to pure wage declines for
18 The relative wage will not be a good measure of teacher quality if the
wages of non-teachers are changing over time as a result of changes in the
average quality of non-teachers. We would like to investigate this
possibility in future work.
teacher skill, however, wage comparisons that ignore educa-
tion and experience will provide misleading information
about the true opportunity cost of teaching. School input
studies have not typically adjusted relative wage measures to
account for these factors, but  gures 4 and 5 suggest that
they may be important.19 We create both simple relative
wage measures and relative wage measures that adjust for
education and experience levels.20
We also consider the importance of gender in the labor
market for teachers. Because women have comprised the
substantial majority of the teaching force throughout the
period covered by this study,21 and because the labor market
for college graduates was characterized by institutionalized
gender differentiation, our relative wage measures are
constructed for women only.
VI. E stima tion of Teacher Wage Effect s
A. Data
Our regression analysis utilizes a state-level panel data set
that we create from the 1960–1990 Public Use Microdata
Samples (PUMS). Unlike the CPS, the PUMS data provide
us with adequate sample sizes at the state level. Our  rst
dependent variable is the log of the state high-school
dropout rate.22 We de ne the dropout rate as the percentage
of all 16–19 years olds living in the state who are not
currently attending high school and do not have a high-
school diploma.23 Because this measure surely includes
individuals who conducted the bulk of their education in
another state, we create a second measure that includes only
those residents who were born in the state in which they are
observed at the time of the survey. The disadvantage of this
latter measure is that we lose individuals who may have
migrated to the state prior to obtaining most of their
We also run regressions using the college attendance rate
as our dependent variable. We recognize that, relative to
dropout rates, the college attendance rate is more likely to be
affected by the migration of individuals across states, but we
want to demonstrate that our results are not an artifact of one
particular measure of student outcomes. We de ne the
college attendance rate as the percentage of 19–20 year olds
who have either attended thirteen or more years of school
(census years prior to 1990) or who have obtained some
schooling beyond completing their high-school diploma
(1990 census). Again, we create this variable both for all
residents and for only those born in-state.
We would like to be able to look at student test scores in
addition to measures of educational attainment, but consis-
tent achievement measures are not available nationally over
this period.24 We do know that, across states, the correlation
between 1990 high-school dropout rates and 1992 National
Assessment of Educational Progress average math scores is
approximately 0.8. Even if no correlation existed between
educational attainment and test scores, the well-established
relationship between individuals’ educational attainment
and future earnings justi es an interest in the outcomes used
We use three different measures of teacher wages in our
analyses: the log of the real teacher wage, the unadjusted
relative wage (which is simply the coefficient on a teacher
dummy variable in a univariate log wage equation), and the
adjusted relative wage (which is created in the same way as
the unadjusted relative wage, except that the wage equation
includes a binary variable for whether the worker has an
advanced degree, and measures of potential experience
(de ned as age minus years of education minus six) and
potential experience squared).25 Our wage sample is re-
stricted to include workers ages 20–64 who indicated that
they had completed college and were working at least 26
19 In fact, determining whether to adjust for education and experience is
complicated by the possibility that these characteristics may increase
productivity in the market for alternative occupations but not in the teacher
labor market. If, for example, the type of education and experience that
teachers have does not contribute to their productivity in the non-teacher
labor market, but the type of education and experience that non-teachers
have does contribute to their productivity in the non-teacher labor market,
then the correct comparison would be between the adjusted teacher wage
and the unadjusted non-teacher wage (essentially comparing teachers to
other workers with no experience or additional education).
20 The best experience measure that we have is potential experience,
which will be a noisy measure of teacher tenure. As a result, the coefficient
estimates on this variable are likely to be biased downward.
21 The fraction of the teaching force that are women has remained fairly
constant over time: the fraction was 68.7% in 1961, and 72.1% in 1991.
22 We have chosen to use logs because the distributions of our variables
in level form are skewed. Moreover, in our context, the logarithmic
speci cation, which relates percentage changes, may be preferred to one
that relates absolute changes. For example, it is probably easier for
policymakers to lower the dropout rate from 20% to 19% than from 2% to
1%. Our results are similar whether we use logs or levels, however: using
levels, we  nd that a 50% increase in teacher wages is associated with a
decrease in the dropout rate of approximately 1.5 percentage points and an
increase in the college enrollment rate of 4.3 percentage points.
23 The education questions in 1960–1980 census surveys focus on years
of education, rather than degree receipt. We classify respondents to these
surveys as high-school graduates if they indicated that they had completed
twelve years of education. If an individual attended high school through
the twelfth year, but did not complete that grade and is not currently in
school, then he or she is classi ed as a dropout. In the 1990 census,
individuals are asked speci cally about whether they have graduated from
high school.
24 One referee has suggested that we try using SAT test scores as a
dependent variable. SAT scores are available by state beginning in 1972
and can be adjusted for cross-state differences in the fraction of students
who take the SAT (thereby implicitly controlling for the fact that the
average SAT score re ects the inclusion of students from a lower part of
the ability distribution when more students take the test). In a single year,
the adjusted SAT score has been shown to be positively correlated with a
state’s average NAEP test score, and it is also positively correlated with
our dropout measures. Changes in SAT scores are not positively correlated
with changes in the dropout rate, however. (We do not have state-level
NAEP scores over multiple years, so we cannot examine this correlation.)
It is, therefore, no surprise that changes in SAT scores are unrelated to
changes in relative teacher wages. We suspect that the adjustment simply
does not work as well over time as it does in a cross section.
25 Because the educational attainment of teachers is more likely to be
endogenous than our measure of experience, we also created a relative
wage measure adjusted only by experience and experience squared. The
results of analyses using this measure are similar to those presented below
for the unadjusted and adjusted relative wage.
weeks during the relevant year.26,27 We run separate regres-
sions for each state/year cell for 1960 through 1980, and use
the estimated coefficient on the teacher dummy as our
estimate of relative wages for a given state in a particular
year. This provides us with 150 observations for each
relative wage variable.28
Our time-varying controls for attribute differences include
state demographic variables such as the state unemployment
rate, state median income, the percentage of individuals
below the poverty line, and the percentage of individuals
who are immigrants. The vector also includes variables more
directly related to the market for teachers: the number of
teachers in the state, school enrollment, the percentage of the
state population that lives in urban areas, and three variables
that characterize the degree to which teachers are union-
ized.29,3 0 In addition, we include the demographic variables
measured contemporaneously with the dropout rate so we
can get a clean estimate of the effect of wages on that portion
of the dropout rate that is not in uenced by contemporane-
ous economic conditions.
Table 1 provides the means and standard deviations of the
variables used in the regression analysis. The dropout rate
decreased steadily over our period, as did its variance across
states. Using our  rst dropout rate measure, the standard
deviation across states in 1959 is 0.061. By 1989, the
standard deviation had dropped to 0.025. Over the same
period, real teacher wages increased by approximately 20%,
but teacher wages relative to the wages of other college
graduates fell by approximately 12%.
B. Results
Cross-sectional Analysis: In order to place our results in
the context of existing studies, we begin by looking at
estimates based on cross-sectional regressions. Table 2
displays the coefficient estimates for single-year regressions
(1969, 1979, and 1989) of educational attainment on the real
teacher wage ten years earlier.31 Model (I) includes no
additional covariates, while model (II) includes all of the
control variables listed above. The estimates produced by
these regressions are similar to those summarized by Han-
ushek (1986, 1997): in the univariate regression, all but two
of the twelve coefficient estimates are positive and most are
signi cant, but—once additional variables are introduced
into the model—there is no evidence that teacher wages
affect student outcomes. Not a single coefficient is both in
the expected direction and statistically distinguishable from
zero. This is consistent with the literature to date, which
 nds scant evidence of teacher wage effects once family
background characteristics are controlled for. Thus far, most
studies of school production functions have focused on
adjusting for the bias that arises from the omission of these
variables, rather than the bias that may arise from improp-
erly using cross-sectional variation in teacher wages to
proxy for variation in the opportunity cost of teaching.
Table 3 displays the cross-sectional results using our two
relative wage measures. Again, the univariate regression
produces estimated coefficients that are all in the expected
direction, and, again, these estimates are affected by the
addition of controls. They are not affected to the same
26 We classify as college graduates in the 1960–1980 census surveys
those who have completed sixteen years of education. In the 1990 census,
respondents identify themselves as recipients of bachelor’s degrees.
27 This is a different comparison group than the one used in our CPS
analysis because, across surveys, PUMS does not have consistent mea-
sures of hours worked.
28 Washington, D.C., is included, but Alaska is not.
29 The unemployment rate, median income, percentage poor, and percent-
age urban variables are from Statistical Abstracts of the United States. The
number of teachers and students are from Digest of Education Statistics.
We create our immigrant variable from census data. The data on unions are
from the NBER data set created by Freeman and Valletta (1988). The three
measures we use are a dummy variable for whether the state allows
collective bargaining, a dummy variable for whether the state permits
agency shops, and a dummy variable for whether strikes are permitted.
30 We have also run all of our regressions including variables that
characterize the racial composition in each state (measured contemporane-
ously both with the dependent variable and with a ten-year lag). The
inclusion of these variables had virtually no effect on our results, nor did
the variables exhibit an independent effect on any of the dependent
31 The weighting technique is similar to that described below for the
difference estimations. In this case, our estimates of the error term come
from an OLS regression of the inverse of the sample size on the squared
residual. There is little difference between the weighted and unweighted
1959 19 69 1979 1989
Log real wage 6.122
Unadjust relative wage 0.305
Adjusted relative wage 0.294
Dropout rate (all residents) 0.209
Dropout rate (those born in-state) 0.200
College enrol lment rate (all resi-
College enrol lment rate (those born
Unemployment rate 5.194
Log median inco me 16.920
Percentage poo r 23.950
(10.956 )
Percentage immigrants 0.039
Log teacher number 9.718
Log enrollment 12.982
Percentage urban 62.994
(15.627 )
(15.136 )
Collective bargain ing 0.041
Agency shop 0.000
Strike 0.00 0
* Note: The numb ers in parentheses are s tandard deviations.
degree as the real wage estimates, however, and most
estimates remain in the expected direction. Consider the
adjusted relative wage, for example: all but one of twelve
point estimates produced by model (II) suggest that the wage
has a positive effect on student outcomes. None of the 1969
or 1979 estimates are signi cant at conventional levels,
Finally, the cross-sectional results show evidence of a
time trend. The magnitude of the estimated effects is quite a
bit larger for 1989 than for the earlier years. The estimates
are in the expected direction and signi cant at conventional
levels. Most previous studies of teacher wage effects have
used data from the 1970s and early 1980s, however, and our
results for those years are consistent with the failure of
earlier research to nd robust evidence that teacher wages
matter. It is puzzling that the magnitude and signi cance of
our estimated teacher wage coefficients change so much
between 1979 and 1989, but we do not believe that this
change is driving the  rst-differences estimates that we
present below, because, when we run our  rst-differences
regression using student outcomes from 1969–1979 only
(wage measures from 1959–1969)our estimates are not
statistically or substantively different from those produced
using the full sample.
Differenced Analysis—Dropout Rates: Next, consider the
results produced by the  rst-differences analysis. Table 4
presents the estimated effect of teacher wages on our  rst
de nition of the dropout rate. Model (I) includes only year
dummies, model (II) includes year and state dummies, and
model (III) adds the time-varying controls. We weight these
regressions to account for heteroskedasticity in our esti-
mates of the dropout rate.32
In all three panels of table 4, the estimated coefficients on
both the unadjusted and the adjusted relative wage (columns
(2) and (3)) are negative and statistically signi cant. The
results from the most inclusive model indicate that raising
the wage by 10% would decrease the dropout rate by 3%. If
we compare the results of model (I) to the  rst panel in tables
2 and 3, we can see that differencing reduces the estimated
wage effect, indicating that part of the wage effect found in
the univariate cross-sectional analysis may be attributed to
state- xed effects. One possible explanation for this result is
that states with preferable attributes also have higher wages.
An alternative is that an underlying state characteristic, such
32 Because we use an estimate of the dropout rate (or college attendance
rate) as our dependent variable, the actual equation that we estimate is
ˆs(t110) 2Y
ˆs(t)5(b0(t110) 2b0(t))1 b 1(Ws(t)2Ws(t210))1(Xs(t110) 2
Xs(t))b21(Zs(t)2Zs(t210))b31µs1(es(t110) 2est )1(Ãs(t110) 2Ãst),
where Y
ˆ5Y1 Ã . Differences in sample sizes across states and over
time suggest that Ãwill be heteroskedastic. We, therefore, run a weighted
regression, using estimates of the variance of [(es(t110) 2est )1
(Ãs(t110) 2Ãst )]21as our weights. Our estimates of the variance of
[(es(t110) 2est )1 Ã s(t110) 2Ãst )]21are derived in two steps. First, we
estimate the equation above using OLS. We then use the squared residuals
from this regression as the dependent variable in a second OLS regression
that includes [(1/Ns(t110))1(1/Nst)] (the sum of the inverse of the sample
sizes in each year) as the only independent variable. The estimated
coefficient on this variable, multiplied by the variable itself, provides us
with an estimate of the variance of Ãs(t110) 2Ãst, while the estimated
intercept provides us with an estimate of the variance of es(t110) 2est.
Differences between the weighted and unweighted estimates are minor.
Dropout Rate
Dropout Rate
(Born In-State) College Enrollment
College Enro llment
(Born In-State)
Model (I) Model (II) Model (I) Model (II) Model (I) Model ( II) Model (I) Model (II)
1969 20.6 56 20.163 20.938 20.125 0.473 0.175 0.614 0.152
(0.299) (0 .298) (0.322) (0.255) (0.144) (0.128) (0.211) (0.183)
1979 20.5 86 0.723 20.56 1 1.138 0.280 20.2 25 0.121 20.303
(0.281) (0 .408) (0.313) (0.413) (0.145) (0.207) (0.189) (0.186)
1989 0.558 20.3 91 0.323 20.570 0.026 0.237 0.054 0.379
(0.281) (0 .422) (0.335) (0.461) (0.130) (0.208) (0.246) (0.214)
Note: The number s in parentheses are White’s stand ard errors. Model (I) has n o controls. Model (II) includ es all time-variant, state-s peci c controls. Sample size is  fty.
Model (I) Model (II)
Dropout rate
1969 20.61 6 20.729 0.207 20.041
(0.365) (0.2 19) (0.129) (0.188)
1979 20.44 5 20.682 20.456 20.496
(0.383) (0.3 39) (0.264) (0.231)
1989 21.18 7 21.387 20.951 21.078
(0.398) (0.3 55) (0.351) (0.336)
Dropout rate (born
1969 20.80 5 20.831 0.167 20.011
(0.379) (0.2 70) (0.132) (0.174)
1979 20.38 7 20.611 20.314 20.363
(0.407) (0.3 73) (0.293) (0.259)
1989 21.51 6 21.631 21.187 21.303
(0.455) (0.3 99) (0.381) (0.372)
College enroll.
1969 0.412 0.387 20.016 0.067
(0.147) (0.0 97) (0.078) (0.091)
1979 0.104 0.172 0 .064 0.054
(0.175) (0.1 49) (0.139) (0.120)
1989 0.210 0.2 33 0.411 0.433
(0.166) (0.1 77) (0.174) (0.174)
College enroll. (b orn
1969 0.403 0.339 20.158 20.073
(0.205) (0.1 70) (0.119) (0.108)
1979 20.00 9 0.042 0.129 0.081
(0.193) (0.1 80) (0.167) (0.146)
1989 0.495 0.500 0 .593 0.614
(0.205) (0.2 05) (0.184) (0.187)
Note: The nu mbers in parentheses are Wh ite’s standard errors . Model (I) has no con trols. Model (I I)
includes tim e-variant, state-sp eci c controls. Sample s ize is f ty.
as interest in education, increases teacher wages but also
increases student outcomes. A comparison across the three
tables also shows that differencing reduces the standard-
error estimates. This reduction could result from non-
pecuniary attribute differences across states which make
cross-sectional wage variation a noisy measure of the total
utility associated with choosing to teach.
Moving across table 4 from left to right, we see that
controlling for state-speci c time trends raises the point
estimates slightly. States that raise wages may be compensat-
ing for a decline in the attractiveness of teaching. Con-
versely, the inclusion of the time-varying controls tends to
decrease the estimated effect of teacher wages and to reduce
the corresponding standard-error estimates. This may occur
because the inclusion of time-varying controls more com-
pletely adjusts for non-pecuniary attribute differences across
states, making our wage measures in model (III) better
estimates of the true opportunity cost of teaching. The
results from model (III) suggest that longitudinal studies that
omit time-varying factors may overestimate the impact of
teacher wages.
The estimated coefficients on changes in the unemploy-
ment rate, immigration levels, and poverty levels are all
statistically signi cant at conventional levels, and the R2
nearly doubles when these variables are included. We  nd
that the signs on the unemployment rate and immigration
coefficients differ depending on whether they are contempo-
raneous with teacher wages or with student dropout rates.
The estimates suggest that an increase in the contemporane-
ous unemployment rate of one percentage point will reduce
dropout rates by nearly 5%, but that an increase in the
unemployment rate ten years earlier of one percentage point
will increase dropout rates by 3%. One interpretation of
these results is that students are more likely to continue their
schooling when alternative labor market opportunities are
scarce, but that growing up during a recession has a negative
impact on educational attainment. Increases in the percent-
age poor (both lagged and contemporaneous) are associated
Model (I) Model (II) Model (III)
Relative Real
Relative Real
DRelative wage 20.565 20.351 20.316 20.513 20.465 20.374 20.07 3 20.256 20.301
(t 210) 2(t) (0.209) (0 .157) (0.131) (0.240) (0.131) (0 .106) (0.178) (0.073) (0.061)
DUnemployment 20. 041 20.041 20.046
(t) 2(t 110) (0.014) (0 .013) (0.012)
DImmigrants 6.637 7.1 20 6.629
(t) 2(t 110) (2.888) (2 .816) (2.764)
DMedian income 0.150 0.077 20.045
(t) 2(t 110) (0.321) (0 .259) (0.253)
DPercentage poo r 0.023 0.017 0.014
(t) 2(t 110) (0.008) (0 .007) (0.007)
DUnemployment 0.031 0.031 0.029
(t 210) 2(t) (0.011) (0.011) (0.011)
DPercentage urban 0.009 0.005 0.007
(t 210) 2(t) (0.010) (0.011) (0.010)
DImmigrants 21.69 3 21.895 21.904
(t 210) 2(t) (1.009) (0.911) (0.925)
DMedian income 20.787 20.748 20.799
(t 210) 2(t) (0.332) (0.327) (0.331)
DPercentage poo r 0.013 0.010 0.010
(t 210) 2(t) (0.005) (0.004) (0.004)
DTeachers 20.006 20.072 20.084
(t 210) 2(t) (0.187) (0.181) (0.174)
DEnrollment 20. 290 20.106 20.119
(t 210) 2(t) (0.174) (0.164) (0.151)
DCollective barg. 0.032 0.034 0.025
(t 210) 2(t) (0.025) (0.024) (0.023)
DAgency shop 20.006 20.023 20.046
(t 210) 2(t) (0.050) (0.049) (0.049)
DAllowed strikes 0.045 0.025 0.008
(t 210) 2(t) (0.059) (0.055) (0.056)
1969–79 0.342 0 .1763 0.2032 0.332 0.177 0.208 0. 881 0.760 0.805
(0.067) (0 .034) (0.034) (0.072) (0.029) (0 .029) (0.093) (0.081) (0.075)
Intercept 20.295 20 .248 20.265 20.357 20.308 20.334 20.271 20.252 20.260
(0.028) (0 .019) (0.020) (0.051) (0.059) (0 .065) (0.052) (0.044) (0.043)
State controls? no no n o yes yes yes yes y es yes
R-squared 0.299 0.28 9 0.287 0.448 0.480 0.466 0.843 0.857 0.870
Note: The numb ers in parentheses are Wh ite’s standard errors. M odel (I) includes a y ear dummy only. Model (II) add s state dummies. M odel (III) adds time-var iant, state-speci c co ntrols. N 5100.
with higher dropout rates. The coefficient estimates on
school inputs other than the relative teacher wage are
typically insigni cant.
The importance of controlling for alternative labor market
opportunities, even in the differenced analysis, is under-
scored when we compare the results using our relative wage
measures to the results based on real wage levels. While the
coefficient on the real wage is signi cant and in the expected
direction in the univariate regressions, this pattern does not
hold up to the inclusion of time-varying controls. In contrast,
the relative wage measures, especially the adjusted relative
wage, are only mildly affected by the inclusion of these
It is useful to know whether our relative wage results are
driven by changes in the teacher wage or in the non-teacher
wage. A simple way to assess the effects of the two
components of our relative wage measure is to enter them
separately in the regression. When all controls are included,
the magnitude of the point estimates for teacher and
non-teacher wages are strikingly similar but with opposite
signs.33 This result provides evidence both that the teaching
wage and the wage of alternative occupations affect stu-
dents’ attainment and that the use of relative wage measures
is appropriate.
Other Outcomes: The results corresponding to our three
additional de nitions of student attainment are presented in
table 5. Much like the estimates in table 4, these results
imply that a 10% increase in wages would reduce dropout
rates for natives of the state by approximately 3%. Our
estimates suggest that this improvement in teacher compen-
sation would increase college attendance by 1.6%. Moving
across the panels of table 5, we see patterns that are similar
to those discussed above. Controlling for alternative labor
market opportunities and other factors that are correlated
with teacher wages affects the magnitude and precision of
our estimates.
VII . Sp eci cation Tests
In order to investigate the robustness of our results, we
perform three speci cation tests.
A. Southern States
Because substantial changes in the quality of education
were occurring in the South during the period we analyze,
one possible concern is that our results are driven by the
North/South convergence of both school inputs and student
outcomes. We investigate this possibility in table 6, which
shows the results of estimating our equations using only the
34 northern states. We  nd teacher wage effects that are
similar in magnitude and signi cance to those based on the
full sample.
33 For the dropout rate, the estimated coefficient on the teacher wage is
20.32 while that on the non-teacher wage is 0.48. The standard errors are
0.32 and 0.16, respectively. For the college enrollment outcome, the
corresponding coefficients are 0.25 and 20.20 with standard errors of 0.14
and 0.09.
Student Outco mes
Model (I) Model (II) Model (III)
Relative Real
Relative Real
DDropout rate (born in-state) 20.538 20.185 20.271 20.513 20.437 20.386 0.155 20.1 97 20.282
(0.211) (0. 188) (0.151) (0.233) (0.139) (0.109) (0.209) (0 .103) (0.079)
DCollege enroll. 0.444 0.22 7 0.174 0.469 0.298 0.201 0.1 50 0.164 0.165
(0.114) (0. 075) (0.069) (0.113) (0.070) (0.057) (0.074) (0 .031) (0.027)
DCollege enroll. (born in-state) 0.498 0.238 0.206 0.494 0.338 0.259 0.028 0.155 0.150
(0.150) (0. 088) (0.077) (0.128) (0.085) (0.069) (0.102) (0 .044) (0.038)
Note: The numb ers in parentheses are Wh ite’s standard errors. M odel (I) includes a y ear dummy only. Model (II) add s state dummies. M odel (III) adds time-var iant, state-speci c co ntrols. Sample size is 100 .
Student Outcomes
Model (I) Model (II) M odel (III)
Relative Real
Relative Real
DDropout rate 20.646 20.310 20.283 20.868 20.45 6 20.360 20.357 20.325 20.359
(0.277) (0.176) (0 .137) (0.257) (0.142) (0.105) (0.214) (0.076) (0.050)
DDropout rate (born in-state) 20.371 20.202 20.215 20.678 20.373 20.346 20.186 20.193 20.352
(0.315) (0.197) (0 .169) (0.294) (0.158) (0.113) (0.254) (0.114) (0.074)
DCollege enroll. 0.366 0.186 0 .137 0.524 0.256 0.159 0.241 0.125 0.137
(0.132) (0.077) (0 .070) (0.141) (0.079) (0.064) (0.069) (0.026) (0.019)
DCollege enroll. (born in-state) 0 .232 0.166 0.153 0.375 0.269 0.210 0.196 0.085 0.110
(0.161) (0.081) (0 .068) (0.154) (0.092) (0.071) (0.057) (0.025) (0.025)
Note: The numb ers in parentheses are Wh ite’s standard errors. M odel (I) includes a y ear dummy only. Model (II) add s state dummies. M odel (III) adds time-var iant, state-speci c co ntrols. Sample size is 68.
B. Two-Staged, Least-Squares Analysis
Our biggest concern is that, even though we include
numerous time-varying controls, we may not be adequately
adjusting for all of the factors that are collinear with wages
and that in uence student outcomes. As noted earlier, the
biases resulting from this omission may be aggravated when
more-aggregate data (such as data measured at the state
level) are used. To systematically assess potential endogene-
ity and omitted-variable problems, we apply two-stage least
squares using as our instrument the change in log wages for
non-teaching women college graduates.
This instrument is highly correlated with changes in our
relative wage measure because it is, essentially, the denomi-
nator of our relative wage measure. Although this is a
nontraditional instrument choice, it does allow us to isolate
substantial variation in the wage measure that is not subject
to the endogeneity and omitted variables bias that we are
concerned about. In particular, this instrument is unlikely to
lead to upward-biased wage estimates. Because the non-
teacher wage is negatively correlated with the relative
teacher wage, an upward-biased estimate will result only if
there are omitted variables that are both positively (nega-
tively) correlated with the non-teacher wage and negatively
(positively) correlated with student outcomes. Although it is
not difficult to think of factors that might be positively
correlated with both non-teacher wages and students’ educa-
tional attainment (such as parents’ socioeconomic status), it
is difficult to think of omitted variables that would lead to a
wage estimate that is biased upward. The inclusion of state
time trends as well as median income, the poverty rate, and
the state unemployment rate should remove much of the
correlation between our instrument and the error term, but, if
any omitted variables remain, the IV estimates will be
conservative. Before proceeding with the 2SLS analysis, we
enter the instrument into our differenced equation to check
for correlation with the error term. The estimated coeffi-
cients are never conventionally signi cant, which suggests
that the non-teacher wage of female college graduates is an
exogeneous instrument.34
Table 7 reports the coefficient on the instrument— the real
wage of non-teaching female college graduates—for all
rst-stage regressions. When the wage of non-teachers
increases by 10%, the relative wage of teachers falls by just
under 10%. The partial R2is over 0.2 for both the adjusted
and unadjusted wage. This provides evidence that our
instrument is strongly correlated with our explanatory
variable, and we do not need to be concerned that our IV
estimates will display an inconsistency of the type discussed
by Bound, Jaeger, and Baker (1995).
Table 8 displays the results for the structural equations.
The IV strategy yields point estimates for the full model that
depict a greater effect of wages on student outcomes than
those in tables 4 and 5. The coefficients on adjusted relative
wage, for example, are 20.454 and 20.432 for the dropout
rates, indicating that a 50% increase in wages corresponds to
more than a 20% decrease in the dropout rate. For college
enrollment, a 50% increase in the wage corresponds to
between a 9% and 13% increase in the college enrollment
rate. Although we can not reject the possibility that these
estimates are equal to the estimates in tables 4 and 5, table 8
provides evidence that our earlier estimates are not biased
upward by the use of an endogeneous regressor. In fact, it
may be the case that these biases are in the other direction, as
would be the case if compensating differentials were at
Table 8 also provides real wage estimates using our IV
strategy. These estimates are smaller than those in tables 4
and 5, which is expected, because non-teachers’ real wage
changes are not a good instrument for changes in teachers’
real wages. If districts raise teacher wages more when the
wages of female college graduates increase, the instrument
will actually pick up wage changes that are negatively
associated with changes in the opportunity cost of teaching.
Although the potential endogeneity of teacher wages is
unlikely to carry over to non-teacher wages, it is possible
that, when wages of women college graduates increase,
female high-school students have more of an incentive to
remain in school, which, in turn, reduces dropout rates and
increases college enrollment.35 Because our instrument is
negatively correlated with the relative wage measures, we
would expect the potential bias resulting from this effect to
be towards  nding no impact of teacher wages on student
outcomes. Thus, the true effect of teacher wages on student
outcomes may be greater than our previous point estimates
34 For example, using our  rst dropout measure and the adjusted relative
wage, the coefficient on the non-teacher wage is 20.18 (0.26 standard
error) in model (I), 0.13 (0.36) in model (II), and 0.23 (0.27) in model (III).
35 Recall, however, that, when our instrument was included directly in
our regressions, we found no evidence that it was correlated with the
dependent variable.
Student Ou tcomes
Model (I) Model (II) Model (III)
Relative Real
Relative Real
Coefficient 0.176 20.79 5 20.947 0.164 20.81 4 20.979 0.071 20.9 07 20.988
Standard error (0 .115) (0.149) (0.161) (0.173) (0.221) (0.236) (0.19) (0.239) (0.286)
Partial R-squared 0.013 0.324 0.3 87 0.008 0.243 0.296 0.001 0.217 0.217
Note: The numb ers in parentheses are Wh ite’s standard errors. M odel (I) includes a y ear dummy only. Model (II) add s state dummies. M odel (III) adds time-var iant, state-speci c co ntrols. Sample size is 100 .
In order to investigate this issue, we run our 2SLS
regression using outcome measures constructed for men
only, adding the change in the wages of male college
graduates as a control and using the change in the female
college-graduate wage as the instrument. When we use the
adjusted relative wage measures and include all of our
control variables, we  nd that the estimated effect of teacher
wages on the log of the high-school dropout rate is 20.59
(with a standard-error estimate of 0.19), which suggests that
dropout rates would fall by more than 5% if teacher wages
were increased by 10%. The larger estimate appears to result
in part from the fact that male students are more responsive
to changes in teacher quality; the estimated effect of teacher
wages on male high-school dropout rates is larger for men
than for the sample as a whole (20.42, with a standard-error
estimate of 0.12), even before applying IV.36
C. District-Level Analyses
The 2SLS results provide evidence that our estimates are
not driven by omitted-variables or endogeneity bias. Be-
cause the concern with state-level data is that it exacerbates
these biases, we infer from these results that our use of
state-level data is appropriate. However, as an additional
speci cation check, we run an abbreviated version of our
analysis using district-level data from California. As dis-
cussed in section IV, reliable district-level data are not
available nationally over time, but we were able to obtain
administrative data on teacher wages and high-school drop-
out rates for most of the uni ed districts in California
starting with teacher salary information in 1976 and district
dropout rate data in 1986.37 (These are the earliest years for
which these measures are available.) We merge these data
with 1995 California school district dropout rates taken from
the Common Core of Data to create a two-year panel data set
that includes teacher salary information from 1976 and 1986
together with student dropout rates for 1986 and 1995. One
nice feature of this data set is that it includes information on
both average teacher salaries and the salary typically paid to
teachers with different levels of education and experience.
This data set (like the other less-aggregate data sets we
considered and rejected) is less than ideal for our study for
several reasons. To begin with, the data set goes back to only
1976 and it contains very little information on the types of
time-varying attributes that we included in our state-level
analyses. Because our main results are driven mostly by the
inclusion of state- xed effects and do not hinge on the
inclusion of geographic-speci c time trends or additional
control variables, we believe that these drawbacks are not
serious enough to impede a simple comparison with the
state-level results. In addition, the dropout rates for 1986 are
de ned differently than those from the 1995 Common Core
of Data. Because of this difference, we cannot be sure that
variation in our outcome is driven by district changes rather
than de nitional changes. Finally, it is difficult to  nd an
appropriate measure of a teachers’ alternative wage for
California districts during this period. We average the wages
of female college graduates across the 1970 and 1980
decennial census to produce a relative wage measure for
1976 and, across the 1980 and 1990 decennial census to
produce a relative wage measure for 1986. In addition to the
potential problems that may arise from averaging, the
geographic identi ers differ substantially in the 1970, 1980,
and 1990 PUMS, and we are not able to match precise labor
markets to many of the districts. For districts located in
Santa Barbara, San Diego, Los Angeles, and the San
Francisco Bay area, we use relatively consistent labor
market boundaries over time, but the only way to create
alternative wage measures for districts located in the rest of
California is to use information from all other counties in the
state. This results in a poor matching of teacher salaries with
alternative wage opportunities and thus limits the variation
in our measure of alternative wages.
Estimates of cross-sectional and  rst-difference regres-
sions are shown in tables 9 and 10. In keeping with the
state-level analysis, we de ne the relative wage as the
difference between the log of the teacher wage and the log of
the average female college graduate, non-teacher, wage in
the corresponding labor market. The real wage is measured
36 For dropouts born in-state, the estimated coefficient is 20.79, with a
standard error estimate of 0.27. For the two college enrollment outcomes,
the estimated coefficients are 0.18 and 0.27 with standard-error estimates
of 0.11 and 0.16. Before applying IV, the coefficient estimates are 20.79,
0.17, and 0.15 with standard-error estimates of 0.27, 0.03, and 0.04.
37 These data were generously provided to us by Thomas Downes of
Tufts University. For detailed information on the data, see Downes (1988).
Student Outcomes
Model (I) Model (II) M odel (III)
Relative Real
Relative Real
DDropout rate 1.358 20.301 20 .253 3.125 20. 628 20.523 6 .328 20.494 20.454
(1.820) (0. 280) (0.229) (4.256) (0.319) (0.253) (17.47) (0.218) (0.189)
DDropout rate (born in-state) 0.793 20.176 20.148 2.815 20.566 20.47 1 6.029 20.47 1 20.432
(1.659) (0. 306) (0.250) (3.875) (0.350) (0.265) (16.51) (0.273) (0.236)
DCollege enroll. 20.164 0.036 0.031 20.805 0.162 0.135 22.540 0.1 98 0.182
(0.706) (0.141) (0 .120) (1.292) (0.103) (0.098) (7.335) (0.087) (0.082)
DCollege enroll. (bo rn in-state) 0.052 20.011 20.010 21.168 0.235 0.195 23.642 0.284 0.261
(0.738) (0.167) (0 .140) (1.504) (0.170) (0.136) (9.871) (0.137) (0.133)
Note: The numb ers in parentheses are Wh ite’s standard errors. M odel (I) includes a y ear dummy only. Model (II) add s state dummies. M odel (III) adds time-var iant, state-speci c co ntrols. Sample size is 100 .
both as the log of the wage for a starting teacher (table 9) and
as the log of the average teacher wage in the district (table
10). Unlike in the previous analyses, we use dropout-rate
levels instead of logs as our outcome variable.38 All equa-
tions control for the percentage of students receiving AFDC.39
As in the state-level analyses, we see that cross-sectional
regressions produce estimates that indicate no relationship
between teacher wages and high-school dropout rates. In
fact, districts with higher wages in 1985 appear to have
higher dropout rates ten years later. Once  xed effects are
included and relative teacher wage measures are used,
however, the teacher wage estimates are positive and
statistically signi cant, suggesting that a 10% increase in the
teacher wage will produce a decrease in the dropout rate of
0.5 to 0.8 percentage points (an approximately 10% de-
crease, on average). Our state-level estimates suggest that
the magnitude of these estimates would probably fall
slightly if we were to include additional time-varying
variables in our analysis. These results back up our conclu-
sion that cross-sectional estimates of the effects of teacher
wages on student outcomes have been biased by researchers’
inability to control for  xed effects. Nevertheless, we
emphasize that, because of the datas imperfections, we do
not place con dence in these estimates.
VIII. Conclusions
In this study, we investigate the relationship between
teacher wages and student outcomes. Our results help to
explain why previous studies have failed to produce system-
atic evidence that teacher wages affect student outcomes: the
identi cation of teacher wage effects has been based on
cross-sectional variation that re ects both supply and de-
mand factors. Because alternative labor market opportuni-
ties and other school district characteristics vary across
districts, the supply of teachers in quality-wage space also
varies across districts. Therefore, we cannot hope to accu-
rately identify the relationship between teacher wages and
student outcomes unless we are able to hold the supply curve
xed. Only a regression analysis that controls for other
factors that affect the supply of teachers will produce
policy-relevant elasticity estimates of the effect of teacher
wages on student outcomes.
Of course, as in other studies, we are not able to directly
control for all of the factors that in uence the opportunity
cost associated with choosing to teach. Instead of conduct-
ing a cross-sectional analysis (for which we would have
needed to control for all factors affecting the supply
decision), we create a state-level panel data set and implic-
itly control for static differences in non-pecuniary attributes
by employing a  rst-difference estimation strategy. We also
account for variation in the opportunity cost of teaching
across states by using relative wage measures in our
analysis. Our two-staged, least-squares estimates indicate
that the results are not driven by endogeneity bias.
Our estimates suggest that, holding all else equal, raising
teachers’ wages by 10% (which would undo the 10% fall in
relative wages that occurred during the 1980s) would reduce
dropout rates by between 3% and 6%. Likewise, if the 20%
increase in real teacher wages that occurred between 1959
and 1989 had been a relative increase (that is, the alternative
opportunities for female college graduates had remained
constant), then dropout rates would be at least 8.4% lower
than they are today. A back-of-the-envelope comparison of
the costs and bene ts associated with raising teacher wages
by 10% indicates that the increase in individuals’ discounted
lifetime wages that would result from the additional educa-
tional attainment produced by such an increase would be
slightly outweighed by the cost. An increase in teacher
wages is likely to affect outcomes other than the educational
attainment measures that we have focused on in this study,
however. Moreover, targeted increases may be more effec-
tive than across-the-board increases. A more complete
analysis of the total costs and bene ts associated with such a
policy is certainly warranted.
When we compare our  rst-differences estimates to those
based on data from a single year, we  nd that the  rst-
differences approach produces standard-error estimates that
are smaller and coefficient estimates that are more similar
across speci cations. In addition, when we include state-
speci c time trends (which partially account for state-
38 The results are substantively similar using either speci cation, but the
standard errors are somewhat smaller when levels are used. We believe this
is due to the difference in the de nition of dropout rate between 1986 and
39 We use the percentage of students receiving AFDC as a proxy for local
income levels. Our results are unaffected by the inclusion of this variable.
in Real
Change in
1985 drop out rates 21.296
1995 drop out rates 0.005
1985–1995 Ddropout
in Real
Change in
1985 d ropout rates 25.201
1995 d ropout rates 0.0127
1985–1995 Ddropout
speci c changes in the attributes that are associated with
teaching), the magnitude of our wage-coefficient estimates
increases. This result is consistent with the existence of
compensating differentials.
Our  ndings have important policy implications. First of
all, they suggest that the quality of education can be
improved by raising teacher salaries. In addition, they
indicate that non-wage attributes are important and should
be taken into account by governments that seek to equalize
the quality of education. Districts that are unable to increase
salaries because of funding limitations may be able to attract
higher-quality teachers by improving other job characteris-
tics. Of course, the feasibility of this alternative depends
upon how much control districts have over their own
characteristics and upon which characteristics affect the
opportunity cost of teaching. Our  rst-differences estimation
approach—together with our use of state-speci c dummy
variables—implicitly control for these characteristics, but
does not provide insight into which school- or district-
speci c factors are most important. Furthermore, we are
unable to control for a number of state-speci c, time-
varying job attributes such as changes in teacher workloads
and changes in teacher certi cation requirements that may
affect the degree to which changes in teacher wages re ect
changes in the opportunity cost associated with choosing to
teach. We hope to investigate these issues in future research.
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... A lot of studies have been done on teacher promotion and upgrading but they did not cover all aspects of these phenomena. For instance, the works of Bennel and Akyeampong (2007), Chiduwoli (2007), Johnson and Donaldson (2006), Loeb and Page (2000), and Masondo (2014) did not cover this pertinent issue. These studies covered some important aspects of teacher motivation, promotion, and upgrading, yet the effects that this denial or delay in these processes has on the affected teachers had been neglected. ...
Full-text available
Promotion and upgrading of teachers after years of service and/or further studies are very essential in the working life of teachers as other formal employees. This is because promotion and upgrading serve as motivational means for hard work and high productivity. However, they do not come without challenges. The challenges inherent in the processes of promotion and upgrading of teachers and the effects the challenges have on teachers seemed to have received little scientific investigation. This research gap precipitated the conduct of this exercise in the Bono region of Ghana. The descriptive survey study was conducted among public senior high school teachers and a sample size of 246 was used. The data were collected using a survey questionnaire and SPSS version 23 was used to analyze the data. The study revealed the following as the challenges teachers encounter during promotions: irregular and untimely release of promotion information, long procedure in the application, too many documents required, and untimely release of promotion results. The challenges tend to have effects on teachers’ work output as well as their psychological, social, and emotional well-being. The study further disclosed that the teachers encounter challenges with upgrading as well which also tends to affect them psychologically, emotionally, and socially as well as their work output. It is therefore concluded that the challenges that the teachers encounter while undergoing promotion and upgrading tend to have an effect on their psychological, social and emotional states as well as their confidence to work which can affect their work output. This would be detrimental to student learning and progress. The study then recommends that the Ghana Education Service (GES) has to take the necessary steps to eliminate the challenges inherent in promotion and upgrading to enable teachers to devote adequate time to their work. Article visualizations: </p
... The result of this study corroborated Udoh and Akpa (2007) who affirmed in their study that employees should be involved in decisions that concern them like general working conditions, fringe benefits and staff development programs as these add to the attractiveness of the work environment. That notwithstanding, Loeb and Page (2000) and Stoddard (2003) confirmed a plausible explanation for why most studies fail to find a relationship between teacher salaries and student outcomes. Student quality and other non-pecuniary characteristics are valued by teachers, vary considerably by district, and are likely to be "capitalized" into teacher wages as compensating differentials; thus teachers may be willing to accept lower wages in districts with better working conditions or higher student quality, both of which are likely to be correlated with higher student outcomes. ...
... For instance, Springer et al. (2016) explained that retention bonuses are rooted in the theory that even small economic awards can mitigate problematic teacher-exit patterns in high-need and low-performing schools. Others, such as Bacolod (2007) and Loeb and Page (2000), refer to the theory of compensating wage differential to explain the need for additional compensation to recruit and retain quality teachers to high-need schools when compared to the compensation offered by more desirable schools or non-teaching careers. In support of the theory, Marvel et al. (2007) found that 15% of teachers left teaching positions to accept another teaching position in a school paying more. ...
Situated against teacher demand problems worldwide, rising teacher turnover and declining teacher education enrollment have rendered the state of South Carolina a region commonly described as facing a “teacher shortage crisis.” This paper reports results from an evaluation of the Rural Recruitment Initiative (RRI), a state-level teacher staffing policy for SC’s hard-to-staff districts. Based on a decade of data analysis, we assess RRI’s causal effect using a Difference-in-Differences model with Arellano–Bond maximum likelihood design and find that RRI funding reduces teacher turnover rate by 1% for fund-receiving districts. We conclude by discussing how the initiative could be improved and what policymakers can learn from our results.
... • A study by Loeb and Page (2000) shows that a 50% increase in teachers' salaries reduces high school dropout rates by more than 15% and increases college enrollment rates by about 8%. They also explain why previous studies have failed to produce systematic evidence that teacher wages affect student outcomes: "The identification of teacher wage effects has been based on cross sectional variation that reflects both supply and demand factors. ...
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Recent economic developments of countries like Japan, Korea, and Singapore, as a result of improvement in the quality of their education, show that having a high-quality education may lead to economic growth. In this article, using some statistical methods, we argue that high quality education can change the economy towards higher growth. Therefore, for the development of the country, one should think about how to improve its education. One of the effective ways to improve the quality of education is to increase the efficiency of teachers and attract talented people to teaching positions. Research shows that raising teachers' salaries, along with a proper quality improvement program, can help facilitate this process.
... Teacher satisfaction with work is mainly influenced by salary, advancement options, appreciation of the teaching profession in the country and conditions of the working contract (duration, % of classes, paid benefits, etc.). Loeb & Page (2000) estimate that raising teacher wages by 10% reduces high school drop-out rates by 3% to 4%. ...
Levels of governance (the nation, states, and districts), student subgroups (racially and ethnically minoritized and economically disadvantaged students), and types of resources (expenditures, class sizes, and teacher quality) intersect to represent a complex and comprehensive picture of K-12 educational resource inequality. Drawing on multiple sources of the most recent available data, we describe inequality in multiple dimensions. At the national level, racially and ethnically minoritized and economically disadvantaged students receive between $30 and $800 less in K-12 expenditures per pupil than white and economically advantaged students. At the state and district levels, per-pupil expenditures generally favor racially and ethnically minoritized and economically disadvantaged students compared to white and economically advantaged students. Looking at nonpecuniary resources, minoritized and economically disadvantaged students have smaller class sizes than their subgroup counterparts in the average district, but these students also have greater exposure to inexperienced teachers. We see no evidence that district-level spending in favor of traditionally disadvantaged subgroups is explained by district size, average district spending, teacher turnover, or expenditures on auxiliary staff, but black and Hispanic spending advantage is correlated with the relative size of the black and Hispanic special education population.
This paper examines how short-term variation in potential teachers’ outside options affects who chooses to teach in public schools. I use variation in state level unemployment rates as a source of plausibly exogenous variation in outside options available to first-year teachers among teachers surveyed in the NCES School and Staffing Survey. I find that those who become teachers when the local labor market is weak are both more likely to have come from highly selective colleges and more likely to express dissatisfaction with their jobs. Other observable demographic, educational, and certification characteristics of newly hired teachers are not affected. Teachers who enter during weaker labor markets are also no less likely to remain in teaching in the short run. Economic downturns provide a potential opportunity for schools to attract and retain academically talented workers, but this may come at a cost to those workers in the form of reduced job satisfaction.
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The purpose of this paper is to clarify the importance of education economics as a modern approach to educational research, especially the importance of the policy of raising teacher wages as a mechanism to improve the educational attainment of students in government schools. The study used the inductive approach by examining the experience of Algeria between 1970 and 2018, where the Algerian government raised teachers' wages by more than 100% with the aim of improving the educational attainment of students. Therefore, the study adopted the standard method through a statistical model for a linear relationship linking the passing rate in the baccalaureate exam to express the dependent variable represented in academic achievement for students, while invoking three independent variables to indicate teachers' wages which are: minimum wages, government support, and inflation. Through the ARDL method, the assessment results showed the direct and strong relationship between teacher wages and educational attainment for students in the short and long term. هدفت الدراسة لتوضيح أهمية علم "اقتصاديات التعليم" كمنهج حديث في مجال البحث التربوي، من خلال تحليل العلاقة بين "أجور المعلمين" و"التحصيل العلمي" للتلاميذ في المدارس الحكومية. وذلك من خلال دراسة تجربة الجزائر بين عامي 1970 إلى 2018 وفق الأسلوب الاحصائي ومن خلال طريقة "الانحدار الذاتي للفجوات الزمنية الموزعة (ARDL)". وقد أظهرت النتائج العلاقة العكسية والقوية لـ "التحصيل العلمي" مع مستوى "التضخم"، بالتوازي مع علاقة موجبة مع كل من "الحد الأدنى لللأجور" ونسبة التغير السنوية في مخصصات "الدعم الحكومي"، وهي نتائج تتوافق مع الأدبيات الاقتصادية وطبيعة الظاهرة، وتؤكد فرضية العلاقة الطردية والقوية بين "أجور المعلمين" والتحصيل العلمي" للتلاميذ على المديين القريب والبعيد. كما أكدت الدراسة على أهمية اعتماد آلية "الحد الأدنى للأجور" وسياسة "التفاوض الجماعي" لتحديد المستوى العام للأجور؛ وأيضاً، عدم التركيز على القيمة الإسمية للأجور واستهداف قيمتها الحقيقية وإلا فلن يكون لسياسة رفع "أجور المعلمين" كآلية لتحسين "التحصيل العلمي" للتلاميذ في المدارس الحكومية أي نتائج.
The extent to which higher per pupil expenditures lead to any desirable outputs is an important policy question. We develop several alternative models which relate per pupil school expenditures to achievement orientation, verbal ability, years of schooling, and earnings. Our results indicate that the point estimate for the rate of return to increases in per pupil school expenditures is quite respectable for whites and very high for blacks irrespective of the model used. However, in one plausible model it is not possible to reject the hypothesis that the rate of return to whites is zero. In contrast, the results for blacks are not only consistently large, but also robust.
Data on a large sample of high school seniors are used to estimate the relationship between ability test scores and various dimensions of educational input. The inputs examined include measures of each student's family background, the background of other students at the high school attended, and components of expenditure per student at the high school attended. The results suggest that: (1) a number of components of educational expenditure are significantly related to ability test scores, (2) both school integration and compensatory education are capable of altering the relation between ability and family background, and (3) school integration by family income level raises the ability test performance of low-income students while lowering that of high-income students by an equivalent or greater amount.
With the help of data from the Project Talent national survey of high schools, and follow-up surveys from the same source, this paper attempts measurement of the long-run effects of increased school spending. School expenditures are found to influence how many years of schooling an individual eventually receives, and the chief effect of spending differences on lifetime income is found to work through this school continuation link. The time-discounted lifetime income gain that is associated with increased spending is estimated to be less than the amount of the increased spending.
This study attempts to shed some light on the cost and output functions of the Iowa public school system (as of 1962-63). As a proxy for high school quality, incremental test scores on the Iowa Tests of Educational Development (ITED) are used. The estimated per pupil cost functions suggest the existence of significant economies of scale for the Iowa sample of 377 high school districts. When a parabolic cost function is utilized, an optimal high school size (in terms of the number of pupils in average daily attendance) can be estimated. Confidence limits for such an optimum are also calculated.
Studies analyzing expenditures for public education have used a variety of inputs into the educational process as proxies for the quality of education. This study attempts to isolate some of the inputs which do, in fact, have an effect upon educational quality. To accomplish this, output measures of quality were derived from a sample of 5,000 West Virginia University students who had graduated from high schools within the state. The results show that only one of the input variables examined, teachers' salaries, was significantly related to the output measures of quality. In addition, factors exogenous to the local school system-factors reflecting socioeconomic characteristics of the communities in which the school systems were located-were observed to have a significant effect upon quality. The results give rise to dual conclusions. First, input variables seem to be imprecise measures of educational quality. Second, the empirical evidence provides some support for the contention that the quality of education may be improved by offering higher salaries to teachers.
This article presents the results of an empirical analysis of the relationship between school funding and student achievement across school districts in Cali- fornia. Student achievement is measured by district average scores on ien standardized tests. The model controls for standard socioeconomic factors and entry-level student performance. It is found that changes in expenditure patterns, e.g., equalization of funding per student, would have a statistically sig nificant effect on test scores.
To investigate school size effects for secondary schools, 18 school outcomes, including the average scores on state-developed tests, student retention, suspensions, postschool employment, and college attendance for 293 public secondary schools in New Jersey were regressed on 23 school characteristics, including district socioeconomic status and percentages of students from low-income families; school size and number of schools within each district; and teacher characteristics encompassing salaries, degree status, and years of experience. District socioeconomic status and the percentage of students from low-income families in the school were the most influential and consistent factors related to schooling outcomes. School size was the next most consistent and was negatively related to outcomes. This finding corroborates previous research conducted primarily on public elementary school and suggests that smaller school districts and smaller schools, regardless of socioeconomic status and grade level, may be more efficient at enhancing educational outcomes.