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Federal Reserve Bank of Chicago
School Vouchers and Student
Achievement: Recent Evidence,
Remaining Questions
Cecilia Elena Rouse and Lisa Barrow
WP 2008-08
School Vouchers and Student Achievement:
Recent Evidence, Remaining Questions
Cecilia Elena Rouse
Princeton University and NBER
Lisa Barrow
Federal Reserve Bank of Chicago
August 6, 2008
We thank David Figlio, Patricia Muller, Jonathan Plucker, and Jesse Rothstein for helpful
conversations and Clive Belfield for providing us with additional information on the Cleveland
Scholarship and Tutoring Program. Elizabeth Debraggio, Emily Buchsbaum, Mitta Isley, and
Katherine Meckel provided expert research assistance. Any views expressed in this paper do not
necessarily reflect those of the Federal Reserve Bank of Chicago or the Federal Reserve System.
Any errors are ours.
Posted with permission from the Annual Review of Economics, Volume 1, © 2009 by Annual
Reviews, http://www.annualreviews.org
Abstract
In this article, we review the empirical evidence on the impact of education vouchers on student
achievement, and briefly discuss the evidence from other forms of school choice. The best
research to date finds relatively small achievement gains for students offered education vouchers,
most of which are not statistically different from zero. Further, what little evidence exists
regarding the potential for public schools to respond to increased competitive pressure generated
by vouchers suggests that one should remain wary that large improvements would result from a
more comprehensive voucher system. The evidence from other forms of school choice is also
consistent with this conclusion. Many questions remain unanswered, however, including
whether vouchers have longer-run impacts on outcomes such as graduation rates, college
enrollment, or even future wages, and whether vouchers might nevertheless provide a costneutral alternative to our current system of public education provision at the elementary and
secondary school level.
1
Of the nearly 60 million school-aged children in the U.S.: 87% attend a public school,
11% attend a private school, and approximately 2% are home-schooled. Fewer than 60,000
currently participate in a publicly-funded school voucher program. Rather, the vast majority –
nearly three-quarters of all students – attend their neighborhood public school (Tice, et al. 2006).
And yet many complain that these traditional public schools do not educate children well, as
evidenced by stagnant test scores and poor showings in international comparisons. What is not
so clear is how to address these concerns.
Convinced that schools need to manage their resources better, recent efforts have
attempted to inject more accountability into the education sector. One approach is through “testbased” or “administratively-based” accountability in which students are regularly assessed and
the results of these assessments are made public. The theory is that with more information about
the performance of the local public schools, parents and administrators will demand a better
product. A second – more controversial – approach is to increase accountability by increasing
the educational choices available to parents.
If the current system does, indeed, provide
education to children inefficiently, then by increasing choice (which should induce competition),
one can, theoretically, improve student achievement without significantly increasing public
expenditures.
Choice in the education sector can take many forms. Since school quality factors heavily
into family residential decisions (e.g., Barrow 2002 and Black 1999), “residential choice” is the
most prevalent form of public school choice. However, several programs increase school choice
for families after they have decided where to live. Open enrollment programs – such as those in
Charlotte-Mecklenburg, NC and Milwaukee, WI – ask parents to rank public schools within the
2
district and then assign children to schools according to parental preference. Magnet schools –
which were largely developed in response to desegregation efforts – are typically specialized
schools to which all district students are eligible to apply. More recently many students also
have the option of applying to charter schools, which are publicly-funded but operate with
greater autonomy than traditional public schools. Finally, since the early 1990s, several smallscale voucher programs have been started in the U.S. – some publicly financed and others
privately financed. In this paper we focus on the evidence from education vouchers, one
particular strategy for increasing competition in education provision and thereby accountability.
As a market-level intervention, there are many important factors to consider when
evaluating the potential impact of school vouchers on society, including their effect on student
outcomes, school efficiency (including costs), and social stratification (both within and across
schools and neighborhoods). Decoupling school finance from residential decisions would also
likely impact housing markets and markets for education inputs, such as teachers. Unfortunately,
a comprehensive treatment of all of these dimensions is beyond the scope of this review.
Instead, we focus on the empirical evidence on the impact of education vouchers on student
achievement, and briefly discuss evidence from other forms of school choice. Our discussion is
limited to U.S. voucher programs since, theoretically, the (relative) effectiveness of such
programs depends on the relative efficiency of the public sector schools as well as the existing
competitive environment in education. For example, public elementary and secondary schooling
in the U.S. has largely depended on local financing meaning that choice between local school
districts may already generate strong competitive pressure. As a result, there may be less
potential for vouchers to generate large efficiency gains (see, e.g., Barrow & Rouse 2004). A
3
less efficient public sector and a less competitive (public schooling) environment may explain
the large impacts of school vouchers that have been estimated in other countries, such as
Columbia (see, e.g., Angrist et al. 2002).
After reviewing the empirical evidence from the U.S., we conclude that expectations
about the ability of vouchers to substantially improve achievement for the students who use them
should be tempered by the results of the studies to date. In addition, while not as extensive or
compelling, the evidence of meaningful gains for those students who remain behind in the public
schools is also weak. That said, many questions remain – for example, no studies have examined
the longer-run impact of vouchers on outcomes such as graduation rates, college enrollment, and
future wages. Further, the research designs for studying the potential impacts of vouchers on
students who remain in the public schools are far from ideal.
In the next section, we discuss the theoretical reasons why education vouchers should
improve student achievement and then review the empirical approaches used for identifying such
effects of vouchers. Next, we present the best evidence examining the impact of school vouchers
on student achievement from existing studies of publicly- and privately-financed programs. We
then briefly discuss evidence from other forms of school choice, consider other potential
increases in social welfare, and finally conclude.
WHY COMPETITION SHOULD IMPROVE THE EDUCATIONAL SYSTEM
The idea of injecting competition into the public school system is not new; Milton
Friedman (1962) argued for separating the financing and provision of public schooling by
issuing vouchers redeemable for a maximum amount per child if spent on education. The basic
4
rationale behind school vouchers is that competitive markets allocate resources more efficiently
than do monopolistic ones. Many observers argue that since children are assigned to attend their
local neighborhood school, public schools in the U.S. have “monopoly” power. Once a family
has decided where to live, they have significantly fewer publicly-funded schooling options.
Parents can choose to send their child to private school, but that means paying for schooling
twice: once through property taxes (for the public schooling they are not using) and again
through private school tuition. If parents had more publicly-funded options, then schools would
have to compete for students. More options might also increase (allocative) efficiency by
improving the match between students and their educational interests and needs. Importantly,
schools in this model would have an incentive to improve along the margins valued by parents.
If parents select schools based on their academic quality, then schools would compete for
students along such margins; if parents value religious education or sports, then one would
expect to see schools respond along these margins.1
One of the challenges in considering the impact of education vouchers on student
achievement in the abstract is that impacts likely hinge on the design of the voucher program in
1
Even if parents value “school quality” a related, yet poorly understood, issue is what is
meant by school quality in practice. A school can have high levels of academic achievement not
because the school is adding significant value to the students, but because the students it attracts
are already high achieving. Thus, if parents select schools based on the average level of the
academic outcomes of the students, then they are implicitly putting more weight on the peers
their child would likely encounter while at that school rather than on the school’s ability to raise
the achievement of a randomly selected child (irrespective of the average achievement of the
child’s classmates). Rothstein (2006) finds evidence consistent with parents choosing schools
based on the potential peer group offered by the school rather than a productive advantage. This
finding suggests that school choice would not provide an incentive for public schools to improve
along academic dimensions defined as value-added. In contrast, Hanushek et al. (2007) find
evidence suggesting that parents put some weight on a school’s value added as well.
5
question. For example, two design features are the generosity of the voucher and whether
parents can “top up” the voucher to attend a school that charges tuition exceeding the voucher
amount. In Friedman’s original conception, the government would pay an amount per pupil for
schooling2 and this voucher could be used to pay part, or all, of the tuition at any “approved”
school.3 Further, all students would be eligible for a voucher and there would be no governmentimposed regulations on how the private schools select their students. By allowing “topping-up,”
extending eligibility to all students, and not imposing restrictions on the admissions processes
used by the private schools, all schools become “public” schools in Friedman’s voucher system
as all accept public financing. In this model the scope for competitive pressure on local public
schools is quite large.
Another important design element is whether transportation is provided with the voucher.
Currently, local public schools provide transportation to students and because most students are
assigned to attend their neighborhood school, transportation costs are minimized. Whether a
voucher program would also pay for transportation affects the viable schooling alternatives for
parents, which would affect the level of competition. Paying for transportation increases the
choices available to parents, but also increases costs.
Far from Friedman’s ideal, the publicly-funded voucher programs in the U.S. to date
require that the participating schools accept the voucher as the full, or a substantial portion of,
2
Friedman is silent on whether the voucher should be “flat” – where all students would
receive the same amount, or “graduated” depending on family income or the child’s educational
needs (e.g., special education or bilingual education).
3
The primary government role in this conception is to impose “minimum” standards.
6
tuition (although they may be allowed to charge additional “fees”); are limited to low-income
students or to students attending very low-performing schools; and require participating schools
to accept all potential voucher students who apply or to randomly choose among them if
oversubscribed. Most of the programs also provide some transportation for the participating
students, particularly if the private school is not located far from the student’s home. With the
exception of the provision of transportation, the other features of these programs – their
relatively small size and the restrictions on the private schools – likely dampen the potential for a
substantial increase in the choices available to parents.
Keeping these issues in mind and assuming that parents value academic quality in their
child’s school, there are two hypothesized ways by which increased school choice would
improve student educational outcomes. The first is a “direct” effect for those students who
actually exercise choice. Assuming that students would only choose to attend a school other than
their neighborhood school if the alternative were better (or a better match), then the academic
achievement of students who opt for a different school should improve relative to what their
performance would have been had they stayed in the public school. The second is a “systemic”
or “general equilibrium” effect on students remaining in the public schools.
Increased
competition should induce the public schools to improve in an effort to attract (or retain)
students.
Not only should the achievement of those who choose to attend a private (or
alternative) school increase, but so should the achievement of those who do not choose to leave
as well. In other words, the increase in competition should also increase the efficiency of public
schools.
Of course, expansion of the private sector is a critical component of increasing
competition. Without new school entry and/or increases in the size of current private schools,
7
vouchers would have limited ability to increase choice.
The fact that many empirical studies find that students in private schools have higher
educational achievement levels than those in public schools (see, e.g., Coleman et al. 1982a,
1982b; Evans & Schwab 1995; Neal 1997; and Altonji et al. 2005a) is presented by voucher
advocates as prima facie evidence that vouchers would improve student achievement for all.
Namely, they argue that private schools outperform public schools because their existence
depends on providing a good product. Educational vouchers are intended to make public schools
compete in this same way; thus, only schools (either public or private) providing a good product
would survive. However, this literature is not conclusive because of the difficulty (described
below) in identifying a causal impact of private schools on student achievement.
Not
surprisingly, critics argue that the observed superiority of private schools in these studies arises
from omitted variables bias – the students who attend private schools differ from the students
who attend public schools – rather than differences in the effectiveness of the schools (see, e.g.,
Goldberger & Cain 1982, Cain & Goldberger 1983, and Altonji et al. 2005b). If this is the case,
the achievement of current public school students would not necessarily improve in private
schools.
While the debate continues whether private schools, in general, are better at educating
children than public schools, researchers have turned to more direct evidence on the impact of
vouchers by studying actual school voucher programs.
EMPIRICAL APPROACHES TO STUDYING SCHOOL VOUCHERS
Economists typically model school outcomes using an “education production function”
8
where schools produce education using inputs and a production technology. The effect of
particular inputs on the output (e.g. educational achievement) can then be measured, usually for
each student. As the theory behind school vouchers is silent on the source of the increased
efficiency – whether it arises from differential use (production technology) and/or the level of
inputs – the empirical research has simply attempted to study whether educational outcomes in
the presence of vouchers are better than educational outcomes in the absence of vouchers.
Strategies to Estimate the Direct Impact of Vouchers
To study the direct impact of vouchers on the students who use them, analysts have
estimated versions of the following education production function:
E it = α + β t Vit + X i γ t + ε it ,
(1)
where Eit represents the output for student i in year t; Vit represents whether student i used a
voucher in year t; Xi represents observable student characteristics (such as sex and race); and εit
is an error term that represents all the other factors affecting achievement but not observed by the
researcher. (One could also constrain the impact of the voucher program to be linear, in which
case the independent variable would be the number of years since the student was eligible for, or
actually enrolled in, a voucher program.) Note here that Vit proxies for the bundle of inputs and
production technologies that make a school a “school” – including the peer group, which may
not be under the control of a school (especially a public school).
A positive coefficient on Vit (βt>0) suggests that students who used a voucher had better
educational outcomes than those who did not. Further, researchers typically infer that the impact
9
of using a voucher (the coefficient on Vit) derives from differences in the effectiveness of the
schools attended by voucher students compared to those who opted to remain in a public school.
The problem in estimating equation (1) (and its variants) is that the non-voucher students may
not provide a valid counterfactual to the voucher students. In particular, voucher use and
educational outcomes may be endogenous such that E[εit|Vit,Xi] ≠ 0. For example, students with
parents who are very educationally focused and motivated may be more likely to apply for a
school voucher, yet these students may have done better than their non-voucher classmates even
in the absence of the voucher program. Unless these non-school inputs are fully observable to the
researcher such that she is able to control for them, the estimated impact of vouchers (βt) will
likely be biased. As a result, to estimate the effect of vouchers on school outputs, researchers
have relied on analytical strategies that adequately control for differences between the two
groups of students.
One of the most common strategies is to assume that a student’s prior test score(s), in
year t-1 (or earlier), reflects her innate “ability” or motivation, as well as the accumulation of the
schooling inputs she has received up to year t. Under this assumption, researchers typically
estimate current achievement as:
Eit = α ′ + λt Eit −1 + β t′Vit + X iγ t′ + ε it′ ,
(2)
where Eit-1 reflects prior achievement (typically a test score). The identifying assumption is that
Eit-1 fully proxies for the inputs that affect a student’s achievement prior to using a voucher and
are also correlated with a student’s likelihood of using a voucher such that E(εit′|Vit,Xi,Eit-1) = 0.
Clearly, this is a strong assumption as test scores are, at best, a noisy measure of student ability.
10
Additionally, one must assume that this prior test score (or a series of test scores) also captures
the unmeasured characteristics that led some students to apply for a voucher program (or that
determine eligibility) while others did not.
If Eit-1 was obtained before the student was selected for, or enrolled in, the voucher
program, this strategy amounts to comparing the average change – or gain – in student
achievement from before to after participation in the voucher program to the change in the test
scores of students in the comparison group (the non-voucher students). In the case where the
researcher observes outcomes for multiple periods, controlling for Eit-1 for periods t>1 will only
allow one to detect βt′>0 in the case where the yearly achievement gains of students in the
voucher program are consistently higher than those of students in the comparison group. If there
is an initial gain by voucher students followed by a plateau, the estimate of βt′ obtained in
equation (2) will potentially understate the impact of the voucher program since the early impact
will have been effectively absorbed by Eit-1.
A variant of equation (2) is to control for all time-invariant student characteristics by
including student fixed effects. In this case βt′ is identified only off of students switching
voucher status. The assumption that must hold for the fixed-effects estimate to generate an
unbiased effect of vouchers is that there are no unobserved time-varying differences between the
two groups of students that would explain changes in the test scores, except for use of a voucher.
While appealing, one might be concerned that there are remaining unobserved differences
affecting both the likelihood of using a voucher and educational achievement.
Perhaps the most compelling strategy to generate causal estimates of the effect of
vouchers on student outcomes is through the use of a random assignment design. In this
11
“experimental” research design, students are randomly assigned to either a “treatment group”
that is offered a school voucher or a “control group” that is not. In this case, there are no
differences in the observed or unobserved non-school inputs, on average, between the two
groups because the offer of a voucher was not determined by family income or one’s motivation,
but rather by the “flip of a coin.” Thus, the typical empirical specification is,
Eilt = α ′′ + θ t Sit + X iγ t′′ + ϕl + ε ilt′′ ,
(3)
where Sit indicates whether a student was selected for (or offered) a voucher and φl represents the
lottery (l) in which the student actually participated. Thus, by construction E[ε˝ilt|Sit,φl] = 0 for
students taking part in the randomization. Note that if the randomization is properly
implemented, then one need not condition on other student characteristics (Xi) in order for the
estimate of θt to be unbiased, although researchers will occasionally do so to gain efficiency in
the standard errors.
Ordinary least squares (OLS) estimation of equation (3) should generate an unbiased
estimate of the impact of offering vouchers on student outcomes in a particular year (θt), a
parameter known as the “intent-to-treat” effect. This impact reflects two parameters that are
important for evaluating a voucher program: the rate at which students actually take-up vouchers
and the relative achievement of students in private schools.
As such, the intent-to-treat
parameter has two appealing properties: it is the only unambiguously unbiased estimate that one
can obtain using typical statistical methods such as OLS regression, and it reflects the overall
potential gains from offering the vouchers as a policy, because it combines take-up with the
relative gains for those who actually use the voucher.
12
Many are also interested in the effect of “treatment-on-the-treated” – whether students
who actually use a voucher experience academic gains as a result. Because actual use of a
voucher is not randomly determined, analysts must resort to non-experimental methods to
generate consistent estimates of the effect of treatment-on-the-treated. A common approach is to
use an instrumental variables strategy in which whether a student was randomly offered a
voucher is used as an instrumental variable for the student attending a private school. This type
of analysis generates a consistent estimate of whether the schools attended by voucher students
were more, less, or equally as effective as the schools attended by the non-voucher students.4
Properly implemented, a randomized design is viewed as the “gold standard” for
estimating a causal relationship between vouchers and student outcomes. In practice however,
non-random differences can emerge between the treatment and control groups. For example,
often researchers conducting the study are not able to collect follow-up data on every study
student potentially introducing non-random selection into the analysis. In addition, to the extent
there are heterogeneous treatment impacts, the estimated impact of vouchers on student
outcomes from one or two small studies may not represent the effect for a different group of
students.
Strategies to Estimate Public School Responses to Competitive Pressure
The empirical strategies discussed above are designed to generate estimates of the direct
4
Technically speaking, an instrumental variables analysis would generate a consistent
estimate of the impact of attending a private school for those students who were induced to
attend the private school only because of the voucher, an estimator known as the “Local Average
Treatment Effect” (LATE) (Angrist & Imbens (1994); Angrist et al. (1996)).
13
impact of vouchers on student achievement. However, the true prize of a voucher system – or of
any program designed to significantly increase the competitive pressure experienced by public
schools – is overall improvement in the performance of the U.S. education system.
Unfortunately, developing a study that would generate unbiased estimates of any such systemic
impacts is extremely difficult.5 The problem is that, in theory, the public schools should improve
in response to the increased competition and thus increase the achievement of the public school
students as well. As a result, the public school students do not represent what would have
happened to the voucher students in the absence of the voucher program, so a simple comparison
of the outcomes of students who use a voucher (or who were offered a voucher) to the outcomes
of students who remained in the public schools (either by choice or because of “bad luck” in a
lottery) would likely underestimate the general equilibrium impact.
Instead, one must first identify the relevant “market” for schooling within which a school
exists. The key is that the unit of observation for this study is not the individual student, but the
market. Ideally one would randomly assign some markets to a treatment group – where the
students would be eligible for school vouchers – and randomly assign the remaining markets to a
control group – where there would be no vouchers. After a period of time, the researcher would
5
Due to the difficulty of obtaining evidence on the impacts of a large-scale voucher
program, a theoretical literature appeals to computable general equilibrium models to understand
broader implications of vouchers, such as the impact on student sorting and residential
segregation. For example, Epple & Romano (1998) focus on the impact of vouchers on student
stratification and Nechbya (1999, 2000, 2003) considers the impact of different voucher schemes
on residential mobility and segregation. Ultimately, though, the potential for school vouchers to
improve student achievement in these models hinges on the relative impact of private schools vs.
public schools on student achievement and/or on the response of public schools to increased
competition (see, e.g., Epple & Romano (1998, 2003) and Nechyba (2003)).
14
then compare the average outcomes of students in the voucher markets to those of students in the
control markets. A simple comparison of student outcomes would yield an unbiased estimate of
the general equilibrium impact of vouchers since, on average, the markets would have been
similar ex-ante.
While such an experiment is possible in theory, in practice it would be
extremely difficult to implement primarily because it would require the coordination and
cooperation of so many different stakeholders. As a result, researchers have turned to other
research designs to try to generate a causal estimate of the impact of a large-scale voucher
program.
One approach that researchers have used is to model student achievement in existing
public schools as a function of the competitive pressure experienced by the student’s school,
school district, or metropolitan area.
If public school student achievement improves, the
assumption is that it is due to a response by the existing public schools to the increased
competitive pressure. As such researchers have estimated versions of the following equation:
Eidt = a + bt H dt + X i gt + eidt ,
(4)
where d indexes the area (the school district, metropolitan area, or geographic area around a
particular school), and Hdt is a measure of the competitive pressure faced by the school – such as
the metropolitan-level Herfindahl-Hirschman Index6, the number of schools within a particular
radius of an existing public school, or the school’s likely exposure to competitive pressure
6
A Herfindahl-Hirschman Index based on the concentration of enrollment in a
geographic area is meant to proxy for the market power of public schools in the area and
therefore the degree of “choice” that parents may have.
15
because of the eligibility rules of a voucher program.7 As before, the challenge is to identify
districts (or metropolitan areas) facing little competitive pressure that can serve as valid
comparisons to those facing increased competitive pressure. One strategy that has been used to
address this endogeneity is to employ an instrumental variable that is correlated with the
endogenous variable (the level of competitive pressure), but not correlated with the error term in
the achievement equation.
Another strategy is to exploit non-linearities in voucher eligibility in an approach known
as “regression discontinuity.” In this case, voucher eligibility is represented by a simple rule,
Vis = 1 if k is ≤ k *
Vis = 0 otherwise,
(5)
where kis is the characteristic (or an index measure of characteristics) on which eligibility is
determined (in this example i indexes the individual and s the school) and k* is the cutoff for
eligibility. To date, this strategy has been used when students attending schools identified as
chronically “failing” according to Florida’s school accountability system were eligible for a
voucher to attend participating private schools or a higher-rated public school. The school’s
“accountability points” clearly determined voucher eligibility and likely had an independent
effect on student achievement (both because the school was failing and because students
attending failing schools were more likely to come from disadvantaged families). However,
students in schools earning just below the accountability point cutoff were arguably quite similar
7
Note that although the unit of observation is the “market” (e.g., school district or
metropolitan area), analysts often employ data on individual students. In this case, they must be
careful to adjust the estimated standard errors to account for clustering of students within the
same “market.”
16
to students in schools earning just above the accountability point cutoff. Thus, researchers
identify the causal effect of voucher eligibility (and voucher “threat”) on student achievement
(for students in the vicinity of the eligibility cutoff) by comparing the average educational
achievement of students in schools just below the accountability point cutoff to the average
educational achievement of students in schools just above the accountability point cutoff. In
practice, researchers have estimated:
′′ ist + X iγ t′′′+ ε ist
′′′
Eist = α ′′′ + c(kis ) + β t′V
(6)
where c(kis) is a polynomial in the characteristic on which eligibility is determined. To the extent
that schools can manipulate their accountability points to affect their identification as “failing,”
the assumption that students attending schools on either side of the accountability point cutoff
are otherwise quite similar is less compelling. A more general concern about estimates derived
from regression discontinuity designs is that while they may generate unbiased estimates of the
impact of a policy for schools near the cut-off point, in the presence of heterogeneous treatment
effects, these impacts may not generalize to other schools.
EVIDENCE ON SCHOOL VOUCHERS AND OTHER FORMS OF CHOICE
Do Students Who Use School Vouchers Benefit?
In the U.S. two types of school voucher programs have been studied: those financed by
the government (publicly-funded school vouchers) and those provided by the private sector
(privately-funded school vouchers).
From a public policy perspective, the evidence from
17
publicly-funded programs is more relevant as they incorporate some of the design features that
might be built into a larger school voucher program, such as limitations on which students are
eligible to receive a voucher and whether transportation is provided or reimbursed. That said,
some of the most compelling evidence from a methodological perspective comes from the
privately-funded vouchers, so we review that evidence here as well. Note that because this
literature essentially compares the performance of students in private schools to that of students
in public schools, it bears striking similarity to that on differential effectiveness of private and
public schools.
In Table 1 we present a summary of selected findings from publicly-funded voucher
programs with formal evaluations. All of the estimates are converted to “effect sizes” (i.e., the
impact divided by the standard deviation of the test distribution) normalized by the national
standard deviation so that the implied magnitudes of the effects are not affected by the standard
deviation of the subgroup within each study. As such, these impacts can be interpreted as
proportions of a national standard deviation. As a benchmark for judging the magnitude of the
impacts, Hill et al. (2007) review effect sizes from many studies of educational interventions.
While they caution it is only valid to compare effect sizes using comparable populations,
contexts and interventions, and outcomes being measured, they report an average estimated
effect size of approximately 0.2σ for studies involving elementary school children.
Launched in the early 1990s, the Milwaukee Parental Choice Program is one of the oldest
publicly-funded voucher programs in the U.S. The program is open to low-income students who
are eligible to receive a voucher to attend any participating school (including religious schools)
worth approximately $6,501 in the 2007-2008 academic year. Nearly 19,000 students and 120
18
schools participated that year.
Early studies evaluating potential achievement impacts of the program were conducted
when the program had only been in operation for about four years and vouchers could only be
used at non-religious schools. At that time, about 12 schools and 800 students participated.
Because the participating schools in the program were required to take all students who applied
or to randomly select among applicants in the event of over-subscription, researchers had two
potential comparison groups: unsuccessful applicants and a random sample of low-income
students from the Milwaukee Public Schools. Using both comparison groups, Rouse (1998)
reports mixed results of the direct effect of the program. She estimates intent-to-treat effect sizes
in the yearly gain of being selected for the program ranging from 0.06 to 0.11σ in math and from
-0.03 to 0.03σ in reading, although the impacts in reading are never statistically different from
zero.8 The estimated yearly gain for those who actually use a voucher in math is 0.14σ while
that in reading is only 0.01σ (and not statistically different from zero).
Evidence from the Cleveland Scholarship and Tutoring Program (CSTP) suggests even
smaller impacts on student outcomes. This voucher program is open to all students living within
the boundaries of the Cleveland Metropolitan School District with preference given to students
8
The range reflects estimates from different model specifications. Other studies using
these early Milwaukee data include Witte et al. (1995), Witte (1997), and Greene et al. (1999).
Using only the sample of low-income students from the Milwaukee Public Schools as a
comparison group, Witte et al. (1995) and Witte (1997) estimate no impact of the program on
student achievement. Greene et al. (1999) only use the unsuccessful applicants as a comparison
group and estimate a positive impact in both math and reading. See Rouse (1998) for further
discussion of the differences between the studies.
19
in low-income families.9 Students are permitted to use the vouchers at both non-sectarian and
sectarian schools.
(The tutoring program provides tutors to interested students from
kindergarten through twelfth grade.) As vouchers are (theoretically) allocated using a lottery, the
CSTP program data allow researchers to identify two groups of applicants: voucher recipients
and non-recipients. Additionally, test scores and some longitudinal Cleveland Municipal School
District data are available for the first grade classmates of voucher recipients who did not use
their voucher as well as the first grade classmates of program applicants who did not use their
voucher or were not awarded a voucher, generating a (non-random) public school sample for
comparison (Metcalf 2001).
Table 1 shows estimates from the cohort of students who entered kindergarten in 1997.
The intent-to-treat estimates compare voucher winners to rejected applicants while the treatmenton-the-treated estimates compare voucher users to rejected applicants.
The specifications
include the student’s test score from the previous year such that the results reflect the one-year
change in test scores rather than the cumulative impact of the voucher program. After three years
(when the students were in 2nd grade), the test score gain for voucher recipients was significantly
lower in math and reading than for applicants who were not offered a voucher. The estimated
gains for voucher users were also negative and statistically significant. After five years (when
the students were in 4th grade), the gains for those offered a voucher were lower in math but
higher in reading than those for non-recipients, although neither impact is statistically different
9
The voucher is progressive in that it pays 90 percent of tuition up to $3,450 for those
with family income below 200 percent of the poverty line and 75 percent of tuition up to a
maximum of $3,450 for those from families earning above 200 percent of the poverty line. The
original program paid tuition up to a maximum of $2,250 (Metcalf et al. 1998).
20
from zero. Similarly, voucher users had lower gains than applicant/non-recipients in math but
higher gains in reading; again, neither impact is statistically different from zero.
While the studies from both Milwaukee and Cleveland attempt to construct valid
comparison groups to generate causal impacts of the programs on student outcomes, they rely on
observational data and therefore may be subject to omitted variables bias. In the case of
Milwaukee, the bias could either be positive (in that the students who participated in the program
were more motivated) or negative (in that the random sample of low-income students in the
public schools were too advantaged relative to the voucher participants). While Rouse (1998)
attempts to determine the extent of any such bias (and concludes it is likely minimal), it remains
an untestable assumption. Belfield (2007) is subject to the same general concern because he
does not observe the actual lotteries in which students participated and because the unsuccessful
applicants may be more advantaged than lottery winners since preference was given to lowincome families.10
This methodological concern can, in theory, be addressed with the relatively new D.C.
Opportunity Scholarship Program (DCOSP) in Washington, D.C. which is being evaluated using
10
The estimates would be biased if a student’s likelihood of winning a voucher varies
across lotteries and participation in a specific lottery is correlated with student characteristics that
also determine achievement. Further, it is not clear whether the non-recipient group also contains
students who were not entered into the lottery due to the preference given to students from lowincome families as suggested by Metcalf (2001). In personal email correspondence, evaluators
of the program believe these more economically advantaged students were always part of the
lottery. Finally, we note that Belfield (2007) includes some measures in his empirical
specifications – such as class size and teacher’s years of experience – that are arguably outcomes
of the voucher program; however, his results are robust to excluding these measures.
21
a random assignment program design.11 In the first two years of the program (spring 2004 and
2005), 2,038 eligible public school students participated in lotteries: 1,387 were awarded a
scholarship and the remaining 921 students became the control group. Wolf et al. (2007)
estimate that after one year, intent-to-treat effect sizes for the first two cohorts of students ranged
from -0.01 to 0.07σ in math and from -0.01 to 0.03σ in reading. After two years, Wolf et al.
(2008) report that the impacts ranged from -0.02 to 0.01σ in math and from 0.05 to 0.08σ in
reading. Not only do these ranges include negative impacts, but none are statistically different
from zero at the 5% level.
To date, the evidence from publicly-funded voucher programs suggests, at best, mixed
improvement among those students who were either selected for a voucher (the intent-to-treat) or
who used one (the treatment-on-the-treated). The largest estimates, from the Milwaukee Parental
Choice Program, suggest potential gains in the intent to treat of 0.11σ in math and gains of 0.14σ
for those who actually attend a private school; most of the other estimates are much smaller or
even negative. However, with the exception of the program in Washington, D.C., the studies
suffer from potentially unsatisfactory comparison groups. As such, we now turn to evidence
from the privately-funded programs.
Although a recent U.S. General Accounting Office (2002) report found 78 privatelyfunded voucher programs to review, only a handful have been subject to any evaluation. Three
privately-funded voucher programs – New York City; Dayton, OH; and Washington, D.C. – had
11
See Wolf et al. (2007, 2008) for more details. Students attending low-performing
public schools were given a better chance of winning the lottery. Although private school
students were eligible for the vouchers, they were excluded from the evaluation.
22
randomized study designs making them the best-suited for rigorous evaluation. As in the
DCOSP, each program had greater numbers of applicants than vouchers available so applicants
could be randomly selected to receive a voucher offer. In New York City, the number of
applicants was so large that the “control” group is comprised of a sample of applicants not
selected to receive a voucher.
As shown in Table 2, both Mayer et al. (2002) and Krueger & Zhu (2004) report small,
statistically insignificant impacts of offering vouchers when analyzing all students. Further, after
three years the estimated impact of attending a private school is at most 0.05σ, although even this
estimate (for the New York City program) is not statistically different from zero.
A widely publicized result from these programs is that there may have been differences
across subgroups of students. Indeed, Howell & Peterson (2002) and Mayer et al. (2002) report
statistically significant positive effects of private school attendance on test scores for African
American students alone (See Table 2). For New York City and Washington, D.C. combined,
after three years African American students who used a voucher are estimated to have
experienced a 0.23σ gain in achievement; those in New York City are estimated to have gained
0.26σ.
(In contrast, Howell et al. (2002) estimate a negative impact for African American
students after three years in Washington, D.C. although the impact is not statistically significant
from zero.)
However, the estimated positive impact on African American students is not robust. In
reanalyzing the data from New York City, Krueger & Zhu (2004) report that the results by race
are particularly sensitive to two analytical decisions. First, Krueger & Zhu (2004) include all
students, whereas Mayer et al. (2002) include baseline test scores in all of their specifications
23
leading them to exclude all students missing baseline test score information, most of whom are
first grade students who were not administered a baseline test. As noted earlier, because students
were randomly chosen to receive or not receive a voucher, baseline characteristics such as test
scores should have been identical for the two groups, on average. The primary reason for
including baseline characteristics is to improve the precision of the estimates. However, Krueger
& Zhu (2004) find very little difference in the precision of the estimated impact of vouchers
using a larger sample excluding baseline test scores compared to using the smaller sample with
baseline test scores. As a result, they argue that the gain in terms of statistical precision is not
large enough to warrant the cost of not generating estimates that are representative of the original
target population.
The second substantive difference between the studies is how the researchers identify a
student’s race. Mayer et al. (2002) identify a student as African American if the mother’s race is
reported as African American (non-Hispanic) irrespective of the race or ethnicity of the father.
Krueger & Zhu (2004) use alternative identifications such as whether either parent is African
American (non-Hispanic) or including the group of students whose parents responded “Other” to
the survey, but indicated they (the parents) were Black in the open-ended response. With the
larger sample and the broadest identification of students as African American, they report that
the estimated intent-to-treat impact falls to 0.05σ after three years and the estimated treatment on
the treated impact falls to 0.03σ.
In sum, there is little evidence of overall improvement in test scores for students offered
an education voucher from privately-funded voucher programs. Although there is some evidence
that African American students benefit from being offered a voucher in the New York City
24
study, the evidence is not robust to sensible alternative ways of constructing the analysis sample.
Do Students Who Remain in Public Schools Benefit?
The voucher studies discussed above are based on relatively small voucher programs
where there was unlikely a sufficient increase in competitive pressure to elicit a public sector
response. The estimates, therefore, reflect the direct effect of vouchers for those offered or using
them. Researchers have attempted to glean whether public school students would potentially
benefit from a large-scale program using evidence from two existing publicly-funded voucher
programs.
When the experimental phase of the Milwaukee Parental Choice Program ended in 1995,
the program was expanded to allow for a maximum of 15% of the public school enrollment.
Further, the Wisconsin Supreme Court ruled in 1998 that the vouchers could be used in religious
schools as well. These two events led to a dramatic increase in program participation by both
students and schools. In fact, the program was so popular that participation was expanded to a
maximum of 22,500 voucher students in 2006. Researchers have attempted to analyze these last
two expansions to estimate the potential impact of a large-scale voucher program on student
achievement in the public sector (see Hoxby (2003), Carnoy et al. (2007), and Chakrabarti
(2008)). While some of the details differ, the basic strategy of all three studies is to attempt to
identify those schools within the Milwaukee Public School District that face more or less
competitive pressure due to the income-level of the students (Those schools with a high
proportion of low-income students who are eligible for the voucher program presumably face
more competitive pressure than those with a low proportion of low-income students.), as well as
25
to identify observably comparable districts elsewhere in Wisconsin. Disproportionate gains
among students attending schools within Milwaukee facing competitive pressure compared to
schools within Milwaukee facing little pressure and districts outside of Milwaukee facing no
voucher pressure would be evidence of a positive impact of competition on school efficiency (as
reflected in student test scores).
As summarized in table 3, all three studies find evidence that with the expansion of the
voucher program in 1998, student performance improved in the first few years, especially in
schools that were most likely to be affected by the increased competition. For example, Hoxby
(2003) estimates that the 4th grade test scores of students attending schools likely facing the most
competitive pressure improved by 0.12σ per year in math and by 0.11σ per year in language
relative to students attending comparison schools outside of Milwaukee.
While interesting, these results must be interpreted as suggestive. First, the identifying
assumption is that there are no unobserved changes from before to after the voucher program
between the “treated schools” and the “comparison” schools.
While certainly possible, it
remains a strong identifying assumption, especially since within the Milwaukee Public School
District all schools were potentially “treated” and outside of Milwaukee the demographic
composition of the schools is quite different (specifically the students come from wealthier
families and are less likely to be minorities). Second, Carnoy et al. (2007) present additional
results that are not consistent with a simple interpretation that performance in the Milwaukee
Public Schools improved due to increased competition.
For example, as evidenced by a
comparison of rows (2) and (3) in table 3, they find there was no additional improvement after
2002 despite the fact that interest in the voucher program increased (as proxied by the number of
26
applications). Further, they find no evidence of a general equilibrium impact when they employ
other direct measures of competition: there are no positive achievement gains for students as the
number of nearby voucher schools increases or as the number of applications from a school
increases (rows (4) and (5) of table 3).12
In order for a voucher program to spur improvement within the public schools, there need
not be a substantial number (or proportion) of students who use a voucher to attend a private
school. Rather, if public school administrators perceive there is a threat that the students will do
so, they may have an incentive to respond by improving school quality. Thus, an alternative way
to gain insight into the potential response of public schools to increased competitive pressure is
to study the schooling outcomes of students attending schools that were under the threat of
becoming voucher-eligible. Researchers have done this by taking advantage of the design of
Florida’s school accountability system: Florida’s A+ Plan for Education. Specifically, since
1999 schools in Florida are given a grade of A-F largely dependent on the performance of the
students.
Schools receiving high grades or improving scores receive bonuses, while low
performing schools (graded either “D” or “F”) are subject to increased administrative oversight
and are provided with additional financial assistance. Further, if a school received an “F” in two
out of four years and has an “F” in the current year, students become eligible for vouchers called
Opportunity Scholarships.13 While other features of the A+ Plan remain in effect, the voucher
12
Their results are quite similar when they limit the analysis to predominantly African
American schools.
13
Currently Florida has two other voucher programs as well: an income tax credit for
corporations to fund vouchers for low-income students and the McKay Scholarship for students
27
program was declared unconstitutional by the Florida Supreme Court in January 2006.
Thereafter students could no longer use a voucher to attend a participating private school, but
could still use a voucher to attend a higher-graded public school.
Under the Florida A+ Plan, school grades are determined by assigning “grade points”
based on student test score performance.14 Grades are then assigned based on whether the school
is above or below the pre-determined cut points for each of the letter grades. Arguably, schools
receiving just enough grade points to earn a grade of “D” are no different than schools earning
just below the number of grade points needed to earn a grade of “D.” As a result, the schools
that received an “F” grade are quite similar to those that received a “D” grade along many
dimensions. Figlio & Rouse (2006), West & Peterson (2006), Chiang (2008), and Rouse et al.
(2007) therefore compare student outcomes from schools earning “D” and “F” grades while
controlling for the number of grade points earned in an effort to recover the causal effect of the
policy on educational achievement.
All of the papers find that the test scores of students improve following a school’s receipt
of an “F” grade. For example, as shown in table 4, Chiang (2008) and Rouse et al. (2007) report
one-year gains ranging from 0.12 to 0.21σ in math and from 0.11 to 0.14σ in reading. Further,
Chiang (2008) and Rouse et al. (2007) find evidence that the improvements persist for at least
with disabilities. Greene & Winters (2008) study the impact of the McKay Scholarships on the
achievement gains of students with disabilities who remain in the public schools. Because their
estimation strategy identifies the general effect of vouchers using students whose disability status
changes, it is unclear the extent to which these results generalize to overall improvements in the
public schools.
14
Literally speaking, school grades were not assigned using grade points before 2002
when Figlio & Rouse (2006) study the system. Nevertheless, their strategy is similar in spirit.
28
three years, even once the students leave the voucher-threatened school.15 As such, these studies
may provide some evidence that increased competitive pressure can generate improvement in
public schools.16
However, the F-graded schools in Florida were also stigmatized as “failing” (one of the
intents of the public announcements of the grades). As such, one cannot strictly identify a
“voucher effect” from a “stigma effect” where under a stigma effect the school administrators
and teachers are not motivated to improve because of perceived increased competition, but
because the label “failing school” generates a significant loss of utility.17 Figlio & Rouse (2006)
indirectly assess the impact of stigma by comparing student achievement following the
implementation of the A+ Plan (which enlisted both the threat of vouchers and stigma ) with
student achievement following the placement of schools on a critically low performers list in
1996, 1997, and 1998 that involved public stigma, but no threat of vouchers. They estimate that
15
In addition, Rouse et al. (2007) report finding evidence that the F-graded schools
responded in educationally-meaningful ways. For example, following receipt of an F-grade,
schools were more likely to focus on low-performing students, lengthen the amount of time
devoted to instruction, and increase resources available to teachers.
16
A statistical issue with which all of the authors wrestle is whether the disproportionate
gains by students in the F-graded schools was due to mean-reverting measurement error or
reflected actual changes in response to the A+ Plan. Mean-reverting measurement error occurs
when gains the year after a school scores unusually low – and is thereby labeled as “F” – reflect
the measurement error in test scores. That is, the test scores of students might have increased in
many of the “F” schools even in the absence of the A+ Plan simply because they were
transitorily low in the prior year. The reliance on a regression discontinuity design helps to
mitigate against the presence of mean-reverting measurement error, although the authors employ
other strategies as well.
17
Given that school principals and teachers have chosen their profession out of a desire
to teach children, such a loss of utility might stem from loss of “identity utility” (Akerlof &
Kranton 2005, 2007) or out of fear of loss of standing in the wider community.
29
the student gains in reading were nearly identical under the two regimes and were actually larger
in math following placement on the critically low performers list, suggesting that the relative
improvements among the low-performing schools may have been due more to stigma than to the
threat of vouchers.
In sum, while the expansion of the Milwaukee Parental Choice Program and the threat of
vouchers created by the Florida A+ Plan provide some evidence that student achievement
improves in schools facing increased competition, the research strategies do not allow one to rule
out other explanations for the improvements. As such, we conclude there is no conclusive
support for the potential for vouchers to spur public schools to improve.
Do Students Benefit from Other Forms of School Choice?
As noted previously, school vouchers are not the only mechanism for broadening the
publicly-funded schooling choices available to families. School districts have operated magnet
schools and implemented open enrollment plans for decades, and more recently, families have
had the option of charter schools as well. As such, estimates of the effects of other forms of
choice on student achievement may provide additional evidence on the potential gains from
private school vouchers. While a full review of the evidence from these other forms of school
choice is beyond the scope of this paper, we briefly review some of it.
Charter schools are probably the closest analog within the public sector to private
schools. While their administrative organization and regulation varies tremendously from state
to state, they are publicly funded and typically have more autonomy than traditional public
schools. Importantly, children are not assigned to attend charter schools – they only attend
30
through the active choice of their parents. As a way of increasing choice within the public
sector, they have become increasingly popular: while there were only two charter schools in
operation in the U.S. in 1992 (Bettinger 2005), by 2007 approximately 1,200,000 students
attended over 4,100 such schools (http://edreform.com).
Not surprisingly, researchers have begun to find ways to evaluate whether charter schools
generate better student outcomes than traditional public schools. Constrained by a dearth of data
on individual students, early studies usually relied on test scores at the school level – often from
Michigan, an early adopter of charter schools (see, e.g., Eberts & Hollenbeck 2002, Bettinger
2005). These papers typically find that the achievement of students in charter schools is no
greater than that in traditional public schools. Clearly a challenge with school-level data,
however, is in accounting for the characteristics of the students taking the exam. As a result,
more recent studies have been based on student-level data using two general approaches.
The first approach has been to use state-wide student-level data (available from Florida,
North Carolina, and Texas) and to control for time-invariant student characteristics using
individual-level fixed effects (see Sass 2006, Bifulco & Ladd 2006, and Hanushek et al. 2007).
These studies identify the effect of charter schools by comparing a student’s achievement in a
charter school to his or her achievement in a traditional public school. If there are time-varying
differences between students (which there could be since, for example, students might decide to
change schools because they started to do poorly in their original school) then the estimates will
be biased. That said, all three papers estimate slight negative impacts of charter schools on
student achievement gains. There is some evidence, however, that the negative impacts decrease
the longer the charter school has been in operation such that after 4-5 years students in charter
31
schools have similar achievement gains to those in traditional public schools.
A second approach takes advantage of the fact that most charter schools must admit all
students who apply or hold a lottery if oversubscribed. These lotteries therefore mimic a random
assignment design. Hoxby & Rockoff (2004) and Hoxby & Murarka (2007) implement this
design using data from Chicago and New York City. The results are mixed: the evidence from
Chicago suggests no overall gains for students attending charter schools while that from New
York City suggests small yearly test score gains. Overall the weight of the evidence thus far
does not suggest that charter schools are much more effective than traditional public schools;
however, these schools are relatively new and their effectiveness may improve with age.
Open enrollment or district-wide school choice – in which students are not assigned to
their neighborhood school, but can choose a school within the district – provides another way to
generate evidence on whether student achievement improves when students actively choose.18 In
these systems, students typically rank a number of schools and then are matched to schools
according to an algorithm. While certain preferences may be built into the selection process –
such as for siblings and proximity – these systems often include a lottery. Several recent papers
take advantage of the fact that some students are randomly allocated to their school of choice to
estimate whether the achievement of lottery “winners” improves relative to the achievement of
those who “lose” the lottery.
18
For example, Cullen et al. (2006) and Cullen & Jacob (2007)
Magnet schools are another form of choice within public schools, however their typical
administration does not lend itself to rigorous analysis. In many districts, magnet schools
specialize in a particular subject (e.g., music, science, computers, foreign language) and the
schools are not obligated to randomly select students if oversubscribed. As such, it is difficult to
obtain statistically unbiased estimates of their effectiveness.
32
exploit randomized lotteries among high schools and elementary schools in the Chicago Public
School District and find no overall improvement in academic achievement among lottery
winners compared to lottery losers. Similarly, Hastings et al. (2006) study the introduction of
open enrollment in the Charlotte-Mecklenburg Public School District and also report no overall
gains among lottery winners.19
Other sources of choice also provide some evidence on the potential for competition to
improve public schools. As noted earlier, perhaps the largest potential source of competition
between public schools arises because school quality already factors heavily into residential
choices. While there is no direct evidence on whether public schools respond to such choice,
Hoxby (2000, 2007) attempt to assess whether public school students in metropolitan areas
where there are many school districts (and hence much residential choice) perform better than
public school students in metropolitan areas where there are fewer school districts. Because the
size of school districts may be endogenous, she employs an instrumental variables strategy using
the number of rivers in the metropolitan area as an instrument for the concentration of districts in
an area. While Hoxby (2000, 2007) concludes that competitive pressure, indeed, improves
public school student achievement, Rothstein (2007) finds that her results are sensitive to the
manner in which the instrumental variable is constructed.
The rapid growth of charter schools provides another means of studying the potential
impact of competition on traditional public schools. Bettinger (2005), Bilfulco & Ladd (2006),
19
Using a structural model to identify parental preferences, Hastings et al. (2006)
conclude that academically-oriented families benefit from school choice. Hastings and
Weinstein (forthcoming) also reach this conclusion based on a randomized experiment in which
they manipulated the presentation of information available to parents on school test scores.
33
and Sass (2006) attempt to estimate whether an increase in the number of charter schools near
traditional public schools improves the achievement of students in the traditional public schools.
Bettinger (2005) and Bilfulco and Ladd (2006) find no evidence that the achievement of students
who remain in the nearby traditional public schools improves with the presence of charter
schools, although Sass (2006) finds some evidence for improvement in math achievement.20
Overall, other forms of school choice do not provide strong evidence that students who
exercise their choice experience achievement gains. Further, the weight of the evidence suggests
that these other forms of school choice do not induce public schools to improve either. That
said, the research on charter schools, in particular, is relatively new (as is the sector); as the
schools mature and become more established within communities both their effectiveness and
their “threat” to the local public schools as a viable alternative may increase.
Might School Vouchers be a Cost-Neutral Way to Increase Social Welfare?
While the literature on achievement gains does not find wholesale improvement from
voucher programs, vouchers may nonetheless make sense from a cost-benefit perspective,
particularly if one broadens the potential criteria on which to judge them. First, one might
support vouchers as a way of promoting greater equity by providing poor families more
opportunities for opting out of the public system – such as those currently enjoyed by wealthier
20
Bettinger (2005) attempts to account for the fact that the location of charter schools
may not be exogenous by taking advantage of institutional details in the development of such
schools in Michigan. Both Bilfulco & Ladd (2006) and Sass (2006) attempt to do so by
including fixed effects that reflect student enrollment spells in a particular school (such that the
impact of the local competition is identified by comparing students in the same school as the
level of competition changes).
34
families. Second, one consistent finding in the literature is that voucher parents report being
more satisfied with their current schooling than non-voucher parents. For example, in the
DCOSP parents of students offered a voucher gave their child’s school a significantly higher
overall grade on a five-point scale (grades “A” through “F”) and were significantly more likely
to give their child’s school a grade of “A” or “B.” Further, they reported significantly greater
satisfaction with their child’s school on all dimensions asked, including location, class sizes,
discipline, academic quality, and the racial mix of the students (Wolf et al. 2007). These results
have also generally been reported for other voucher programs such as those in New York City
(Mayer et al. 2002) and Milwaukee (Witte et al. 1995).21
If one considers gains in equity and increased parental satisfaction, then introducing
vouchers could increase social welfare if vouchers are no more expensive than our current
system of public education. This potential net improvement in social welfare depends on both the
general equilibrium effects of vouchers and the cost advantage over current public schools, two
issues that are not well understood. While small-scale voucher programs indicate that parents
offered a voucher are more satisfied with their child’s school than those not offered a voucher, a
large scale voucher program might generate some parents who are more satisfied and some who
21
At the same time, not all parents are satisfied with the voucher schools. Focus groups
from DCOSP participants found that parents believed a few schools misrepresented aspects of
their program and that there was a need for an evaluation of participating schools (Stewart et al.
2007). Similarly, in the early years of the Milwaukee Parental Choice Program, 43% of the
parents who took their children out of the voucher schools cited the quality of the voucher school
as one of the primary reasons for withdrawal; including being unhappy with the staff, the
education their child was receiving, a lack of programs for special needs, and that the teachers
were too disciplinarian. Thirty percent cited the quality of the program, including hidden school
fees, difficulties with transportation, and the limitation on religious instruction (Witte et al.
1995).
35
are less satisfied.
In order for social welfare to be increased with a cost-neutral voucher
program, the benefits to the parents made better off must be large enough to outweigh the losses
to parents made worse off.
Additionally, it is not clear that a well-developed voucher program would be cost-neutral.
On its face an education voucher system should be no more expensive than the current system as
the state (or other public entity) would simply send a voucher check to schools for each
participating child rather than to the local public school or district. However, if implemented on
a large scale, there may be other, less appreciated costs that would depend critically on the
design of the program. Levin & Driver (1997) caution that depending on how a program deals
with students currently attending private schools, the transportation of children to and from
school, record keeping and monitoring of student enrollment, and the process of adjudicating
disputes (particularly if there are differing voucher amounts), the cost of a voucher system could
actually exceed those of the current geographically-based system. While their estimates are
rough – based on hypothetical voucher programs and crudely estimated costs – their analysis
suggests, at a minimum, that we should not assume a voucher program would be cost-neutral.
Further, there may be large costs associated with the transition to a voucher system that should
be considered.
Why has it been so difficult to observe large improvements in student achievement?
Why might vouchers (or competition in general) not generate large improvements in
student achievement? One explanation may be that the public sector is not as inefficient as many
perceive because schools already compete for students through residential choice (see, e.g.,
36
Barrow & Rouse 2004). Another explanation may be that the education sector does not meet the
conditions for perfect competition to result in an efficient outcome (Garner & Hannaway 1982).
For one, information on school quality may be costly and difficult for parents to obtain.
Obviously, any potential academic gains from additional choice cannot be realized if consumers
do not have the information on which to make informed decisions. Further, education is not a
homogenous good. While competition for students may make schools more responsive to
parents, this may be achieved through changes in other dimensions, such as religious education
or nicer gymnasiums, rather than academic achievement. A growing literature is attempting to
understand what kind of information is available to parents or conversely, whether one can
improve it or make it more transparent (see, e.g., Hastings & Weinstein, forthcoming).
Similarly, several recent studies have attempted to better understand the extent to which parents
– particularly low-income parents who would most likely be offered school vouchers – factor a
school’s academic quality into their decision-making process (Hanushek et al. 2007; Hastings et
al. 2005, 2006; Hastings & Weinstein forthcoming; and Jacob & Lefgren 2007). Unfortunately,
the findings are mixed.
In addition, the studies to date necessarily focus on the short-run effects of vouchers
when, in fact, there may be longer-run impacts on high school graduation, college enrollment, or
even future earnings. For example, Altonji et al. (2005b) study the effect of Catholic education
on a variety of outcomes and find little evidence that Catholic schools raise student test scores.
At the same time, their results suggest that Catholic schools increase the probability of
graduating from high school and potentially the probability of enrolling in college. These longerrun effects have yet to be credibly examined in studies of school vouchers.
37
CONCLUSION
Milton Friedman’s dream of a publicly-funded – but not necessarily publicly-provided –
school system where parents have a choice of many different schools for their children has never
been tested in the U.S. And yet, its theoretical appeal has led to several, mostly small-scale,
attempts to determine whether students might benefit from such a reform. Unfortunately, results
from these small programs cannot test Friedman’s hypotheses. The most credible evidence
comes from studies focused on the short-run academic gains for students who use vouchers. As
a result, many questions remain about the potential long-run impacts on academic outcomes and
about both the public and private sector responses to a large, permanent, and well-funded
voucher program.
Keeping these limitations in mind, the best research to date finds relatively small
achievement gains for students offered education vouchers, most of which are not statistically
different from zero. Further, what little evidence exists about the likely impact of a large-scale
voucher program on the students who remain in the public schools is at best mixed, and the
research designs of these studies do not necessarily allow the researchers to attribute any
observed positive gains solely to school vouchers and competitive forces. The evidence to date
from other forms of school choice is not much more promising. As such, while there may be
other reasons to implement school voucher programs, one should not anticipate large academic
gains from this seemingly inexpensive reform.
38
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Table 1: Estimated test score impacts of publicly-financed voucher programs
Voucher Program
Notes
Math
Reading
ITT
TT
ITT
TT
Milwaukee Parental Choice
Program from Rouse (1998)
Annual test score growth of students
in grades K-8 selected to receive a
voucher relative to unsuccessful
applicants and low-income students
in Milwaukee Public Schools; with
and without student fixed effects.
0.06* to
0.11**
0.14**
-0.03 to 0.03
0.01
Cleveland Scholarship and Tutoring
Program from Belfield (2007)
Grade 2 test score gains of students
selected to receive a voucher
relative to unsuccessful applicants.
-0.11**
-0.11**
-0.13**
-0.13**
Cleveland Scholarship and Tutoring
Program from Belfield (2007)
Grade 4 test score gains of students
selected to receive a voucher
relative to unsuccessful applicants.
-0.02
-0.08
0.04
0.07
D.C. Opportunity Scholarship
Program from Wolf et al. (2007)
Randomized experiment comparing
lottery winners in grades K-12 to
non-recipients in the first year.
-0.01 to
0.07*
-0.01 to 0.03
D.C. Opportunity Scholarship
Program from Wolf et al. (2008)
Randomized experiment comparing
lottery winners in grades K-12 to
non-recipients in the second year.
-0.02 to 0.01
0.05 to 0.08*
Notes: Reported estimates have been converted to effect sizes in national standard deviation units. Estimates from Rouse
(2008) are from Table VI col. (1) and Table Va col. (2) for math and from Table Vb cols. (7)-(8) for reading. Clive Belfield
generously provided the intent-to-treat estimates for Cleveland reported above as well as within sample standard deviation
information used to convert effect sizes to those based on national standard deviation units from CTB/McGraw-Hill, 2001.
Estimates of the effect of treatment-on-the-treated come from Belfield (2007) Table 3, panel C, col. (1) and (2) and Table 6,
panel C, col. (1) and (2). Estimates from Wolf et al. (2007) are from Tables H-1 and H-2, Full sample; those from Wolf et
al. (2008) are from Tables D-1 and D-2, Full sample. For D.C. we use the average national standard deviation over grades
K through 12 reported in Stanford Achievement Test Series (1996) along with those reported in Wolf, et al. (2007) to
convert effect sizes. ITT is "Intent-to-Treat" and TT is "Treatment-on-the-Treated." Statistical significance levels are
reported as: *** = 1 percent; ** = 5 percent; * = 10 percent.
45
Table 2: Estimated test score impacts for privately-financed voucher programs after three years
Study
Voucher Program
Mayer, et al. (2002)
New York City
Krueger & Zhu (2004)
New York City
Howell & Peterson (2002)
Two-city average
Notes
Randomized experiment
comparing lottery winners
and voucher users to nonrecipients. TT estimates
reflect the gains to
attending private school for
at least one year.
Randomized experiment
comparing lottery winners
and users to nonrecipients. TT estimates
reflect the gains to an
additional year in private
school.
Randomized experiment
comparing voucher users
to non-recipients.
Estimates reflect the gains
to attending private school
for at least one year.
All Students
ITT
TT
African American Students
ITT
TT
0.03
0.05
0.19***
0.26***
-0.01 to 0.01
0.00
0.05
0.03
0.02
0.23***
Notes: The two-city average is for New York City and Washington, D.C. National percentile rank impacts were converted to
effect sizes in national standard deviation units using a standard deviation of 28.5. Estimates for Mayer, et al. (2002) come from
Table 20, col. (3) and (6). ITT estimates from Krueger & Zhu (2004) are from Tables 4 and 5, Third follow-up test (using the
broadest definition of African American); TT estimates are from Table 6, Third follow-up test (using the broadest definition of
African American). Howell & Peterson (2002) estimates are from Table 6-1, Year III. ITT is "Intent-to-Treat" and TT is
"Treatment-on-the-Treated."
Statistical significance levels are reported as: *** = 1 percent; ** = 5 percent; * = 10 percent.
46
Table 3: Estimated test score impacts from expansion of the Milwaukee voucher program
Study
(1)
Hoxby (2003)
(2)
Carnoy et al. (2007)
(3)
Carnoy et al. (2007)
(4)
Carnoy et al. (2007)
(5)
Carnoy et al. (2007)
Notes
Annual test score growth of students in mosttreated schools relative to students in
untreated comparison schools (outside
Milwaukee).
Average program impact on test score gain of
students in lowest income schools relative to
students in comparison schools outside
Milwaukee.
Average program impact on test score gain of
students in lowest income schools relative to
students in comparison schools outside
Milwaukee.
Test score gains per voucher place within 1
mile/enrollment in 2001-02.
Test score gains per average voucher
application/enrollment 1998-2001.
Chakrabarti (2008)
Program impact on test scores of more
treated schools relative to comparison
schools outside Milwaukee.
(6)
Time period
Math
Language
1996-97 to 1999-2000
0.12
**
0.11
**
1998-99 to 2001-02
0.22
**
0.16
**
1998-99 to 2004-05
0.22
**
0.16
**
2001-02
-0.04
-0.01
2001-02
-0.12
-1.54
2001-02
0.15
**
0.24
***
Notes: All estimates apply to test scores for students in the 4th grade. Estimates from Hoxby (2003) are derived from Table
8.8 and are converted to standard deviation units using the national percentile rank standard deviation of 28.5. Estimates from
Carnoy et al. (2007) come from Tables 3 and 9. Table 3 estimates are converted to standard deviation unites using the national
Terra Nova standard deviations for 4th grade of 39.32 in math and 36.27 in language. Table 9 estimates are converted to
standard deviation units using the normal curve equivalent standard deviation of 21.05. Estimates from Chakrabarti (2008)
come from Table 12, Panel C, and are converted to national standard deviation units using within sample standard deviations
reported and the national standard deviation of 21.06 for normal curve equivalent scores.
Statistical significance levels are reported as: *** = 1 percent; ** = 5 percent.
47
Table 4: Estimated test score impacts of receipt of "F" grade from Florida's A+ Plan for Education
Study
Notes
Math
Year 1
Reading
Year 3
Year 1
Year 3
Rouse et al (2007)
Regression discontinuity estimates
reflecting the impact of receiving an
"F" grade (controls for school fixed
effects).
0.212***
0.118***
0.140***
0.088***
Chiang (2008)
Regression discontinuity estimates
reflecting the impact of receiving an
"F" grade (Year 3 estimates control
for observable school
characteristics).
0.118**
0.084*
0.112**
0.030
Notes: All estimates based on the FCAT Reading and Math ("high-stakes") tests. Estimates from Rouse et al.
(2007) come from Table 4 rows labeled "2002-03 cohort compared with 2001-02 cohort" in 1st and 2nd panels.
Chiang (2008) estimates come from Tables 6 and 7 rows labeled "All accountable students" including middle school
controls (for the Year 3 estimates). All coefficients have been normalized by the standard deviation of test scores of
students in Florida by grade.
Statistical significance levels are reported as: *** = 1 percent; ** = 5 percent; * = 10 percent.
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WP-07-13
Labor Market Transitions and Self-Employment
Ellen R. Rissman
WP-07-14
First-Time Home Buyers and Residential Investment Volatility
Jonas D.M. Fisher and Martin Gervais
WP-07-15
Establishments Dynamics and Matching Frictions in Classical Competitive Equilibrium
Marcelo Veracierto
WP-07-16
Technology’s Edge: The Educational Benefits of Computer-Aided Instruction
Lisa Barrow, Lisa Markman, and Cecilia Elena Rouse
WP-07-17
The Widow’s Offering: Inheritance, Family Structure, and the Charitable Gifts of Women
Leslie McGranahan
WP-07-18
Demand Volatility and the Lag between the Growth of Temporary
and Permanent Employment
Sainan Jin, Yukako Ono, and Qinghua Zhang
WP-07-19
A Conversation with 590 Nascent Entrepreneurs
Jeffrey R. Campbell and Mariacristina De Nardi
WP-07-20
Cyclical Dumping and US Antidumping Protection: 1980-2001
Meredith A. Crowley
WP-07-21
The Effects of Maternal Fasting During Ramadan on Birth and Adult Outcomes
Douglas Almond and Bhashkar Mazumder
WP-07-22
5
Working Paper Series (continued)
The Consumption Response to Minimum Wage Increases
Daniel Aaronson, Sumit Agarwal, and Eric French
WP-07-23
The Impact of Mexican Immigrants on U.S. Wage Structure
Maude Toussaint-Comeau
WP-07-24
A Leverage-based Model of Speculative Bubbles
Gadi Barlevy
WP-08-01
Displacement, Asymmetric Information and Heterogeneous Human Capital
Luojia Hu and Christopher Taber
WP-08-02
BankCaR (Bank Capital-at-Risk): A credit risk model for US commercial bank charge-offs
Jon Frye and Eduard Pelz
WP-08-03
Bank Lending, Financing Constraints and SME Investment
Santiago Carbó-Valverde, Francisco Rodríguez-Fernández, and Gregory F. Udell
WP-08-04
Global Inflation
Matteo Ciccarelli and Benoît Mojon
WP-08-05
Scale and the Origins of Structural Change
Francisco J. Buera and Joseph P. Kaboski
WP-08-06
Inventories, Lumpy Trade, and Large Devaluations
George Alessandria, Joseph P. Kaboski, and Virgiliu Midrigan
WP-08-07
School Vouchers and Student Achievement: Recent Evidence, Remaining Questions
Cecilia Elena Rouse and Lisa Barrow
WP-08-08
6
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