NBER WORKING PAPER SERIES
THE LONG-TERM CONSEQUENCES OF FREE SCHOOL CHOICE
Victor Lavy
Working Paper 20843
http://www.nber.org/papers/w20843
NATIONAL BUREAU OF ECONOMIC RESEARCH
1050 Massachusetts Avenue
Cambridge, MA 02138
January 2015
Excellent research assistance was provided by Elior Cohen, Michal Hodor and Assaf Kott. I benefitted
from comments and suggestions from participants at the Bergen/UCL/Warwick 2015 Topics in Labor
Economics Workshop, the CESifo 2015 Conference on Economics of Education, The London Centre
for the Study of Market Reform of Education 2016 School Choice Conference, seminars at the Hebrew
University, the Ministry of Education in Madrid, Warwick University and from Gordon Dahl, David
Deming, Christian Dustman, Magne Mogstad, Steve Machin, Craig Riddell, Kjell Salvanes, Uta Schoenberg,
and Fabian Waldinger. I thank Israel’s National Insurance Institute (NII) for allowing restricted access
to post-secondary schooling and economic and social outcomes data at adulthood in the NII protected
research lab. I acknowledge financial support from the European Research Council through ERC Advance
Grant 323439, The Israel Science Foundation and the Falk Research Institute. The views expressed
herein are those of the author and do not necessarily reflect the views of the National Bureau of Economic
Research.
NBER working papers are circulated for discussion and comment purposes. They have not been peer-
reviewed or been subject to the review by the NBER Board of Directors that accompanies official
NBER publications.
© 2015 by Victor Lavy. All rights reserved. Short sections of text, not to exceed two paragraphs, may
be quoted without explicit permission provided that full credit, including © notice, is given to the source.
The Long-Term Consequences of Free School Choice
Victor Lavy
NBER Working Paper No. 20843
January 2015, Revised February 2017
JEL No. J24
ABSTRACT
I study the long-term consequences of what amounted to an effective free school choice program which
two decades ago targeted disadvantaged students in Israel. I show that the program led to significant
gains in post-secondary education, through increased enrollment in academic and teachers' colleges
but without any increase in enrollment in research universities. Free school choice increased also earnings
at adulthood of treated students. Male students had much larger improvements in college schooling
and labor market outcomes. Female students, however, experienced higher increases in marriage and
fertility rates, which most likely interfered with their schooling and labor market outcomes.
Victor Lavy
Department of Economics
University of Warwick
Coventry, CV4 7AL
United Kingdom
and Hebrew University of Jerusalem
and also NBER
A Data Appendix is available at http://www.nber.org/data-appendix/w20843
1
1. Introduction
The evaluation of educational programs and interventions has focused on short-term
outcomes, primarily standardized test scores, as a measure of success. However, understanding that
the purpose of education is to improve lifetime well-being, attention has shifted recently to long term
consequences at adulthood. In light of the increasing economic returns to higher education, the initial
focus has been on post-secondary attainment (Heckman and LaFontaine 2010; Acemoglu and Autor
2010). Garces et al (2002), Ludwig and Miller (2007) and Deming (2009) studied the long-term
benefits of Head Start; Schweinhart et al (2005) examined the long term effect of the Perry Preschool
program; Chetty et al (2011) studied the effect of kindergarten classroom on earnings in early
adulthood; Dustmann et al (2012) examined the effect of high school quality on completed schooling
and labor-market outcomes; Dynarski et al (2013) examined the effect of smaller classes in primary
school on college entry, college choice, and degree completion; Deming et al (2013) studied the
impact of accountability pressure in high schools on post-secondary attainment and earnings; Chetty
et al (2014) examined the earnings consequences of primary and middle school teacher quality; and
Deming, Billings, and Rockoff (2014) studied the impact of the end of race-based busing on college
attainment and young adult crime.
The common goal of these studies is to determine which interventions are more effective in
improving long-term outcomes, but the scope of educational interventions studied is still limited, and
much remains to be unraveled. In this paper I study the long term consequences of free school choice
offered to primary school students at the point of transition to secondary schools. The main question I
address here is whether the effects of free school choice persist beyond attainment and test scores in
high school, and lead to long-term enhancements to human capital and well-being. I do so using a
school choice experiment which was conducted two decades ago in the city of Tel Aviv, Israel. The
program had positive short and medium-term effects on cognitive outcomes and schooling attainment
during middle and high school and improved students’ social skills (Lavy 2010). In this paper I study
whether the free school choice among public schools had long-term effects on social and economic
outcomes. This paper provides the first evidence of links between school choice, students’
employment and earnings, and social outcomes at adulthood. I examine the impact on various types of
post-secondary schooling that vary by quality, on employment, and on earnings at 11-13 years after
high school graduation, almost two decades after students were able to exercise free school choice.
I observe students' outcomes every year from high school graduation (2000-2001), until age
30-32 (in 2014). Thus, I can estimate the treatment effects for every year in the period, and trace the
dynamic evolution of the program effect. Since a high proportion of the sample was in military
service for two (female) or three (male) years after high school
1
, the estimates for these years (2000-
1
Israelis begin a period of compulsory military service after high-school graduation. Boys serve for three years
and girls for two (longer if they take a commission). Ultra-orthodox Jews are exempt from military service as
2
2004) are not very informative, because they are based on a small and selective sample of those
students not enlisted into military service. The evidence shows that the school choice had increased
post secondary schooling. Treated students are 4.6 percentage points more likely to enroll in post
secondary schooling, and complete almost an additional a fifth year of college in comparison to
students in the control group. These effect sizes reflect an 11 percent increase relative to pre-program
means and are similar in magnitude to the effect of the program on end of high school matriculation
outcomes. The increase in post-secondary schooling reflects mainly an increase in academic (as
opposed to vocational) education, through increased enrollment in academic and teachers’ colleges,
but without any increase in enrollment in research universities. This is not a surprising result, since
those affected by the program are marginal students from low socio-economic backgrounds who
would probably not enroll in any academic post secondary schooling if not for the school choice
program. It is important to note that these results are general equilibrium in nature, because those
affected by the experiment are a very small proportion of their cohort and therefore the expansion in
post-secondary schooling in the treated sample is not at the expense of others who could have been
‘crowded out’ by the new demand for higher education. Furthermore, these effects occurred during a
period of expansion of the supply of academic colleges in Israel. Otherwise, the concern of general
equilibrium effect will have to be addressed in a context of at scale implementation of such school
choice program. Alongside these gains in post-secondary schooling, average annual earnings among
treated students 11-13 years after high school graduation increased by 6-7 percent relative to the
control group mean. These gains are due to improvements in high school outcomes (matriculation
composite score, matriculation diploma, number of matriculation subjects at honor level) and in post
secondary schooling attainment, both of which are highly correlated with labor market earnings.
Finally, I find that the school choice program did not affect age of marriage and marriage rate but it
delayed by half a year the age of having the first child. However, this finding disguises large
heterogeneity in the effect on marital outcomes by gender, with significant effects on females and no
effect on males.
The lessons learned from this analysis are easily transferable and applicable to other
educational settings in developed countries. Both the high school system in Israel and its high-stakes
exit exams are very similar to those in other countries. Importantly, variants of the school choice
program studied here have been implemented in recent years in developed and developing countries.
Another important advantage of the evidence presented in this paper is that school choice can be
directly implemented as a public policy, while most recent studies of longer-term outcomes cover
measures that are not as easily influenced by policy, such as school or teacher quality.
There is little causal evidence on the long term effect of school choice even though it is a
controversial policy. The earlier studies on short term effects of school choice, for example Rouse
long as they are enrolled in seminary (Yeshiva); orthodox Jewish girls are exempt upon request; Arabs are
3
(1998) and Cullen, Jacob and Levitt (2006), were followed recently by studies looking at the long
term effects, in particular on misbehavior and crime (Deming 2011), and on post-secondary schooling
attainment (Demming et al 2013, Chingos and Peterson 2013, Wondratschek et al 2014). Demming et
al (2013) study the impact of the public school choice lottery in Charlotte-Mecklenburg schools and
find a significant overall increase in college attainment among lottery winners who attend their first-
choice school. Chingos and Peterson (2013) report on an experiment that offered a private-school
voucher to low-income families. Overall, this study reports no significant effects on college
enrollment of the voucher offer, but they estimate large significant impacts for African-American
students and smaller but not statistically significant impacts for Hispanic students. Wondratschek et al
(2014) study the short and long term effect of Sweden’s 1992 school choice reform, and find it had
very small positive effects on marks at the end of compulsory schooling, but it had zero effects on
university education, employment, criminal activity and health at age 25.
The remainder of the paper is as follows. In Section 2 I describe the Tel Aviv school choice
program, in section 3 I present the data and in section 4 I outline the identification and econometric
model. In Section 5 I present the results and in section 6 some conclusions.
2. Background
The analysis of the short and medium term effects, presented in Lavy (2010), indicated that
the Tel Aviv school choice program reduced the dropout rate from 7
th
to 12
th
grade by 7.3-8.4
percentage points (a 32 percent decline), increased the matriculation rate by 8 percentage points (a 25
percent increase), and increased the average score in the Bagrut exams by almost 7 points (a 12
percent increase). It also improved the quality of schooling as the number of Bagrut credit units
increased by 2 (a 11 percent increase), the number of credits in science subjects increased by one third
of a unit (a 13 percent increase), and the number of Bagrut subjects studied at honor level increased
by 0.3 (a 13 percent increase). I summarize below the main features of the Tel Aviv school choice
program and then examine whether these gains were translated into economically meaningful
improvements in adulthood.
The Tel-Aviv school-choice program
In May 1994, the Israeli Ministry of Education approved a two year trial of the Tel Aviv
School Choice Program (TASCP) in the 9th district (see Map 1 in online appendix). It was the first
choice program in the country since the 1968 education reform that enacted compulsory integration in
grades 7–9.
2
TASCP was a response to parents' dissatisfaction with students’ outcomes and with the
exempt, though some volunteer.
2
The 1968 reform established a three-tier structure of schooling: primary (grades 1–6), middle (7–9), and high
school (10–12). The reform established neighborhood school zoning as the basis of primary enrollment and of
the integration and busing of students out of their neighborhoods in middle school. In Tel-Aviv, most middle
schools were part of six-year high schools and there were several high schools that only offered the higher
grades (10
th
-12
th
).
4
rigid lack of school choice. Its objectives were to give disadvantaged students access to better schools,
facilitate a better match between students and schools, and motivate school productivity
improvements through competition. The 9th schooling district included 16 public primary schools -
12 secular and 4 religious. Until 1994 the graduates of five of these secular primary schools were
bused to one of 5 secondary schools in districts 1-5 in north Tel-Aviv (about 36 percent of the
districts’ pupils) and a few more of the districts' pupils (5 percent) were enrolled in charter schools
outside the district. The graduates of the seven other secular primary schools were assigned to one of
the three secondary schools within district 9.
3
In May 1994 the Tel-Aviv Education Board announced that as of September 1994 this system
would be replaced by free choice for the incoming 7th graders, while older cohorts in the district
would continue with the old system. The structure of choice was as follows. At the end of sixth grade
each student was asked to rank his preferences among the five schools in his choice set, which
consisted of the district's three secondary schools and two out of district schools (in districts 1-5
which were the same schools to which students were bused before the program). The choice set varied
among students in accordance with the primary school they attended. If there was excess demand for a
particular school, students were assigned to schools such that the socio-economic balance of the
district was maintained.
4
The city opened information centers and ran workshops for parents and
pupils, and high schools held open days to provide information about the choice program for the
incoming 7th grade cohort.
City reports indicate that in the program's first year, 90 percent of students received their first
choice and others the remaining 10% their second. In the second year the first choice rate was even
higher
5
, and since 2003 excess demand has been resolved by lottery. Another relevant factor was an
expansion of the supply of middle school classes: four high schools, two in district 9 and two in the
city’s northern districts, which had previously only offered the higher grades (10th-12th), were
expanded to offer middle school grades at the commencement of the reform. Despite these changes,
over time the choice program led to the expansion of some high schools and to the contraction of
others (one school was even closed due to declining enrollment). Enrollment in the city’s schools was
also affected by the stricter enforcement of the Ministry’s rule that pupils were not allowed to attend
schools outside of Tel Aviv. Because school budgets were determined according to enrollment,
schools that expanded enrollment gained more resources.
The choice program was accompanied by a decision that the city's post-primary schools
would have a six grade structure that includes the middle (7th-9th) and higher grades (10th-12th) as
part of the same school. In practice this allowed the city to cancel the admission process at the end of
3
These schools were located on the same campus but they were very different in terms of their curriculum and
programs offered to students. For example, one included low and high tech vocational schooling.
4
Siblings in the same school and school capacity were also used as criteria to balance enrollment.
5
The Tel-Aviv Educational Authority (1999).
5
the 9th grade and to introduce the concept of ‘persistence’, whereby students automatically enrolled in
the 10th grade in the school in which they completed their middle school education. This important
component of the reorganization of the school system in Tel Aviv strongly limited the ability of
schools to select students into their higher grades based on academic performance. The explicit
default became that pupils could remain in the school they chose in the 7th grade for the duration of
their secondary education. To overcome this default option, a school had to gain explicit approval
from a special city committee: consent was only given in cases where pupils displayed severe
behavioral problems and never on the grounds of poor academic performance. This policy change
most likely explains a large part of the dramatic decline in the pupil transfer rate in 9th grade, from
about 50 percent before the choice program to about 15 percent following it.
In 1996 the experiment was expanded to district 8, in 1998 to district 7, and in the following year to
the rest of the city (Tel-Aviv Educational Authority, 2001).
The Israeli high school system
When entering high school (10
th
grade), students choose whether to enroll in the academic or
non-academic track. Students enrolled in the academic track receive a matriculation certificate
(Bagrut) if they pass a series of national exams in core and elective subjects taken between 10
th
and
12
th
grade. Students choose to be tested at various proficiency levels, with each test awarding one to
five credit units per subject, depending on difficulty. Advanced level subjects are those subjects taken
at a level of four or five credit units; a minimum of 20 credit units is required to qualify for a Bagrut
certificate. About 52 percent of all high school seniors received a Bagrut in the 1999 and 2000 cohorts
(Israel Ministry of Education, 2001). The Bagrut is a prerequisite for university admission and
receiving it is an economically important educational milestone. For more details on the Israeli high
school system, see Abramitzky and Lavy (2014).
3. The Data
In this study I use data from administrative files for students in primary schools that were
enrolled into the school choice program, pre (sixth graders in 1992 and 1993) and post (sixth graders
in 1994) treatment cohorts, and similarly for the control schools, respective pre and post cohorts. The
students in the sample completed high school between 1999 and 2001, and in 2013 they are adults,
age 29-31. I use several panel datasets available from Israel’s National Insurance Institute (NII). The
NII is responsible for social security and mandatory health insurance in Israel. NII allows restricted
access to this data in their protected research lab. The underlying data sources include: (1) the
population registry data, which contains information on marital status, number of children and their
birth dates; (2) NII records of postsecondary enrollment from 2000 through 2013 based on annual
reports submitted to NII by all post-secondary education institutions, from which we calculated the
6
number of years of post-secondary schooling
6
; (3) Israel Tax Authority information on income and
earnings of employees and self-employed individuals for 2000-2014; (4) NII records on
unemployment benefits, marriage and fertility for the period 2009-2012. The NII linked these data to
students’ background data that I used in Lavy (2009) to study the effect of the teachers’ incentive
experiment on high school academic outcomes. This information comes from administrative records
of the Ministry of Education on the universe of Israeli primary schools during the 1997-2002 school
years. In addition to an individual identifier, and a school and class identifier, it also included the
following family-background variables: parental schooling, number of siblings, country of birth, date
of immigration if born outside of Israel, ethnicity and a variety of high school and high school
achievement measures. This file also included a treatment indicator, school ID and cohort of study. I
had restricted access to this data in the NII research lab at the NII headquarters in Jerusalem.
The post high school academic schooling system in Israel: The post high school academic
schooling system in Israel includes seven universities (one of which confers only graduate and PhD
degrees), and over 50 colleges that confer academic undergraduate degrees (some of these also give
master’s degrees).
7
All universities require a bagrut diploma for enrollment. Most academic colleges
also require a bagrut, though some look at specific bagrut diploma components without requiring full
certification. For a given field of study, it is typically more difficult to be admitted to a university than
to a college. The national university enrollment rates for the cohort of graduating seniors in 1995
(through 2003) was 27.6 percent and the rate for academic colleges was 8.5 percent.
8
The post-high school outcome variables of interest here are indicators of ever having enrolled
in a university and in an academic college as of the 2013 school year, and the number of years of
schooling completed in these two types of academic institutions by this date. We measure these two
outcomes for our 1999-2001 12
th
grade students. Even after accounting for compulsory military
service
9
, we expect that most students who enrolled in academic post-high school education, including
those who continued beyond the undergraduate level, to have graduated by the 2013 academic year.
Definitions of Outcomes in Adulthood: In this subsection, I describe the outcomes in
adulthood for students in the sample. To account for age differences of the different cohorts included
6
The NII, which is responsible for the mandatory health insurance tax in Israel, tracks postsecondary
enrollment because students pay a lower health insurance tax rate. Postsecondary schools are therefore required
to send a list of enrolled students to the NII every year. For the purposes of our project, the NII Research and
Planning Division constructed an extract containing the 2001–2013 enrollment status of students in our study.
7
A 1991 reform sharply increased the supply of postsecondary schooling in Israel by creating publicly funded
regional and professional colleges.
8
These data are from the Israel Central Bureau of Statistics, Report on Post-Secondary Schooling of High
School Graduates in 1989–1995 (available at:
http://www.cbs.gov.il/publications/h_education02/h_education_h.htm).
9
Boys serve for three years and girls for two (longer if they take a commission). Ultra-orthodox Jews are
exempt from military service as long as they are enrolled in seminary (Yeshiva); orthodox Jewish girls are
exempt upon request; Arabs are exempt, though some volunteer.
7
in the sample, the post-secondary schooling outcomes are also adjusted for years since graduating
high school.
Labor Market Outcome. Earnings: Individual earnings data comes from the Israel Tax Authority
(ITA). Only individuals with non-zero self-employment earnings are required to file tax returns in
Israel, but the ITA has information on annual gross earnings from salaried and non-salaried
employment, and they transfer this information, including the number of months of work in a given
year, annually to the NII. The NII produces an annual series of total annual earnings from salaries and
self-employment and I used this variable for 2000-2014. Following NII practice, individuals with a
positive (non-zero) number of months of work and zero or missing value for earnings are assigned
zero earnings. 14.1% of individuals have zero earnings at age 30-32 in our basic sample of 13,142. To
account for earnings data outliers I dropped from the sample all observations that are six or more
standard deviations away from the mean. Very few observations are dropped from the sample in each
of the years and the results are not qualitatively affected by this sample selection procedure. To
account for age differences of the different cohorts in the sample, the employment and earnings
outcomes are adjusted for years since graduating high school. The same earnings data is also available
for the parents of the students in our sample, for the years 2000-2002 and 2008-2012. I compute the
average earnings of each parent and of the household for 2000-2002 and use it as an additional control
in a robustness check of the evidence presented in this paper. These data were not available for the
analysis of the effect of the program on short-term outcomes. Employment: An indicator with value 1
for individuals with non-zero number months of work in a given year, 0 otherwise.
Education. Here as well I measure the outcomes by adjusting for years since graduating high school.
University schooling: is an indicator for being enrolled for at least one year in university schooling
and years of university schooling is the number of years of attendance during the period 2000-2013.
Academic college schooling: is an indicator for being enrolled for at least one year in any academic
college and years of college schooling is the number of years of attendance.
Personal Status Outcomes: The data on marital status and having children is available only for 2011.
Therefore for these outcomes, we can adjust for years since graduating high school based on
information about date of marriage and children’s birth dates.
Marriage: is an indicator for being married. Children: is an indicator for having at least one child.
Number of Children: is the number of children.
The NII linked these data to students’ background data that I used in Lavy (2010) to study the
effect of the choice program on high school academic outcomes.
10
This information comes from
10
As high school outcomes I used an indicator of dropping out before completing twelfth grade, an indicator for
matriculation (Bagrut) eligibility, credit-weighted average score on the matriculation exams, number of
matriculation credits, number of matriculation credits in science subjects and number of matriculation subjects
at honors level. Bagrut eligibility is a prerequisite for admission to higher education in Israel and the average
score on the matriculation exams, number of matriculation credits in science subjects and number of
8
administrative records of the Ministry of Education on the universe of Israeli primary schools during
the 1992–1994 school years. In addition to an individual identifier, and a school and class identifier, it
also included the following family-background variables: parental schooling, number of siblings,
country of birth, date of immigration if born outside of Israel, ethnicity and a variety of high school
and Bagrut high school achievement measures. This file also included a treatment indicator, school ID
and cohort of study. I had restricted access to this data in the NII research lab at the NII headquarters
in Jerusalem.
4. Identification and Estimation
In previous work (Lavy 2010) I used difference in differences (DID) and geographical
discontinuity in program placement as two alternative methodologies to estimate the effect of the
school choice program on short term outcomes (dropout rate) and on medium term outcomes (success
at the end of high school, six years after the school choice decision, in high stakes exams). Using DID
methodology, I relied on three alternative comparison groups which all yielded almost identical
evidence regarding the impact of the choice program.
11
I therefore use this same identification method
to estimate the effect of school choice on long term adulthood outcomes, while combining all three
comparison groups into one in order to increase efficiency in the estimation. Results based on using
each of these comparison groups separately are in line with the evidence that I present in this paper
and are available from the author upon request. I also used in Lavy (2010) geographical discontinuity
(GD) in program placement as an alternative identification strategy, which yielded evidence
consistent with the evidence based on the DID estimation. I therefore also use this GD identification
method in this paper to estimate the effect of school choice on long term adulthood outcomes. I
summarize briefly below the comparison group used here in the DID estimation and the group used in
the GD estimation. More detail about each of them is provided in Lavy (2010).
The first DID comparison group, based on the gradual implementation of the program,
includes school districts in Tel Aviv that were enrolled immediately following the two year
experiment. Since all the schools in districts 1-5 were included in the choice sets of students in district
9, only districts 6-8 could serve as a comparison group. Districts 6 and 8 are adjacent to district 9 but
their sample of students is too small, therefore I consider district 7 to also be part of the potential
comparison group (see Map 1 in online appendix). All three of these districts are part of South Tel
Aviv, geographically adjacent to or near district 9, and their population is much more similar to that of
district 9 than to that of Northern Tel Aviv (Lavy 2010). The second comparison group includes two
adjacent cities east of Tel-Aviv, which are part of the Dan metropolitan area: the Dan metropolitan
matriculation subjects at honors level are used to screen and select students for prestigious universities and
sought-after academic programs such as medicine, engineering, and computer science.
11
In Table A1 in the online appendix I present the mean demographic characteristics of the students in the
treatment group and in each of the three alternative control groups used in the DID estimation. This table is a
replication of Table 1 in Lavy (2010).
9
area covers five major cities, including Tel Aviv. District 9 includes the city’s southeastern
neighborhoods and is tangential to two of the neighboring cities: Givataim and Ramat-Gan (referred
to as GR, see Map 1 in online appendix). GR have independent and separate education systems and
therefore were not part of Tel-Aviv’s school choice reform.
12
GR students are very different in mean
characteristics from district 9 students (Lavy 2010). However, these differences are very stable as they
are similar in 1992 and 1993 as well. The solution, therefore, to the pre-program imbalances is to use
data on pre and post program cohorts (panel data) in a difference-in-differences framework that
removes time invariant heterogeneity across treated and control groups. Holon is another city adjacent
to Tel-Aviv (south) and it is very close to district 9, and I use it as the third comparison group. It is
more similar to district 9 in its characteristics than the GR group.
13
Therefore, the first identification approach that I apply in this paper is based on a contrast
between district 9 and a comparison group that includes districts 6-8, RG and Holon, before and after
the program was implemented. I use data on pre- and post-program cohorts (panel data) in a
difference-in-differences framework that removes any remaining time invariant heterogeneity across
treated and control groups. Since this DID estimation compares two consecutive cohorts, and since
the program was implemented immediately after it was announced, it is reasonable to assume that the
remaining differences were constant within this narrow time range. A concern with this DID
approach, however, is that the cohort immediately prior that I use as a control group might be affected
through spillover effects at the school level. As these students will be attending the same schools as
the treated students, peer effects or competitive effects on school productivity might impact the
untreated students as well.
As noted above I also use a geographical discontinuity in program placement as an alternative
identification strategy. Following Black (1999), I limit the sample to observations within a narrow
band around the municipal border between district 9 and GR (see Map 2 in online appendix). As
shown in Lavy (2010), the physical and other characteristics of the communities within this strip (for
example, type and average size of homes) are identical, as are zoning laws and municipal (type of
property) taxes, which are determined by the central government. Presumably there might still be
some differences, such as the political affiliation of the mayor, for example. The concern remains then
that such remaining differences may confound the effect of the program. As mentioned above, the use
of data on pre- and post-program cohorts in a DID framework will remove such time invariant
12
The Givataim, Ramat-Gan and Holon high school enrollment system before the inception of the TASCP was
based on zoning and it has not changed since, nor have these cities undergone any other major educational
reform since 1994.
13
The fact that two alternative sets of DID estimates, one that is based on a comparison group that has much
better characteristics and outcomes (GR or Holon) than the treated group and a second that is based on a
comparison group that has marginally worse characteristics and outcomes (districts 6-8), yield exactly the same
results is reassuring, given the possibility that the DID estimates are biased because of regression to the mean or
due to differential time trends in unobserved heterogeneity between treatment and control.
10
heterogeneity across treatment and control groups. I define this sample based on drawing a symmetric
band around the municipal border, 250 or 500 meters on each side. Contrary to the imbalances
between district 9 and GR, this GD sample yields better balanced treatment and control groups. In the
analysis of the long term outcomes I will use the +/-500 meters band, again in order to have a larger
sample for estimation, but it should be noted that the +/-250 meters band yields similar results.
4.1 Estimation
I first present a controlled comparison of treated and untreated students using samples of pre
and post treatment cohorts based on the following regression:
(1) Y
ijt
= X
ijt
+ Z
j
d + U
ijt
where Y
ijt
is the ith student's outcome in school j and year t; X
ijt
is a vector of the same student’s
characteristics; Z
j
is the treatment indicator (which equals 1 for district 9 students) and d is the
treatment effect. As noted above, I will first estimate the equation using as a comparison group a
sample that includes Tel-Aviv district 6-8 students, and GR and Holon students, and then I will also
exploit the GD sample (using the +/-500 meters sample).
In addition, I use the before-and-after cross section data as stacked panel data that permits
regression analysis with controls for primary-school fixed effects. Therefore, I will estimate stacked
models using three years of cross-section data combined. The treatment indicator Z
jt
is now defined as
the interaction between a dummy for the year 1994 and the district 9 indicator, as follows:
(2) Y
ijt
= µ
j
+ π
t
+ X
ijt
+ Z
jt
d+
ijt
where µ
j
is the primary school fixed effect and π
t
is a year (i.e., 1992, 1993 and 1994) fixed effect.
Apart from providing a check on the precision of the 1992-1993 vs. 1994 contrast in treatment effects,
the introduction of school (fixed) effects also provides an alternative approach to the clustering
problem. The validity of this control, however, depends on the validity of an additive conditional
mean function as a specification for potential outcomes in the absence of treatment.
4.2 Descriptive Statistics
Table 1 presents detailed descriptive statistics of the outcome variables for 11 years since
high school graduation for the 1992-1994 cohorts, by treatment and control group and by pre- and
post-reform cohorts. Post-secondary enrollment statistics are presented in panel A. The enrollment
rate in university schooling in the treatment group for the pre-treatment cohorts (1992 and 1993) is
17.2 percent and for the control group it is 23.1 percent. The difference is -0.058 (se=0.012), and is
statistically different from zero. The respective enrollment rates in academic colleges are 20.0 percent
and 26.3 percent; the difference is -0.063 (se=0.012) and is statistically different from zero.
1415
The
respective means and estimated differences for the post-treatment cohort are presented in column 4-6.
14
Note that very few students ever enroll in more than one type of post-secondary educational institution.
11
Note that the mean difference in university enrolment did not change much while the mean difference
in the academic college enrolment rate declined to -0.028 from -0.063. The difference between these
two differences (which is a simple uncontrolled difference in difference estimate), 0.035, will be
shown to be very close to the controlled difference in difference estimate that I will present in the next
section.
Summary statistics on completed years of schooling are presented in panel B. The average
number of years of university completed eleven years after high school graduation in the pre-reform
cohorts of the treatment group is 0.683 and in the control group it is 0.974. The difference is -0.290
(se=0.056). The respective means for years of college education are 0.555 and 0.822 and the
difference is -0.267 (se=0.043). This evidence suggests, as expected, that the treatment-control
imbalance at baseline in both types of post-secondary education is in favor of the control group. A
similar treatment-control comparison based on the post treatment cohort (1994) reveals that the gap in
university attendance remained unchanged while the gap in academic colleges’ attendance was almost
completely eliminated, and the remaining difference became statistically negligible. The implied
simple difference in differences estimate for college is 0.161 years and for university it is -0.040.
These dynamic changes suggest that the program led to improvement in college-going rates and years
of college completed without an effect on university outcomes. These estimates are similar to what I
will present in the next section based on controlled difference in differences estimation.
Summary statistics for the labor market outcomes are presented in panel C of Table 1. Eleven
years after high school graduation, 86.8 and 84.1 percent of the individuals in the pre-treatment
cohorts in the treatment and control group, respectively, were employed and the difference between
the two was 1.1 percent (se=0.010). The respective rates in the post treatment period are 84.1, 84.4
and -0.003 (se=0.014). Average annual earnings at baseline
16
was lower in the treated group by about
NIS 3,000 ($750), a gap consistent with post-secondary education treatment-control differences.
The summary indicators in panel D suggest that just over half of the treated sample is married
by 2011; in the pre-treatment control group this rate is 2 percentage points lower. Age of marriage in
the treated group is 25.6, about a third of a year younger than in the control group and a similar gap is
observed in age of having the first child.
In panel E I report statistics on parental income in 2000-2002. This information, which was
not available when studying the short and medium term effects of the school choice program, reveals
gaps in favor of the control group. This is of course consistent with the other imbalances seen in Table
1: father’s income is higher in the pre-program control cohorts by NIS 27,175 and in the post-program
by NIS 24,093 and these two differences are not statistically different from each other. The respective
15
The respective means for the whole cohort (82,500 students) are 24.0 in universities and 24.0 percent in
academic colleges.
16
The mean earnings in this sample, NIS70,639, is identical to mean earnings in the whole cohort,
NIS 70,300.
12
differences between average mother’s earnings are NIS -10,904 and NIS -7,974. These stable
differences will be shown not to affect the treatment effect estimates of school choices when added as
controls in the difference-in-differences regressions.
5. Empirical Evidence
The school choice program had positive and significant short and medium term effects on
students’ high school completion rate and on academic achievements during high school. Across
identification methods and comparison groups, the results consistently suggest school choice
significantly reduced the drop-out rate by 8.4 percent (35 percent decline) and increased the
matriculation rate by 6.1 percentage points (25 percent improvement). These results are presented in
Table A1 in the online appendix. These very large effects were accompanied by an improvement in
the quality of schooling. The average number of Bagrut credits increased by two units relative to the
pre-program mean of 12 units and the average score in all of the Bagrut exams was up by 6.6 points,
about 10 percent improvement. Other dimensions of quality improvement are the increase in number
of Bagrut credits in science subjects and the increase in Bagrut honor level studies (up by a quarter
relative to a mean of one such subject). These estimates are also presented in Table A1. The estimates
based on the GD sample are presented in Table A2 and reveal a similar pattern of a positive effect of
the school choice program on high school outcomes.
In Lavy (2010) I also provided evidence about potential mechanisms of the effect of school
choice on the short and medium term academic outcomes. This analysis shows that school choice
improved the learning and social environment in school. For example, as a result of the program,
teacher–student relationships and students’ social acclimation and satisfaction at school improved and
the level of violence, bulling and classroom disruptions declined. The higher satisfaction of students
at school can probably be attributed to a better match between students and schools, an improvement
facilitated by the school choice program. Indirect evidence of the improved matching is the fact that a
large proportion of district 9 students who had the longest travel distance from home to schools in
districts 1-4, opted out as well, and chose out of district schools. This is evidence of the willingness of
students to enroll in what they perceive to be a better school, even at the expense of longer travel time
and higher cost. Also shown in Lavy (2010) is that competition among schools intensified following
school choice and that it led to improved school quality. For example, two schools that experienced
sharp decline in enrollment were closed while others expanded. Improved quality was facilitated by
the flexibility that schools enjoyed with respect to curriculum and programs. For example, some
schools introduced new programs such as enrollment in university courses. However, conclusions
about whether free school choice improves real human capital accumulation and well-being can only
be based on longer term effects, in particular outcomes such as post-secondary enrollment and
completed years of tertiary education, employment, earnings, welfare dependency and other social
outcomes. We study these next.
13
5.1 Effect on Post-Secondary Schooling Attainment
I first present graphs illustrating the effect of the school choice program on post-secondary
education. I focus on the two sub-sectors of academic post-secondary education in Israel. The first
includes the seven research universities in Israel that confer BA, MA and PhD degrees. These
universities require a matriculation diploma for admission, including an intermediate or advanced
matriculation unit in English
17
and at least one matriculation subject at an advanced level. About 35%
of all students are enrolled in one of the seven universities. The second sub-sector is made up of more
than 50 academic colleges that mostly confer a BA degree and predominantly offer social sciences,
business and law degrees.
Figure 1 presents the dynamic of the treatment effect on academic college enrollment (vertical
axis) starting from the first year after high school graduation until 12 years later (horizontal axis). We
note again that during the first few years after high school graduation almost all boys (for three years)
and most girls (for two years) are still in military service and therefore the treatment effect is not
informative because it is based on a limited sample of those not drafted to service. This treatment
effect is however positive and statistically significant from year four after graduating high school,
reaching a high of 4.8 percent and declining slightly towards the end of the period to 4 percent. The
respective mean enrollment rate for the treated group increases gradually from year one and is highest
at 21 percent twelve years later. The effect size here is therefore a 20 percent increase. The effect on
completed years of academic college (presented in Figure 1A) increases continuously until 12 years
after graduating high school, reaching a peak at 0.19 years and leveling thereafter. The mean of
completed years of academic college in the treatment group is 0.6 and therefore the effect size is a 30
percent increase.
Figures 2 and 2A present the estimated effects on university enrollment and attainment and
the pattern revealed in these figures is very different, as the effect is practically zero. The treated
group mean of university enrollment rate is 0.18 and the mean years of university is 0.71 years, and
both of these outcomes are not changed due to the program.
In Figures 3-3A I replicated this graphical analysis for any type of post-secondary education
(including teachers colleges and non-academic education) and the results are very similar to those
presented in Figures 1-1A. Overall post-secondary enrollment increased by almost 5 percentage points
and total education increased by a fifth of a year.
18
Table 2 presents detailed estimates from regressions of the effect of free school choice on
post-secondary education attainment when outcomes are measured twelve years after high school
graduation. The first row presents DID estimated effect on enrollment in any type of post-secondary
17
To qualify for a matriculation diploma a basic study program in English is sufficient, but university admission
requires a higher level.
18
It is important to note here that the expansion in enrollment in academic colleges due to the school choice
program could not have been at the expense of other students because the choice program and the number of
students affected was very small relative to the overall enrollment in academic colleges in the whole country.
14
education (column 2) and on the respective completed years of education (column 4). Standard errors
appear below each estimate in brackets and are clustered by secondary school. School choice
enrollment in any post-secondary education increased by 4.6 percentage points relative to a pre-
program mean of 42.5 percent in treated schools and 52.9 percent in the control group. The effect on
completed years of education (column 4) is 0.187 (SE=0.089). Relative to the pre-choice treatment
group mean (1.648) this is a 15 percent gain.
It is interesting and important to know what types of post-secondary education are affected.
Since the treated population is from a low socio-economic background with relatively low enrollment
at the higher quality end of academic institutions, we expect the effect to be low on university
education and higher on colleges and non-academic post-secondary institutions. In the second row I
present the estimated effect on university education and in the third row the effect on education in
academic colleges. The effect on university enrollment is practically zero (0.006, SE=0.014) and so is
the effect on university years of education. The effect on academic college enrollment is however up
by 4 percent, significantly different from zero (t=2.2), and completed years of this type of education
increased also, by almost a fifth of a year (0.171, SE=0.050).
19
The gain in academic college
education is almost equal to the overall gain in any type of post-secondary education, indicating that
the effect on any other type of education is very small or zero.
2021
The evidence presented above clearly demonstrates that the gain in post-secondary education
is concentrated in the lower end of academic education in Israel. The academic colleges are less
prestigious than universities and their admission requirements are less demanding in terms of Bagrut
results. This pattern is perhaps expected because the treated population is mostly from a
disadvantaged segment of the Israeli population and their enrollment and years of study in university
is much lower than the overall mean in the country. In addition, we can safely claim that the affected
students are at the margin of being admitted to post-secondary education, which can also explain why
the treatment effect is concentrated at the lower end of the quality distribution of academic education
in Israel.
The long term data that I use in this paper includes information on parental income during the
years of the experiment. It allows me to assess how sensitive the post-secondary treatment estimates
are to adding controls for family earnings. The estimates presented in Table A3 in the online appendix
19
It is important to note here that the expansion in enrollment in academic colleges due to the school choice
program could not have been at the expense of other students because the choice program and the number of
students affected was very small relative to the overall enrollment in academic colleges in the whole country.
20
Indeed enrollment in teachers’ colleges also increased, by 2.7 percent and significantly different from zero,
but the respective increase in years of this type of education is positive but small and imprecisely measured.
Enrollment and years of schooling in vocational education (two-year colleges that confer practical engineering
degrees) declined by 1.5 percentage points and by 0.025 years, very small and imprecisely measured changes.
These results are not presented in the paper and are available from the author.
21
In results not shown here I estimated placebo effects based on a contrast between the two untreated cohorts of
1992 and 1993. Overall, these controlled experiment estimates are not significantly different from zero, similar
to respective placebo regression estimates with high school outcomes as the dependent variables (Lavy 2010).
15
show that adding to the difference-in-differences regression a control for family income (average in
2000-2002) does not change at all the point estimates relative to those presented in Table 2. For
example, the estimated effect on college enrollment in Table A3 is 0.041 and on college years of
education it is 0.170, almost identical to the respective estimates in Table 2. This is a remarkable
result given that the treatment and control samples are not balanced in family income, but they are
equally imbalanced in this dimension, as in others, for the pre- and post-treatment cohorts.
To further check the robustness of the evidence presented above, I use the GD design
described in the previous section. The GD sample includes observations within a relatively narrow
band around the municipal border between district 9 and GR and the descriptive statistics of the
control and treatment group in this sample are presented in Table 3. It is important to note that in this
sample, the treated group is from a much higher socio-economic status and it resembles more closely
the control group. For example, the mean of fathers’ and mothers’ years of education in the GD
treated sample in the 1993 cohort is 11.43 and 11.58, respectively, while in the rest of district 9 the
respective means are less than 10. A similar pattern is observed for the post-secondary educational
outcomes presented in Table 3, where in the GD treated sample the mean enrollment in university and
academic college education in the post treatment cohort (1994) is 22.6 and 24.7 percent, respectively,
while the respective means in the rest of district 9 are 17.9 and 20.9 percent, respectively. The much
higher socio-economic status of treated students in the GD sample in comparison to the rest of district
9 suggests that we might expect a higher effect of school choice on university schooling than what we
estimated based on district 9’s full sample.
Indeed this is the case, as shown in Table 4 where I report estimates derived from the GD
sample. The effect on university enrollment is 0.051 and the effect on academic college enrollment is
-0.011. The effect on years of university education is 0.260 and the effect on academic college years
of education is 0.017. This pattern is strikingly different from the evidence that is based on all of
district 9. However, these estimates are less precisely measured than the respective estimates in Table
2, most likely because of the much smaller sample size. As we will see below, the gain in university
education will be rewarded with a higher increase in annual earnings relative to the gain in annual
earnings experienced by those who improved only academic college education.
5.2 Effect on Employment and Earnings
We start here as well with a graphical presentation of the impact of the school choice program
on employment and earnings. Again we measure for each individual these two outcomes based on
number of years since graduating high school. The employment and earnings data are available until
year 2014, so thirteen years is the longest period after graduating high school for which we examine
the effect of the program. Figure 4 presents the yearly estimates on employment. As noted earlier, the
estimates for the first three years are not meaningful because most of the students in our sample were
still in military service. In the fourth year after high school graduation, about 85 percent of the
16
individuals in the sample were employed (according to our definition of employment, which is
employed at least for one month during the year and had positive earnings). For almost all years the
estimates are not precisely measured: for 5-7 years after high school graduation the estimates are
positive and thereafter they are negative, but in most years they are not statistically different from
zero, especially in 12 and 13 years after high school graduation. Similar evidence is obtained for the
outcome that measures the number of months per year of being gainfully employed. These imprecise
and inconclusive employment dynamics imply that they do not play an important role in determining
the change in earnings due to the school choice program.
We next turn to the time series of estimated effects on annual earnings, which are presented in
Figure 5. The treatment effect estimates on earnings are positive throughout the period after high
school graduation. They increase over time monotonically with the exception of a spike in treatment
effect nine years after high school graduation. Similarly, average annual earnings in the sample also
increase monotonically until the end of the period, from NIS 40,000 (about $10,000) five years after
high school graduation to just over NIS 80,000 13 years after high school graduation. The treatment
effect on earnings in the last two periods of analysis is just below NIS 5,500 a year and it is
significantly different from zero at the 10 percent level of significance in both periods. It is interesting
to note that the earnings treatment effect is not negative even in the period when post-secondary
enrollment rate is higher among treated students. This pattern is different from that reported in Lavy
(2016), where teacher pay for performance increased university education while lowering
employment and earnings during the three to five years when students are studying. This contrasting
pattern is not surprising for several reasons. First, it is typical that students in academic colleges in
Israel work part time or full time, while university studies have a more demanding academic schedule
and requirements that correspond to full time attendance, making it more difficult to combine work
with study. Secondly, the treated students in academic colleges are usually from a lower socio-
economic background in comparison to students in universities, and therefore they can rely less on
parental support. Thirdly, scholarships based on academic merit and on low family income are
available for university students but not for students in academic colleges.
Table 5 presents evidence about the effect of the school choice program on employment,
number of moths worked in a year, and monthly earnings, for 11 to 13 years after high school
graduation (columns 2, 4, 6) and based on stacking the three periods in one sample (columns 8). The
average employment rate in the treatment group in these three periods is 87.0, 85.2 and 85.4,
respectively. The respective treatment effect on employment is negative, though it is small and
practically not different from zero in the last two periods. The estimated effect on months worked per
year has the same pattern. It is important to note that the negative though small employment effect
does not reflect a higher rate of individuals still studying among treated students; the proportion of
students in the 1994 cohort who are not yet employed and are still studying is the same in both
17
groups: in the treatment group in 2012 it is 1.4 percent and in the control group it is 1.3 percent. The
respective means in the 1992-93 cohorts are 0.7 percent and 0.8 percent.
The average annual earnings for the 1992-1993 cohorts in treated schools 11 years after high school
graduation is NIS 74,709 ($17,620), 12 years after high school graduation it is NIS 78,313 ($19,216)
and 13 years after high school graduation it is NIS 81,230 ($21,377). The estimated effect of the
school choice program on annual earnings is NIS 3,368 ($935) 11 years after high school graduation,
NIS 5,544 12 years after and 5,662 13 years after. The last two estimates are significantly different
from zero at the 5 percent level of significance. I also estimated an earnings effect using a combined
11 to 13 years after high school graduation earnings, stacking the data together for these three periods.
This estimate is presented in column 8 of Table 5. The estimated effect of school choice on earnings
from this stacked data is NIS 4,763, close to the average of the estimates in these three years.
In Table A4 in the online appendix I present the treatment estimates on earnings and
employment when controls are added for parental or family earnings. The three columns correspond
to estimates for 11, 12 and 13 years after high school graduation. These estimates of the treatment
effect of the program are very similar to the estimates presented in Table 5. The obvious conclusion is
that adding a control for parental earnings does not affect at all the treatment estimates of the effect of
school choice on labor market outcomes.
In Table 6 I present the estimated effect on labor market outcomes based on the GD sample.
The effect on earnings has the same pattern as in Table 5 but the estimates are larger. Focusing on the
stacked data estimates in column 8, the annual earnings gain during 11 to 13 years since high school
graduation is NIS 7,613: a 9 percent gain relative to total annual earnings in this period. The larger
gain estimated based on the GD sample reflects to some extent the higher increase in years of post-
secondary education and the higher rate of return for university education in Israel relative to the rate
of return to academic college education. Caplan et al (2009) report that in many fields of study,
academic college graduates in their first jobs earn on average 20 to 30 percent less than university
graduates. However, the effect on employment is negative and larger than what is observed in the full
sample. This is a puzzling pattern that is resolved when I estimated all treatment effects by gender
which show that all of the negative effect on employment is on women, and that most of the positive
effect on earnings is due to men. Consistent with these results is the positive effect on women’s
marriage rate and fertility without a corresponding effect on men. I present more background to these
results in the sections where I report results by gender, and the marriage and fertility effect of school
choice.
Comparing the Effect on Earnings to Related Evidence
This is the first study to provide evidence of the effect of school choice on students’ earnings
at adulthood. However, it is still useful to compare our results to the impact of other childhood and
education interventions on earnings at adulthood. Andersson et al. (2013) estimated that living during
18
teenage hood in public or voucher housing increased females earnings by 18-21 percent. Each
additional year of public or voucher-supported housing increases earnings by 7 percent for females.
For males each year of public housing participation as a teenager increases adult earnings by 5 percent
with no corresponding effect of voucher housing. Chetty et al. (2011) have shown that having a
kindergarten teacher with more than ten years of experience increased students’ average annual
earnings at ages 25 to 27 by 6.9 percent ($1,093) between 2005 and 2007. Similarly, an improvement
in class quality increased average annual income earned between ages 25 and 27. Johnson et al.
(forthcoming QJE) show that for children from low-income families, increasing per-pupil spending by
10 percent in all 12 school-age years increased adult hourly wages by 13 percent. Schweinhart et al.
analyze the long term effect of the High/Scope Perry Preschool experiment and find that students in
treatment had significantly higher median annual earnings than the no-program group: 20 percent
higher at age 27 and by 36 percent higher at age 40. Finally, Chetty, Hendren and Katz (2016) find
that moving to a lower-poverty neighborhood (MTO) significantly improves college attendance rates
– by 2.5 percent – and earnings by 31 percent, for children who were young (below age 13) when
their families moved. Clearly our estimated effects on earnings are not unusually high relative to
estimates surveyed above. For example, the teachers’ pay experiment raised college enrollment by 5
percent, twice that of the MTO effect, and increased earnings 10-12 years after high school graduation
by 7-9 percent, a quarter of the MTO effect.
What Explains the Increase in Earnings?
Note that if we assume that all of the 6 percent average increase in annual earnings 11-13
years after high school graduation (based on the DID estimates using the full sample and stacked data)
is due to the 0.2 increase in years of schooling, this would imply a much higher rate of return to a year
of schooling estimated in recent studies in Israel (Frisch and Moalem 1999, Frisch 2007).
22
However,
as shown above, treated students experienced a range of improvements in educational outcomes that
are likely to be rewarded in the labor market independently of the return to post-secondary years of
schooling. Particularly important is the matriculation rate, which increased by 6-7 percent and earns a
return of about 13 percent independently of the return to years of schooling.
23
In addition, the quality
improvements in the matriculation study program and diploma (for example, the average score,
number of credit units and credits in honor and science subjects) could also be rewarded in the labor
market beyond the return to years of schooling.
24
The program also led to improvements in some non-
22
It should be noted that the sample used in this analysis includes individuals with zero earnings. Therefore the
estimated impact on earnings could also reflect an indirect effect through an effect on employment, while a
classic Mincer rate of return to schooling regression does not include individuals with zero earnings. However,
the evidence in Table 5 did not reveal any effect on employment.
23
For example, Angrist and Lavy (2009) estimate that Bagrut holders earn 13 percent more than other
individuals with exactly 12 years of schooling.
24
Caplan et al (2009) demonstrate that earnings in Israel are highly positively correlated with the quality of
post-secondary schooling (colleges versus universities and higher versus lower quality universities). For
19
cognitive behavioral outcomes, for example it reduced the level of violence and classroom disruption,
improved teacher–student relationships and increased students’ social acclimation and satisfaction at
school. These effects suggest that the program improved students’ social kills, and recent evidence
suggests that the labor market increasingly rewards such skills.
25
The interesting question therefore is whether the gains experienced by students due to the
access to free school choice (particularly the increase in academic college entry, completed years of
education and the higher earnings at adulthood) could be predicted by the short- and medium-term
positive effects of school choice on Bagrut outcomes? That is, are the effects measured at the time of
the experiment predictive of the program’s long-term effects? Do Bagrut outcomes that measure
quality of study program play an equal role in this regard? It should be noted however that we can
address this question but we cannot decompose the effect on earnings of Bagrut outcomes to the
component that operates through its effect on post-secondary schooling and the part that reflects a
direct independent effect unrelated to post-secondary schooling.
We approach this question by first estimating OLS regressions of annual earnings on the
various high school educational outcomes, while including in the regression controls for student’s
parental and demographic characteristics. In these regressions we use a sample that includes only the
control group from the two pre-reform years. These results are presented in Table A5 in the online
appendix. Using data for 13 years after high school graduation, I report in panel A estimates from
regressions when only one of the high school outcomes is included in the regressions (columns 2) and
also estimates when all outcomes are included jointly in the regression (columns 3). When included
one at a time, estimates of all outcomes are positive and very precisely measured. When all four are
included jointly, all outcomes (the average matriculation score, the indicator of obtaining a
matriculation diploma, the overall number of matriculation credits and units in science subjects)
remain positive and statistically significant, though the point estimates are smaller – as expected due
to high collinearity among these variables. These results are consistent with evidence reported in
Lavy, Ebenstein and Roth (2014) and Ebenstein, Lavy and Roth (2016) who use random shocks to
performance in matriculation exams to identify the reduced form effects of these high school
outcomes on earnings at adulthood, and find strong and significant positive effects.
In panel B column 2, I report estimates from regressions of the post-secondary enrollment and
completed years outcomes on earnings 13 years after high school graduation, first when including
only one outcome at a time (column 2), and secondly where all four are included jointly (column 3).
Here as well each of these outcomes have positive and significant association with earnings, and when
included jointly all four are positive but only three of them are statistically significant. In column 4, I
example, this study shows that earnings are much higher for graduates of Tel Aviv, Jerusalem and the Technion
Universities relative to graduates from the other four universities in the country. Admission to the top
universities is of course positively correlated with the high school matriculation outcomes.
25
See for example Deming (2015).
20
report the estimates from a regression where all high school and post-secondary education outcomes
are included jointly. Note that six of the eight outcomes still have positive and significant estimated
coefficients and that three of the high school outcomes are among them, even though the regression
includes the post-secondary schooling variables. I view this as evidence that the high school outcomes
that measure quality of education have an effect on earnings in addition to their effect on post-
secondary schooling. A second conclusion from Table A5 is that high school and post-secondary
schooling outcomes are indeed correlated with earnings.
Another way to check whether the program’s effect on earnings stems from improvement in
schooling outcomes is to examine whether the estimated effect on post-secondary attainment and
earnings shrinks or even disappears when the Bagrut outcomes are added as controls. Of course, such
evidence could be only suggestive because the high school outcomes are endogenous and are
probably correlated with the error term in the regressions of long term outcomes. In Table 7 I present
estimates of the coefficient of the school choice treatment effect in a DID regression that includes also
the high-school outcomes as explanatory variables – first including one at a time and secondly all four
jointly. For ease of comparison, I present in column 1 the original treatment effect estimates from
Tables 2 and 6. The effect of school choice on enrollment in any post-secondary schooling is 0.040.
The inclusion of each of the high-school outcomes as an additional control shrinks the treatment effect
two thirds towards zero, with the exception of number of Bagrut science credit units. When all four
high school outcomes are included, the treatment effect estimate falls to 0.013 and it is not statistically
different from zero (first row-column 6). A similar pattern is seen in the second row of Table 7, when
the long term outcome is completed years of college schooling: the treatment effect declines from
0.171 to 0.079. However, the most striking result is the sensitivity of the treatment effect on earnings
to adding the high school outcomes as controls: the average matriculation score and the number of
matriculation credits reduce the treatment effect from NIS 4,763 to just over 600, an 87 percent
decline. When all four high school outcomes are added to the regression as control, the earnings effect
declines to 79, though it has a large standard error. Similar results are obtained when the GD sample
is used.
Effect of School Choice by Gender
Previous research on the effectiveness of schooling interventions has shown differences in the
responsiveness of boys relative to girls (for example, Angrist and Lavy 2009). To test for this
possibility, in Table 8, I stratify the sample based on the gender of students and present first the effect
of school choice on high school outcomes, by gender.
26
Free school choice improved all five
outcomes for boys and girls except the dropout rate of girls, which declined by only 2.1 percentage
points, with a t statistic of just 1.5. However, it is noticeable that girls have higher means in all six
high school outcomes and girls’ dropout rate is much lower than that of boys, 10.3 percent versus 26.6
21
percent among boys in the sample. However, all of the point estimates suggest that the effects are
larger among boys except for the effect on the matriculation rate. The gender differences are
statistically significant for the following outcomes: dropout rate, average score, number of credits,
number of subjects studied at honor classes.
In Table 9 I report the estimated effects of school choice on post-secondary schooling
outcomes by gender. Boys gained a 9.3 percentage increase in enrollment and a third of a year of
post-secondary schooling, most of it in academic colleges but some in university. The girls’ gain is
limited to academic colleges, but the estimated effect is much smaller than that for boys. Table 10
shows that these gender differences are also reflected in the labor market. Focusing on the estimates
based on the stacked regressions that pool data for the period 11-13 years after high school
graduation, the effect on boys’ earnings is NIS 6,807 (se=3,615), an 8 percent increase, while the
earnings effect for girls is NIS 1,785 (se=2,136), which is not statistically different from zero.
However, the girls’ labor market experience includes also a 3.1 percent decline in employment rate
and a two thirds of a month decline in months of work in a given year. Both these effects are precisely
measured. The decline in months of work among treated girls accounts for a negative NIS 4,931 (=
[(68,347/9.288) x 0.671)]) effect, which wipes out the expected positive effect of the increase in
college education on earnings. On the other hand, the effect on boys’ employment is practically zero.
What can explain the different pattern of the labor market effects by gender, in particular the negative
effect on girls’ employment? I turn in the next section to the effect on marriage and fertility outcomes,
which provides partial answers to this puzzle.
5.3 Effect on marriage and children
In Table 11 I report results regarding the program’s effect on marriage and fertility. The
marriage and fertility data is available up to 2011. However, I can still compute these outcomes by
years after high school graduation because the dates of marriage and of birth of children are available
in the data. Fifty six percent of the treated sample are married after ten years following high school
graduation. The treatment effect on being married at this date is 2.8 percent but it is not precisely
measured. The age of marriage effect is similar (0.125, se=0.151). The estimated effects on the
indicator of having children and on the number of children are positive, but they are not measured
precisely. However, the age of having the first child is delayed by half a year and this effect is
precisely measured with SE=0.174.
In columns 4 and 6 I present the respective effects on boys and girls and meaningful
differences are revealed. School choice has a negative though imprecise effect on boys’ marriage rate
and it has a large positive effect on girls’ marriage rate, which is 8.1 percent higher relative to a mean
of 62.9 percent. Age of first marriage of girls is unchanged while it is delayed by a third of a year for
boys. The probability of having children by age 28 is increased for girls by 8.8 percent, relative to a
26
These results are not reported in Lavy (2010).
22
mean of 51.8 percent, while the effect for boys is negative. The effect on number of children is
positive for girls, up by 0.158 children, while for boys it is negative, a decline of 0.102 children. All
the estimated effects on girls are statistically significant and so are some of the estimated effects on
boys. The higher marriage and fertility rates among women in the treated sample could be related to
the lower employment and earnings gains of this group, even though they had higher means of end of
high school and post-secondary schooling outcomes relative to untreated women in the sample.
Of course, marriage and fertility are endogenous choice variables, and therefore it is not
possible to study the school choice effect by samples stratified by marriage and parenting status. Yet it
is interesting to note that married women in our sample, both in treatment and in the control group,
have lower employment rate and lower earnings. A comparison of married women in the treated
group and the control group did not yield any differences in spouse’s mean education and earnings,
ruling out the possibility that own education and earnings were substituted by the spouse’s outcomes
through marriage. I of course caution again that stratification of the sample by these choice variables
is not legitimate and therefore this evidence is only suggestive of potential links among outcomes.
6. Conclusions
The vast majority of published research on the impact of school interventions has examined
their effects on short-run outcomes, primarily by looking at their impact on standardized test scores.
While important, a possibly deeper question is the impact of such interventions on life outcomes in
the long-run. This is a critical question because the ultimate goal of education is to improve lifetime
well-being. Therefore, gaining new insights about which interventions are more effective in
improving long-term outcomes will make a potent contribution to the design and implementation of
new interventions, better resource allocation and the efficiency of the education sector.
Recent research has begun to look at this issue, but much work remains to be done,
particularly with regard to the long-term effects of interventions explicitly targeting improvement in
the general quality of education and students’ educational attainment. The empirical evidence from
this study contributes to a more complete picture of the long term returns to various educational
interventions. This effort should enable teachers, institutions and governments to make more informed
decisions as to which educational programs constitute the most beneficial use of limited school
resources. The high school system in Israel and its high-stakes exit exams are very similar to those in
other countries, and the school choice program studied in this paper shares many features with
programs implemented in recent years in the US and in European and other OECD countries. As a
result, the lessons learned from this research are transferable and applicable to the education system in
other developed countries.
The school choice program studied here had positive longer term outcomes at adulthood. The
evidence clearly suggests that allowing children to choose their secondary school freely at age 12, not
only improved sharply their high school outcomes six years later, but it also impacted positively their
23
path to post-secondary schooling and increased meaningfully their earnings about a decade and a half
later. It is important to note also that these gains were not at the expense of other students in the
receiving schools, because this later group was already exposed to a similar proportion of incoming
students as a result of the bussing program that preceded the school choice program. If such a peer
effect was operational it should have been positive, because the opting out to schools outside the own
school district was voluntary in the choice program while being compulsory during the bussing
program. In earlier work I have shown that the improved outcomes during middle school and high
school were facilitated by a better student-school match, by more competition among schools and by
higher schooling quality. These results are important because the school choice experiment targeted a
disadvantaged population in some of the more deprived parts of Tel Aviv. Since evidence about the
Tel Aviv school choice program has become available, other school choice programs were introduced,
for example in Jerusalem in 2006 and more recently in many cities in Israel.
27
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The Ministries of Education and of Finance in Israel recently introduced a large school choice program that
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Harvard School of Education.
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of Childhood Investments on Postsecondary Attainment and Degree Completion” Journal of
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(1), 159-208.
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Milwaukee Parental Choice Program,” Quarterly Journal of Economics, 118, 553–602.
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IZA and ZEW Discussion Paper No. 7898.
Treated
schools
mean
Non
treated
Schools
mean
Mean Difference
(Standart error)
Treated
schools
mean
Non
treated
Schools
mean
Mean Difference
(Standart error)
(1) (2) (3) (4) (5) (6)
A. Enrollment
University 0.172 0.231 -0.058 0.158 0.231 -0.073
(0.378) (0.421) (0.012) (0.365) (0.421) (0.016)
Academic College 0.200 0.263 -0.063 0.254 0.282 -0.028
(0.400) (0.440) (0.012) (0.436) (0.450) (0.017)
B. Years of Schooling
University 0.683 0.974 -0.290 0.646 0.975 -0.330
(1.728) (2.044) (0.056) (1.688) (2.019) (0.077)
Academic College 0.555 0.822 -0.267 0.759 0.865 -0.106
(1.311) (1.595) (0.043) (1.559) (1.594) (0.062)
C. Labor Market Outcomes
Employed (1 = Yes, 0 = No)
0.868 0.841 0.028 0.841 0.844 -0.003
(0.338) (0.366) (0.010) (0.366) (0.363) (0.014)
Months Worked
9.284 9.021 0.264 9.004 9.081 -0.077
(4.369) (4.572) (0.126) (4.534) (4.524) (0.176)
Average Annual Earnings (NIS)
70,639 73,588 -2,949 73,091 75,518 -2,427
(58,957) (64,070) (1,759) (64,950) (67,281) (2,608)
D. Personal Status Outcomes
Married (1 = Yes, 0 = No)
0.525 0.505 0.020 0.457 0.393 0.064
(0.500) (0.500) (0.014) (0.498) (0.489) (0.019)
Age of first marriage
25.563 25.871 -0.308 24.953 25.260 -0.308
(3.014) (2.901) (0.108) (2.522) (2.574) (0.145)
Children (1 = Yes, 0 = No)
0.447 0.408 0.039 0.372 0.281 0.091
(0.497) (0.491) (0.014) (0.484) (0.449) (0.018)
Age of first child
26.592 26.989 -0.397 25.962 25.962 0.000
(2.939) (2.900) (0.122) (2.589) (2.649) (0.173)
Number of children
0.796 0.692 0.104 0.612 0.443 0.169
(1.070) (1.025) (0.029) (0.976) (0.841) (0.034)
E. Parental Earnings
Average Father's Earnings in 2000-2002 93,374 120,550 -27,175 98,227 122,320 -24,093
(114,484) (154,358) (4,229) (100,779) (158,485) (6,043)
Average Mother's Earnings in 2000-2002 48,131 59,035 -10,904 53,899 61,873 -7,974
(60,738) (71,551) (1,952) (84,227) (73,365) (2,946)
Average Family Earnings in 2000-2002 141,820 179,988 -38,168 153,039 184,665 -31,626
(137,004) (184,831) (5,080) (139,228) (186,745) (7,256)
Number of Observations 1,519 8,902 779 4,255
Table 1: Descriptive Statistics and Pre and Post Treatment-Contorl Comparison of Means of Post-Secondary Schooling
Outcomes , Employment Earnings, and Personal Status Outcomes (11 Years Since High School Graduation)
Post: 94 cohort
Notes: The table reports means and standard deviations for different post-secondary education and employment variables for 11 years
after high school graduation. Each column represents these statistics for a different group as described in each column's headline. Panel A
is comprised of binary variables indicating whether the individual was ever enrolled 11 years after high school graduation in a specific
type of post-secondary institution. The categories are not mutually exclusive and overlapping is possible. Panel B reports the number of
years of education an individual has attained by 11 years after high school graduation in each type of the post-secondary institutions listed
in panel A. Panel C reports the mean of an employment indicator, annual earnings and the number of months worked 11 years after high
school graduation.
Pre: 92 and 93 cohorts
Mean, 1992-1993
Cohorts in Treated
Schools
Treatment
Mean, 1992-1993
Cohorts in Treated
Schools
Treatment
(1) (2) (3) (4)
A. Any Post Secondary Schooling 0.425 0.046 1.648 0.187
(0.494) (0.022) (2.363) (0.089)
B. University Schooling 0.179 0.006 0.717 0.050
(0.383) (0.014) (1.801) (0.063)
C. College Schooling 0.209 0.040 0.589 0.171
(0.407) (0.018) (1.361) (0.050)
Number of Observations 1,539 15,669 1,539 15,669
Table 2: Effect of School Choice on Post-Secondary Schooling, 12 Years Since High School Graduation
Enrollment
Years of Schooling
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on post-secondary schooling.
Columns 1-2 measure enrollment into different types of post-secondary institutions, while columns 3-4 measure completed years of post-secondary
education by institution type. The results are for 12 years after high school graduation. The variable "Any Post-Secondary Education" refers to all
different post-secondary institutions. Columns 1 and 3 .represent the mean and standard deviation for the 1992-1993 (untreated) cohorts in the
treated schools. Columns 2 and 4 report the differences-in-differences estimates for each of the dependent variables. Standard errors are clustered at
the school level.
Treated
schools mean
Non treated
Schools mean
Mean
Difference
(Standart
error)
Treated
schools
mean
Non treated
Schools
mean
Mean
Difference
(Standart
error)
(1) (2) (3) (4) (5) (6)
A. Enrollment
University 0.226 0.297 -0.071 0.209 0.272 -0.063
(0.419) (0.457) (0.025) (0.407) (0.446) (0.031)
Academic College 0.247 0.293 -0.046 0.288 0.339 -0.051
(0.432) (0.455) (0.025) (0.454) (0.474) (0.033)
B. Years of Schooling
University 0.869 1.257 -0.387 0.850 1.162 -0.312
(1.864) (2.244) (0.117) (1.870) (2.146) (0.145)
Academic College 0.705 0.939 -0.234 0.885 1.084 -0.199
(1.459) (1.688) (0.089) (1.621) (1.748) (0.121)
C. Labor Market Outcomes
Employed (1 = Yes, 0 = No)
0.890 0.830 0.060 0.856 0.864 -0.008
(0.314) (0.376) (0.020) (0.352) (0.343) (0.025)
Average Annual Earnings (NIS)
77,144 78,738 -1593.381 80,634 76,893 3740.997
(59,438) (70,772) (3,688) (71,412) (70,312) (5,055)
Months worked
9.473 8.938 0.535 8.874 9.212 -0.338
(4.315) (4.687) (0.252) (4.587) (4.297) (0.316)
Number of Observations 535 834 340 463
D. Personal Status outcomes
Married (1 = Yes, 0 = No)
0.546 0.489 0.057 0.453 0.352 0.101
0.499 0.501 0.039 0.499 0.478 0.035
Age of first marriage
25.894 26.689 -0.795 24.955 25.528 -0.573
2.947 2.395 0.290 2.429 2.366 0.269
Children (1 = Yes, 0 = No)
0.403 0.308 0.095 0.335 0.222 0.113
(0.491) (0.462) (0.037) (0.473) (0.416) (0.032)
Age of first child
26.917 27.959 -1.042 24.955 25.528 -0.573
2.889 2.375 0.340 2.429 2.366 0.269
Number of children
(0.713) (0.486) (0.227) (0.535) (0.333) (0.203)
1.063 0.794 0.072 0.926 0.710 0.058
E. Parental Earnings
Average Father's Earnings in 2000-2002 112,853 139,061 -26,208 107,873 138,760 -30,887
(140,079) (153,169) (8,343) (112,571) (151,137) (9,971)
Average Mother's Earnings in 2000-2002 56,552 71,761 -15,210 61,268 76,347 -15,079
(70,152) (76,009) (4,093) (110,611) (93,145) (7,237)
Average Family Earnings in 2000-2002 169,279 211,501 -42,222 169,992 215,898 -45,906
(162,594) (181,331) (9,827) (163,890) (198,632) (13,600)
Number of Observations 1,519 8,902 779 4,255
Table 3: Geography Discontinuity Descriptive Statistics and Pre and Post Treatment-Contorl Comparison of Means of Post-
Secondary Schooling Outcomes , Employment Earnings, and Personal Status Outcomes (11 Years Since High School
Graduation)
Pre: 92 and 93 cohorts
Post: 94 cohort
Notes : The table reports means and standard deviations for different post-secondary education and employment variables for 11 years
after high school graduation for the geography discontinuity sample described in the paper. Each column represents these statistics for a
different group as described in each column's headline. Panel A is comprised of binary variables indicating whether the individual was
ever enrolled until 11 years after high school graduation in a specific type of post-secondary institution. The categories are not mutually
exclusive and overlapping is possible. Panel B reports the number of years of education an individual has attained 11 years after high
school graduation in each type of the post-secondary institutions listed in panel A. Panel C reports the mean of an employment indicator,
annual earnings and the number of months worked 11 years after high school graduation.
Mean of 1992-
1993 Cohorts in
Treated Schools
Estimate
Mean of 1992-
1993 Cohorts
in Treated
Schools
Estimate
(1) (2) (3) (4)
A. Any Post Secondary Schooling
Ten years 0.503 0.044 1.845 0.265
(0.500) (0.037) (2.258) (0.145)
Eleven years 0.509 0.045 1.945 0.247
(0.500) (0.037) (2.363) (0.155)
Twelve years 0.512 0.042 2.004 0.209
(0.500) (0.039) (2.453) (0.165)
B. University Schooling
Ten years 0.232 0.048 0.879 0.259
(0.423) (0.032) (1.836) (0.148)
Eleven years 0.236 0.046 0.908 0.258
(0.425) (0.032) (1.897) (0.157)
Twelve years 0.235 0.051 0.913 0.260
(0.424) (0.031) (1.941) (0.158)
C. College Schooling
Ten years 0.234 -0.006 0.647 0.049
(0.424) (0.030) (1.363) (0.098)
Eleven years 0.247 -0.004 0.705 0.043
(0.432) (0.030) (1.455) (0.102)
Twelve years 0.257 -0.011 0.749 0.017
(0.437) (0.030) (1.515) (0.102)
Number of Observations 547 2,206 547 2,206
Table 4: Geography Discontinuity Estimates of the Effect of School Choice on Post-Secondary Schooling, 10-12 Years Since
High School Graduation
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on post-secondary
schooling for the geography discontinuity sample described in the paper. Columns 1-2 measure enrollment into different types of
post-secondary institutions, while columns 3-4 measure completed years of post-secondary education by institution type. The results
are for 10-12 years after high school graduation. The variable "Any Post-Secondary Education" refers to all different post-secondary
institutions. Columns 1 and 3 represent the mean and standard deviation for the 1992-1993 (untreated) cohorts in the treated schools.
Columns 2 and 4 report the differences-in-differences estimates for each of the dependent variables. Standard errors are clustered at
the school level.
Enrollment Post High School
Education
Post High School Years of
Schooling
mean, 1992-
1993 Cohorts in
Treated Schools
Estimate
mean, 1992-
1993 Cohorts in
Treated Schools
Estimate
mean, 1992-
1993 Cohorts in
Treated Schools
Estimate
1992-1993
Cohorts in
Treated Schools
Estimate
(1) (2) (3) (4) (5) (6) (7) (8)
Employment Indicator (1 = Yes, 0 = No) 0.870 -0.031 0.852 -0.012 0.854 -0.009 0.858 -0.015
(0.337) (0.015) (0.355) (0.014) (0.353) (0.012) (0.349) (0.011)
Total Annual Earnings (2009 NIS) 74,709 3,368 78,313 5,544 81,230 5,662 78,188 4,763
(64,595) (2,285) (67,521) (2,500) (70,432) (2,668) (67,808) (2,282)
Months worked 9.310 -0.317 9.251 -0.313 9.170 -0.154 9.228 -0.241
(4.354) (0.198) (4.453) (0.155) (4.456) (0.150) (4.433) (0.146)
Number of Observations 1,537 15,634 1,532 15,616 1,527 15,578 4,668 47,276
Table 5: Effect of School Choice on Employment and Income By Years Since High School Graduation
Stacked Regression 11-13
Years
13 Years
12 Years
11 Years
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on different employment and earnings outcomes. Columns 1-2 report results for 11
years after high school graduation, columns 3-4 report results for 12 years after high school graduation and columns 5-6 report results for 13. The variable "Employment Indicator" equals 1 if an
individual has any work record for the given year and 0 otherwise. Columns 1,3, 5 and 7 report the mean and standard deviation for the 1992-1993 (untreated) cohorts in the treated schools.
Columns 2, 4, 6 and 8 report the differences-in-differences estimates for each of the dependent variables listed above. Standard errors are clustered at the school level.
Mean of 1992-
1993 Cohorts in
Treated Schools
Estimate
Mean of 1992-
1993 Cohorts in
Treated Schools
Estimate
Mean 1992-1993
Cohorts in Treated
Schools
Estimate
Mean 1992-1993
Cohorts in Treated
Schools
Estimate
(1) (2) (4) (5) (7) (8) (7) (8)
Employment Indicator (1 = Yes, 0 = No) 0.892 -0.065 0.867 -0.066 0.865 -0.042 0.872 -0.058
(0.311) (0.027) (0.340) (0.026) (0.343) (0.023) (0.335) (0.023)
Total Annual Earnings (2009 NIS) 83,397 10,099 87,782 9,044 92,623 6,005 87,810 7,613
(67,627) (4,341) (71,565) (5,281) (76,376) (5,882) (72,250) (4,859)
Months worked 9.720 -0.678 9.497 -0.752 9.538 -0.758 9.534 -0.747
(4.061) (0.347) (4.298) (0.273) (4.286) (0.256) (4.256) (0.262)
Number of Observations 546 2,204 546 2,204 539 2,184 1,668 6,659
Table 6: Goegraphy Discontinuity Estimates of the Effect of School Choice on Employment and Income By Years Since High School Graduation
Stacked Regression 11-13 years
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on different employment and earnings outcomes for the geography discontinuity
sample described in the paper. Columns 1-2 report results for 11 years after high school graduation, columns 4-5 report results for 12 years after high school graduation and columns 5-6 report
results for 13. The variable "Employment Indicator" equals 1 if an individual has any work record for the given year and 0 otherwise. Columns 1,3, 5 and 7 report the mean and standard deviation
for the 1992-1993 (untreated) cohorts in the treated schools. Columns 2, 4, 6 and 8 report the differences-in-differences estimates for each of the dependent variables listed above. Standard errors
are clustered at the school level.
11 Years
12 Years
13 Years
Original
Estimate/ No
Added
Variables
Average
Matriculation
Score
Received High
School
Matriculation
Number of Credit
Units in
Matriculation
Exams
Number of
Science Credit
Units
All High School
Outcome
(1) (2) (3) (4) (5) (6)
Full Sample
Enrollment in college 12 years after high school garduation (1 = Yes, 0 = No) 0.040 0.017 0.019 0.015 0.036 0.013
(0.018) (0.017) (0.018) (0.017) (0.018) (0.017)
Completed Years of college Schooling 12 years after high school garduate 0.171 0.094 0.096 0.087 0.153 0.079
(0.050) (0.046) (0.049) (0.047) (0.051) (0.048)
Annual Earnings 11-13 years after high school graduate (2009 NIS) 4,763 653 1,700 640 2,585 79
(2,282) (2,423) (2,301) (2,394) (2,182) (2,288)
Geography Discontinuity Sample (500m sample)
Enrollment in college 12 years after high school garduation (1 = Yes, 0 = No) -0.011 -0.044 -0.039 -0.043 -0.012 -0.045
(0.030) (0.030) (0.031) (0.029) (0.030) (0.029)
Completed Years of college Schooling 12 years after high school garduation 0.017 -0.096 -0.083 -0.093 0.009 -0.102
(0.102) (0.105) (0.110) (0.105) (0.103) (0.110)
Annual Earnings 11-13 years after high school graduate (2009 NIS) 7,613 1,337 3,425 2,042 4,506 811
(4,859) (4,678) (4,660) (4,629) (4,675) (4,552)
Notes : This table assesses the sensitivity of the treatment effects presented in tables 2-6 when adding high school educational outcomes as control in the DID regressions. Column 1 reports the
estimated treatment effects from tables 1-5 for each specific sample and dependent variable. Columns 2-5 present the estimated treatement effects when the high school educational outcome
variable mentioned in the column header is added to the DID regression estimated in table 2, 4, 5 or 6 Column 6 represents the estimated treatement effect when all the four high school
educational outcomes are added together to the DID regressions. Standard errors are clustered at the school level.
Added Control Variables
Table 7: Effect of the School Choice when High School Educational Outcomes are Added As Contorls in the DID Regression
Mean, 1992-
1993 Cohorts
in Treated
Schools
Treatment
Mean, 1992-
1993 Cohorts
in Treated
Schools
Treatment
(1) (2) (5) (6)
Drop out 0.266 -0.101 0.103 -0.021
(0.442) (0.027) (0.304) (0.014)
Eligible for Bagrut 0.377 0.071 0.513 0.090
(0.485) (0.024) (0.500) (0.029)
Average score 53.499 8.856 66.823 3.968
(37.166) (1.784) (32.578) (1.643)
Number of science credits 1.414 0.466 1.709 0.333
(3.101) (0.199) (3.606) (0.201)
Number of Credit Units in Matriculation Exams
14.427 2.913 17.312 1.167
(11.641) (0.590) (10.000) (0.541)
Number of honor-level subjects 1.390 0.386 1.698 0.182
(1.540) (0.085) (1.346) (0.068)
Number of Observations 801 8,093 741 7,601
Table 8: Effect of School Choice on High School Outcomes By Gender
Girls
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on high school
outcomes for boys and girls separately. Columns 1 and 3 represent the mean and standard deviation for the 1992-1993
(untreated) cohorts in the treated schools. Columns 2 and 4 report the differences-in-differences estimates for each of the
dependent variables. Standard errors are clustered at the school level.
Boys
Mean, 1992-
1993 Cohorts
in Treated
Schools
Treatment
Mean, 1992-
1993 Cohorts
in Treated
Schools
Treatment
Mean, 1992-
1993 Cohorts
in Treated
Schools
Treatment
Mean, 1992-
1993 Cohorts in
Treated Schools
Treatment
(1) (2) (3) (4) (5) (6) (7) (8)
A. Any Post Secondary Schooling 0.372 0.093 1.447 0.331 0.481 -0.003 1.864 0.029
(0.484) (0.031) (2.323) (0.120) (0.500) (0.029) (2.389) (0.136)
B. University Schooling 0.143 0.030 0.605 0.113 0.218 -0.021 0.838 -0.015
(0.350) (0.023) (1.751) (0.105) (0.413) (0.022) (1.848) (0.108)
C. College Schooling 0.191 0.039 0.561 0.197 0.222 0.039 0.619 0.133
(0.393) (0.024) (1.340) (0.076) (0.416) (0.022) (1.383) (0.066)
Number of Observations 798 8,064 798 8,064 741 7,605 741 7,605
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on post-secondary schooling for boys and girls separately. Columns 1-2 and 5-6 measure
enrollment into different types of post-secondary institutions, while columns 3-4 and 7-8 measure completed years of post-secondary education by institution type. The variable "Any Post-Secondary
Education" refers to all different post-secondary institutions. Columns 1, 3, 5 and 7 represent the mean and standard deviation for the 1992-1993 (untreated) cohorts in the treated schools. Columns 2, 4,
6 and 8 report the differences-in-differences estimates for each of the dependent variables. Standard errors are clustered at the school level.
Years of Schooling
Table 9: Effect of School Choice on Post-Secondary Schooling, 12 Years Since High School Graduation
Boys
Girls
Enrollment
Years of Schooling
Enrollment
mean, 1992-
1993 Cohorts in
Treated Schools
Estimate
mean, 1992-
1993 Cohorts in
Treated Schools
Estimate
mean, 1992-
1993 Cohorts in
Treated Schools
Estimate
1992-1993
Cohorts in
Treated Schools
Estimate
(1) (2) (3) (4) (5) (6) (7) (8)
A. Boys
Employment Indicator (1 = Yes, 0 = No) 0.853 -0.010 0.836 -0.002 0.837 0.009 0.842 -0.000
(0.354) (0.023) (0.371) (0.023) (0.370) (0.021) (0.365) (0.020)
Total Annual Earnings (2009 NIS) 82,746 4,705 86,638 7,949 91,653 8,790 87,400 6,807
(73,242) (3,696) (76,652) (3,898) (79,139) (4,256) (76,785) (3,615)
Months Worked 9.205 0.171 9.173 0.011 9.153 0.335 9.172 0.187
(4.542) (0.290) (4.627) (0.247) (4.639) (0.258) (4.601) (0.244)
Number of Observations 797 8040 792 8028 789 7994 2411 24222
B. Girls
Employment Indicator (1 = Yes, 0 = No) 0.888 -0.052 0.870 -0.020 0.873 -0.029 0.875 -0.031
(0.316) (0.018) (0.336) (0.020) (0.334) (0.019) (0.331) (0.014)
Total Annual Earnings (2009 NIS) 66,053 1,218 69,403 2,252 70,087 1,504 68,347 1,785
(52,438) (2,891) (54,794) (2,340) (57,743) (2,408) (55,007) (2,136)
Months Worked 9.423 -0.827 9.335 -0.612 9.188 -0.659 9.288 -0.671
(4.143) (0.260) (4.261) (0.222) (4.255) (0.212) (4.245) (0.175)
Number of Observations 738 7,584 1,532 14,605 1,527 14,569 2,257 23,054
Table 10: Effect of School Choice on Employment and Income, By Gender and Years Since High School Graduation
11 Years
12 Years
13 Years
Stacked Regression 11-13 Years
Notes: This table presents the differences-in-differences estimates of the effect of the School Choice program on different employment and earnings outcomes for boys and girls separately. Columns 1-2 report results for 11
years after high school graduation, columns3-4 report results for 12 years after high school graduation and columns 5-6 report results for 13. The variable "Employment Indicator" equals 1 if an individual has any work
record for the given year and 0 otherwise. Columns 1,3, 5 and 7 report the mean and standard deviation for the 1992-1993 (untreated) cohorts in the treated schools. Columns 2, 4, 6 and 8 report the differences-in-differences
estimates for each of the dependent variables listed above. Standard errors are clustered at the school level.
mean, 1992-1993
Cohorts in Treated
Schools
Estimate
mean, 1992-1993
Cohorts in Treated
Schools
Estimate
mean, 1992-1993
Cohorts in Treated
Schools
Estimate
(1) (2) (3) (4) (5) (6)
Children (1 = Yes, 0 = No) 0.433 0.031 0.355 -0.021 0.518 0.088
(0.496) (0.021) (0.479) (0.026) (0.500) (0.030)
Number of children 0.794 0.021 0.614 -0.102 0.972 0.158
(1.069) (0.045) (0.966) (0.051) (1.136) (0.065)
Age of first child 26.590 0.513 27.316 0.460 26.067 0.522
(2.941) (0.174) (2.530) (0.255) (3.103) (0.241)
Married (1 = Yes, 0 = No) 0.562 0.028 0.499 -0.022 0.629 0.081
(0.496) (0.021) (0.500) (0.030) (0.483) (0.025)
Age of first marriage 25.567 0.125 26.561 0.345 24.752 0.004
(3.014) (0.151) (2.537) (0.172) (3.134) (0.232)
Number of Observations 1,542 15,708 801 8,098 741 7,610
Table 11: Effect of School Choice on Marriage and Fertility, 10 Years After High School
Entire Sample
Boys
Girls
Notes : This table presents the differences-in-differences estimates of the effect of the School Choice program on different personal outcomes. Columns 1-2
report results for the entire sample while columns 3-4 and columns 5-6 report the results for boys and girls respectivly.Columns 1,3, and 5 report the mean
and standard deviation for the 1992-1993 (untreated) cohorts in the treated schools. Columns 2,4, and 6 report the differences-in-differences estimates for
each of the dependent variables listed above. Standard errors are clustered at the school level.
Figure 1A
Figure 1
Figure 2A
Figure 2
Figure 3A
Figure 3
Figure 4
Figure 5
