The Economic Journal, 118 (July), 1025–1054. Ó The Author(s). Journal compilation Ó Royal Economic Society 2008. Published by
Blackwell Publishing, 9600 Garsington Road, Oxford OX4 2DQ, UK and 350 Main Street, Malden, MA 02148, USA.
STAYING IN THE CLASSROOM AND OUT OF THE
MATERNITY WARD? THE EFFECT OF COMPULSORY
SCHOOLING LAWS ON TEENAGE BIRTHS*
Sandra E. Black, Paul J. Devereux and Kjell G. Salvanes
This article investigates whether increasing mandatory educational attainment through compulsory
schooling legislation encourages women to delay childbearing. We use variation induced by changes
in compulsory schooling laws in both the US and Norway to estimate the effect in two very different
institutional environments. We find evidence that increased compulsory schooling does in fact
reduce the incidence of teenage childbearing in both the US and Norway, and these estimates are
quite robust to various specification checks. These results suggest that legislation aimed at improving
educational outcomes may have spillover effects onto the fertility decisions of teenagers.
Research suggests that teenage childbearing adversely affects women’s economic outcomes such as the level of completed schooling, labour market participation and
wages.1 Given these deleterious consequences, it is important to understand what
factors contribute to this decision. We know that low-educated women are more likely
to have a teenage birth but does this imply that policies that increase educational
attainment reduce early fertility? In particular, would increasing mandatory educational attainment (through compulsory schooling legislation) encourage women to
delay childbearing? If compulsory schooling reduces harmful or risky behaviour,
then these factors should be considered when evaluating the benefits of this type of
legislation.
This article provides evidence on the causal effects of changes in compulsory
schooling laws on teenage childbearing using data from the US and Norway. Having
data from these two countries provides an interesting contrast: one country is very
supportive of teenagers who have children, with extensive financial support (Norway),
while the other is much more punitive in its treatment (the US). Understanding the
differences in responses to compulsory schooling laws can provide useful information,
not only on the direct effect of schooling laws on teenage fertility but also the relative
difference across different institutional environments.
In the US, there has been extensive variation in compulsory schooling laws across
states and over time. Changes in these laws have been used as instruments for education in other contexts by Acemoglu and Angrist (2001), Lochner and Moretti (2004)
and Lleras-Muney (2005). There were many changes in minimum schooling requirements between the 1920s and the 1970s; we utilise changes over this entire time period
* The authors thank Marina Bassi for helpful research assistance. Black and Devereux gratefully
acknowledge financial support from the National Science Foundation and the California Center for Population Research. Salvanes thanks the Norwegian Research Council for financial support. Special thanks to
Enrico Moretti for providing the data on US compulsory schooling legislation and to Phil Oreopoulos,
Marianne Page and Ann Stevens for providing their data on state characteristics. A previous (2004) version of
this article circulated under the title ÔFast Times at Ridgemont High? The Effects of Compulsory Schooling
Laws on Teenage BirthsÕ.
1
See Klepinger et al. (1999), Angrist and Evans (1996) and Levine and Painter (2003) for results from the
US, and Chevalier and Viitanen (2003) and Goodman et al. (2004) for results from Europe.
[ 1025 ]
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THE ECONOMIC JOURNAL
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by using data from the Census from 1940 to 1980 to analyse cohorts born between 1910
and 1960.
During the 1960s in Norway, there was a drastic change in the compulsory schooling
laws affecting primary and middle schools. Pre-reform, the Norwegian education system required children to attend school through to the seventh grade; after the reform,
this was extended to the ninth grade, adding two years of required schooling. Implementation of the reform occurred in different municipalities at different times, starting
in 1960 and continuing through 1972, allowing for regional as well as time series
variation. Evidence in the literature suggests that these reforms had a large and significant impact on educational attainment.2 We study cohorts impacted by the reform –
women born between 1947 and 1958.
Our results suggest that increased compulsory schooling does seem to reduce the
incidence of teenage childbearing in both the US and Norway. These findings suggest
that policy interventions to increase female education at the lower tail of the educational distribution may be an effective means of reducing rates of teenage childbearing.
Once this relationship is established, it is then useful to attempt to understand the
mechanisms through which this relationship works. We examine two possible mechanisms. The first is the Ôincarceration effectÕ; to the extent that compulsory schooling
reduces the time available to engage in risky behaviour, the incidence of teenage
pregnancy might go down. The second is the Ôhuman capital effectÕ; additional education increases both current and expected future human capital and this higher level
of human capital could change fertility decisions. We describe these mechanisms in
more detail and discuss possible tests to distinguish between them. Our estimates
suggest that the effect of the laws on fertility is not just an ÔincarcerationÕ effect,
resulting also from the effects of the laws on human capital accumulation.
The article unfolds as follows. In Sections 1 and 2, we provide a short overview of the
literature and brief descriptions of the support systems for single mothers in Norway
and the US, as well as a description of the compulsory schooling law changes used for
identification. Sections 3 and 4 present our estimation strategy and the data sets used.
Section 5 presents the estimation results and robustness checks. In Section 6, attempts
are made to disentangle some possible explanations for a causal relationship between
compulsory schooling laws and fertility choice. Section 7 concludes.
1. Background Information
1.1. Previous Literature
Teenage motherhood has been associated with many long-term economic and health
disadvantages such as lower education, less work experience and lower wages, welfare
dependence, lower birth weights, higher rates of infant mortality and higher rates of
participation in crime (Ellwood, 1988; Jencks, 1989; Hoffman et al., 1993; Kiernan,
1997). There is an ongoing debate as to the extent that these adverse effects of teen
childbearing are truly caused by having a teen birth rather than reflecting unobserved
2
See Black et al. (2005). Results on the impact of similar reforms on educational attendance also exists for
Sweden, see Meghir and Palme (2005); for England and Ireland, see Harmon and Walker (1995) and
Oreopoulos (2003); and for Germany, see Pischke and von Wachter (2005).
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COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
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family background differences; see Hotz et al. (2005) for an example. However, the
balance of evidence suggests that at least part of the negative consequences of teen
births on mothers is causal (Klepinger et al., 1999; Angrist and Evans, 1996; Levine and
Painter, 2003). Thus, as a policy matter, efforts to reduce the rate of teen childbearing
are often considered as a strategy to improve the life chances of young women.
In addition to the effects of teen childbearing on mothers, there is also a literature
concerned with the negative effects on children. In recent work, Francesconi (2005)
takes a family fixed effects approach to show that children born to teenagers have
poorer outcomes as adults than children born to women when older. In addition, Hunt
(2006) provides evidence that children of teen mothers are more likely to engage in
crime. Thus, the policy interest in this topic also arises from presumed negative effects
on children.
Despite the policy relevance, there has been little work studying the role of education
policy in reducing teen fertility. A recent paper by McCrary and Royer (2006) focuses
on two states (California and Texas) and examines the effect of education on teenage
childbearing and child health by applying a regression discontinuity approach using
school starting-age rules. They find little evidence that the induced educational
changes affect children’s health or woman’s fertility choices. However, while their data
are very well suited for studying children’s health (administrative data on all births in
California and Texas from 1989 to 2001), it is less appropriate for focusing on teenage
fertility decisions (as it contains a select sample of those women who did in fact have
children). We attempt to enhance our understanding of the link between teenage
fertility and education by using data that is better suited for this particular question,
examining a broader region (the entire US and Norway), and using a different source
of variation by focusing on changes in dropout ages rather than school entry ages.
1.2. Institutional Setting
In addition to the fact that our identification strategy allows us to use large and representative data sets, another advantage of our study is that we can compare the effect
of changes in compulsory schooling laws on teenage fertility choice across two countries. Norway and the US are similar in that both have very high GDP per capita and
education levels but differ in terms of institutional environment; of particular importance are the welfare support systems for teenage mothers.3 Figure 1 shows the trends
in teenage childbearing in both countries; while teen birth rates are similar in the early
1970s, Norwegian teenage fertility rates have since fallen to be substantially below those
of the US.
The US system of support for teenage mothers is considered to be relatively
unsupportive when compared to many other industrialised countries. Established
under Title IV of the Social Security Act, Aid to Dependent Children was operated
3
US and Norwegian educational attainment is quite similar. According to the OECD, in 2003, approximately 95% of both Norwegian males and Norwegian females have completed at least an Upper Secondary
School Education; the corresponding numbers for the US are 86% and 89% (male and female, respectively).
Among 35–44 year olds, Norwegians males and females are at 91% and 92%, while US males and females are
at 87% and 89%. Finally, among 45–54 year olds, Norwegian males and females are at 85% and 84% while US
males and females are at 88% and 90%.
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THE ECONOMIC JOURNAL
United States
96
19
92
19
88
19
84
19
80
19
76
19
72
19
68
19
64
19
19
60
10
9
8
7
6
5
4
3
2
1
0
Norway
Fig. 1. Teenage Birth Rates Per 100 15–19 Year Olds
largely under state and local control (Baicker, 2005). Targeted primarily at the children
(and not the parents), eligibility was often limited by Ôsuitable homeÕ requirements
(stating that benefits could only be given when eligible children resided in a suitable
home), seasonal employment policies and illegitimacy exclusions. Although there is
significant variation across states, there is a common belief that it is not a generous
system relative to more socialised countries such as Norway.
In contrast, since the early 1960s, the relevant time period for the compulsory
schooling legislation change in Norway, the Norwegian welfare system has been very
generous (Rnsen and Strm, 1991). To enable single parents to take care of their
children without working, the government provides income support via the social
security system until the child is ten years of age (so long as the woman is not living with
the child’s father).4 The government also helps to enforce child support payments
from the father. In addition, the government pays all education expenses for the
mother (reimbursement is only partial if the woman is working) and provides subsidised housing and child care.5 Finally, single parents get double child allowances
from the government.6 In summary, the Norwegian system of support for single
mothers is very generous.
Access to contraception and abortion has changed in both countries in the past
40 years. Although the birth control pill was approved in 1960 by the Food and Drug
Administration and spread rapidly among married women, it was not until the late
1960s that it diffused among single women – with a series of changes in state legislation
reducing the age of majority and extending mature minor decisions; see Goldin and
Katz (2002) for more details. Thus, the pill influenced behaviour during the teenage
years of only the youngest cohorts in our US sample. In Norway, the birth control pill
was introduced in the late 1960s and spread quite quickly and so was available during
4
This system was introduced in 1964 and became a part of the social security system in 1971.
In 1990 the income support system was made less generous in order to provide incentives for work;
however, this is not relevant to the cohorts we study.
6
All parents get a child allowance in Norway (about 1000 NOK per year).
5
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COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1029
the teenage years of some of the later cohorts in the sample we study (Noack and Ostby,
1981).7
Abortion was not legalised in Norway until 1979. In the US, abortion was legalised in
1973 through the landmark Roe vs. Wade Supreme Court decision.8 As a result, almost
none of the women in either our Norwegian or US sample had access to legal abortion
during their teenage years.
2. The Compulsory Schooling Laws
2.1. Changes in US Compulsory Schooling Laws
Since the history of compulsory schooling laws in the US is by now well documented –
see, in particular, Lleras-Muney (2002) and Goldin and Katz (2003) – we will not
describe them in great detail here. Essentially, there were five possible restrictions on
educational attendance:
1
2
3
4
5
maximum age by which a child must be enrolled,
minimum age at which a child may drop out,
minimum years of schooling before dropping out,
minimum age for a work permit, and
minimum schooling required for a work permit.
In the years relevant to our sample, 1924 to 1974, states changed compulsory
attendance laws many times, usually upwards but sometimes downwards.9 Appendix
Table A1 shows the minimum dropout age by states over time. Although there is
variation, there is also substantial persistence, highlighting the importance of adjusting
standard errors for clustering at the state level.10 We follow Acemoglu and Angrist
(2001) and Lochner and Moretti (2004) in assigning compulsory attendance laws to
women on the basis of state of birth and the year when the individual was 14 years old
(with the exception that the enrolment age is assigned based on the laws in place when
the individual was 7 years old).
Papers on the topic have used a variety of combinations of these restrictions as their
measures of compulsory schooling. To be consistent with the source of variation in our
Norwegian data, our baseline specification will examine the effect of the minimum
dropout age on teenage pregnancy. As a specification check, we will also examine the
sensitivity of our results to the use of required years of schooling, defined as the
difference between the minimum dropout age and the maximum enrolment age
following Lleras-Muney and Goldin and Katz, as well as to the inclusion of the minimum age for a work permit.
7
Interestingly, we have examined the effects of the compulsory schooling legislation on earlier cohorts
only and find similar effects, suggesting that this changing environment has no significant impact on our
results.
8
Abortion was legal in New York, California, Washington, Hawaii and Alaska beginning in 1970. See
Levine (2004a, b) for more details.
9
While there were some exemptions to the compulsory schooling laws, we have no knowledge of any
exemption in any state for pregnant women. However, it was not unusual for women who became pregnant to
be asked to leave school.
10
Some large states made no changes to the dropout age over the sample period. Thus, in our later
regressions, about 60% of observations come from states in which there was no change in the dropout laws.
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Lleras-Muney (2002) thoroughly investigates the relationship between changes in
compulsory schooling laws and other state-level variables. She finds no evidence that
the relationship between the laws and education is related to manufacturing wages,
manufacturing employment, expenditures on education, or demographic characteristics of the population. In the robustness checks in Section 5, we carry out several checks
that suggest that the relationship between compulsory schooling laws and early fertility
is robust to the presence of state-year trends, different weights, the inclusion of labour
market characteristics and different ways of measuring compulsory schooling.
2.2. The Norwegian Primary School Reform
In 1959, the Norwegian Parliament legislated a mandatory school reform that
increased the minimum level of education in society by extending the number of
compulsory years of education from 7 to 9 years (thereby increasing the minimum
dropout age from 14 to 16, as students started at age 7); there were no exemptions to
these laws. Prior to the reform, children started school at the age of 7 and finished
compulsory education after 7 years, i.e. at the age of 14. In the new system, the
starting age was still 7 years old, but the time spent in compulsory education was now
9 years. In addition, the reform standardised the curriculum and increased access to
schools, since 9 years of mandatory school was eventually made available in all
municipalities.
The parliament mandated that all municipalities (the lowest level of local administration) must have implemented the reform by 1973; as a result, although it was started
in 1960, implementation was not completed until 1972.11 This suggests that, for more
than a decade, Norwegian schools were divided into two separate systems; which system
you were in depended on the year you were born and the municipality in which you
lived. The first cohort that could have been involved in the reform was the one born in
1947. They started school in 1954, and either
(i) finished the pre-reform compulsory school in 1961, or
(ii) Went to primary school from 1954 to 1960, followed by the post-reform middle
school from 1960 to 1963.
The last cohort who could have gone through the old system was born in 1958. This
cohort started school in 1965 and finished compulsory school in 1972.
To receive funds from the government to implement the reform, municipalities had
to present a plan to a committee under the Ministry of Education. Once approved, the
costs of teachers and buildings were provided by the national government. While the
criteria determining selection by the committee are somewhat unclear, the committee
did want to ensure that implementation was representative of the country, conditional
on having an acceptable plan. (Telhaug, 1969; Mediås, 2000).12 Appendix Figure A1
11
The reform had already started on a small and explorative basis in the late 1950s but applied to a
negligible number of students because only a few small municipalities, each with a small number of schools,
were involved. See Lie (1974), Telhaug (1969) and Lindbekk (1992), for descriptions of the reform.
12
Similar school reforms were undertaken in many other European countries in the same period, notably
Sweden, the UK and, to some extent, France and Germany (Leschinsky and Mayer, 1990).
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COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1031
presents the spread of the reform over time, focusing on the number of municipalities
implementing the reform per year.
While it is not necessary for our estimation strategy because of the inclusion of
municipality fixed effects, it would be useful if the timing of the implementation of the
reform across municipalities were uncorrelated with teenage pregnancy rates, our
outcome of interest. To test this, we examine the relationship between the timing of
the reform (by municipality) and teenage pregnancy rates prior to the reform (1960).
We also look at other characteristics that might be associated with teenage pregnancy
rates. For example, one might think that poorer municipalities would be among the
first to implement the reform, given the substantial state subsidies, while wealthier
municipalities would move much slower. However, work examining the determinants
of the timing of implementation finds no relationship between municipality characteristics such as average earnings, taxable income and educational levels, and the
timing of implementation; see Lie (1973, 1974).13 To examine this ourselves, Appendix
Figures A2, A3, A4, and A5 examine the implementation of the reform by the average
income, parental education, the size of the municipalities and the teenage birth rate;
these figures suggest that there is little relationship between these factors and the
timing of the implementation of the reform.
As a more rigorous test, in Appendix Table A3 we regress the year of implementation
on different background variables based on 1960 municipality averages, Consistent with
the existing literature, there appears to be no systematic relationship between the
timing of implementation and the teenage birth rate, parent average earnings, education levels, average age, urban/rural status, industry or labour force composition,
municipality unemployment rates in 1960, and the share of individuals who were
members of the Labour party (the most pro-reform and dominant political party).14
3. Empirical Methodology: Probability of Having First Birth as a Teenager
In both the US and Norway, there is time-series as well as cross-sectional variation in the
number of years of compulsory schooling required of individuals during the periods
studied.
3.1. US Model
The empirical model for the United States is as follows:
TEENBIRTH ¼ a0 þ a1 COMPULSORY þ a2 COHORT þ a3 STATE þ a4 WHITE þ t ð1Þ
where COHORT refers to a full set of year of birth indicators, STATE refers to a full set
of state indicators and WHITE is a dummy indicator for whether the woman is white.
For the US, COMPULSORY is a vector of three dummy variables describing the
minimum dropout age in a state, with a minimum dropout age of less than 16 as the
13
Municipalities that are located geographically near municipalities that already implemented the reform
were themselves more likely to implement the reform; numerous interviews revealed that this was likely due to
a particularly effective county administrator. As a result, the research supports a complex adoption process
without finding support for a single important factor to explain the implementation process.
14
We also include 20 county dummies in the regression.
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omitted category (usually the dropout age in this case was 14 or 15). Because
TEENBIRTH is a binary indicator for whether the woman had her first birth as a
teenager, we estimate the model using maximum likelihood probit.15
It is important to note that we are including both cohort and state effects. The cohort
effects are necessary to allow for secular changes in educational attainment over time
that may be completely unrelated to compulsory schooling laws. The state effects allow
for permanent differences in fertility behaviour across states that might be correlated
with the strength of compulsory schooling laws.
3.2. Norway Model
We use a similar specification for the Norwegian data, replacing the state dummies with
municipality dummies. The specification is as follows:
TEENBIRTH ¼ a0 þ a1 COMPULSORY þ a2 COHORT þ a3 MUNICIPALITY þ t:
ð2Þ
For Norway, COMPULSORY equals 1 if the individual was affected by the education
reform (minimum dropout age of 16), and 0 otherwise (minimum dropout age of
14).16 Again, cohort effects are quite important since the income support system for
single mothers changed somewhat over time and we want to compare the effect of the
compulsory schooling laws on teenage fertility within cohorts.
4. Data
4.1. United States
We use the IPUMS extracts from the decennial Census from 1940 to 1980. The
particular samples we use are the 1% 1940 sample, the 1% 1950 sample, the 1% 1960
sample, the two 1% 1970 state samples, and the 5% 1980 sample. Analysis using the
Census is complicated by the fact that children are only observed if they are living in the
household with their mother. It is possible to link mothers to their children in these
data and use the age of the eldest own child in the household to determine the age at
which the mother first gave birth. We omit women from the sample if their first birth
occurred before age 15 because births at age 14 or younger are extremely rare and
unlikely to be influenced by laws that determine whether the dropout age is 16 or
higher. Since children tend to start leaving home about age 16, this implies that we can
only get an accurate count on teenage births for the sample of women aged no more
than about 31 (15 þ 16). Thus, we restrict our Census sample to women aged between
20 and 30.
15
We choose probit rather than the linear probability model because of the well-known problems with
using OLS for binary dependent variables; see Horrace and Oaxaca (2006). In practice, the choice between
these tends not to make much difference to our results. The linear probability model estimates are a little
different from the probit marginal effects for the US specifications but almost identical to the probit ones for
the Norwegian data. One feature of probit estimation is that cases are dropped if they are perfectly predicted
to be a one or zero. In the Tables we report the sample sizes that are actually used in estimation i.e. the
number of undropped observations. In the US data, no observations are dropped for this reason; in the
Norwegian data, the issue arises only for births at ages 16 and 17.
16
Note that we do not include race dummies for Norway as there is very little variation in race in Norway
during this period.
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For most of our sample (1960–80), the data include quarter of birth and we use this
variable to determine the woman’s age at first birth to within 3 months. For the 1940
and 1950 samples, we do not observe quarter of birth and so age at first birth is known
to within a year. As is standard in the literature, we assign the compulsory schooling law
indicators on the basis of state of birth rather than state of residence. We do so because
mobility across states may be influenced by educational attainment and hence by the
compulsory schooling laws. Random mobility at any point after birth may imply that an
individual is not actually impacted by the laws that we think they are; this creates a
measurement error problem that will tend to bias our estimates of the effects of the
laws towards zero.
4.2. Norway
Based on different administrative registers and census data from Statistics Norway,
a comprehensive data set has been compiled of the entire population in Norway,
including information on family background, age, marital status, educational history,
and employment information.17 Note that, unlike with the US data, we are able to
observe all children and not just those living in the household.
The initial database is linked administrative data that covers the entire population of
Norwegians aged 16–74. These administrative data provide information about educational attainment, labour market status and a set of demographic variables (age,
gender).
To determine whether women were affected by the compulsory schooling legislation, we need to link each woman to the municipality in which she grew up. We do
this by matching the administrative data to the 1960 census. From the 1960 census,
we know the municipality in which the woman’s mother lived in 1960.18 In 1960, the
women we are using in the estimation are aged between 2 and 13.19 As in the US
case, random mobility at any point after we assign location may imply that an individual is not actually impacted by the reform although we think they are. This creates
a measurement error problem that will tend to bias our estimates of the effects of the
reform towards zero.
Our primary data source on the timing of the reform in individual municipalities is
the volume by Ness (1971). To verify the dates provided by Ness, we examined the data
to determine whether or not there appears to be a clear break in the fraction of
students with less than 9 years of education. In the rare instance when the data did not
seem consistent with the timing stated in Ness, we checked these individual municipalities by contacting local sources. If the reform took more than one year to implement
in a particular municipality or we were not able to verify the information given in
Ness (1971), we could not assign a reform indicator to that municipality and the
17
See Men et al. (2003) for a description of the data set.
Since very few children live with their father in the cases where parents are not living together, we should
only have minimal misclassification by applying this rule.
19
One concern is that there may be selective migration into or out of municipalities that implement the
reform early. However, since the reform implementation did not occur before 1960, reform-induced mobility
should not be a problem for us. Evidence from Meghir and Palme (2003) on Sweden and Telhaug (1969) on
Norway suggest that reform-induced migration was not a significant consideration.
18
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municipality was dropped from our sample. We are able to calculate reform indicators
successfully for 545 out of the 728 municipalities in existence in 1960.
We include cohorts of women born between 1947 and 1958 in our sample. For these
women, we observe their children in 2000. From the year and month of birth of the
children and the year and month of birth of the mother, we can determine the age of
the mother at her first birth to the nearest month. We exclude from our sample the
small number of women who have a first birth before age 15 (since individuals aged 14
or younger face compulsory schooling before and after the reform) and we define a
teenage birth as one occurring when the mother has not yet reached her 20th birthday
at the birth of her first child.
4.3. Descriptive Statistics
Table 1 provides summary statistics for the women in our sample. First consider the US
data. About 4% of women in the sample faced a dropout age of less than 16, 75% had a
minimum dropout age of 16, 12% had a dropout age of 17 and 9% had a minimum
dropout age of 18. Also, we see that 17% of women have their first birth as a teenager.
In the Norwegian data, we see that 52% of women are affected by the reform. Similar
to the US, 17% of women have their first birth as a teenager.
4.4. Effect of Laws on Educational Attainment
To provide some background, we assess the impact of the compulsory schooling laws
on educational attainment by regressing completed education on the laws and on the
cohort dummies and state dummies (for the US) and municipality dummies (for
Norway).20 The results are presented in Appendix Table A2.
Consistent with our earlier work on Norway (Black et al., 2005), we estimate a coefficient on the reform of 0.122 (0.022) indicating that, on average, education
increased by 0.12 of a year as a result of the law change. In the US, the coefficient on
Dropout Age ¼ 16 is 0.404, suggesting that the educational impact of a similar change
in the US is bigger than that in Norway (however, the US estimate is quite imprecise
and is statistically insignificant).
Readers may find it surprising that we find no statistically significant relationship
between US compulsory schooling laws and educational attainment. Many previous
studies have used these laws as instruments for education and reported very strong first
stage relationships, for example, Lochner and Moretti (2004) and Lleras-Muney
(2005). This discrepancy appears to arise because we cluster our standard errors at the
state level while these other papers cluster at the state-year level.21 In the third column
of Appendix Table A2, we report estimates when we cluster at the state-year level and
the standard errors are about four times lower. This probably reflects the long
time-series component to our state year panel and the presence of serial correlation
(Bertrand et al., 2004). It is important to note, however, that although we do not find
20
We restrict our US sample to women aged between 22 and 30 in order to reduce the problem of
censored educational attainment.
21
Goldin and Katz (2003) also cluster at the state level and they find marginally significant effects of the
laws on educational attainment during the early part of the twentieth century.
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Table 1
Descriptive Statistics
Variable
Mean
Std. Dev.
Min
Max
US
Birth cohort
Age at census
Education
White
Child before 17
Child before 18
Child before 19
Child as teenager
Child before 21
Dropout age is <16
Dropout age is 16
Dropout age is 17
Dropout age is 18
Enrolment age is 6
Enrolment age is 7
Enrolment age is 8þ
N ¼ 1,584,094
1948.14
24.80
12.30
0.86
0.02
0.06
0.11
0.17
0.24
0.04
0.75
0.12
0.09
0.14
0.66
0.20
12.34
3.16
2.52
0.34
0.15
0.23
0.31
0.38
0.43
0.19
0.43
0.32
0.28
0.35
0.47
0.40
1910
20
0
0
0
0
0
0
0
0
0
0
0
0
0
0
1960
30
17
1
1
1
1
1
1
1
1
1
1
1
1
1
Norway
Birth Cohort
Age in 2000
Education
Child before 17
Child before 18
Child before 19
Child as teenager
Child before 21
Reform implemented
N ¼ 260,641
1953
47.01
11.50
0.01
0.04
0.09
0.17
0.25
0.52
3.35
3.35
2.58
0.09
0.19
0.29
0.38
0.43
0.50
1947
42
5
0
0
0
0
0
0
1958
53
21
1
1
1
1
1
1
statistically significant effects, our standard errors are large, so we cannot rule out large
effects of compulsory schooling on educational attainment.
5. Results for the Probit Models
In order to provide a visual representation of the effect we are estimating, Figures 2
and 3 present event-study style graphs of teenage pregnancy rates before and after
changes in compulsory schooling laws.22 Time zero represents the year of
implementation of the reform. While it is clear that there is some measurement error
associated with the change in the compulsory schooling laws (as exhibited by the sharp
decline in fertility over a two-year period, from 2 to 0), these graphs also demonstrate
the (relatively) discrete change in fertility around the changes in compulsory
schooling.
22
These calculations are based on linear probability models that include state/municipality and year
effects. All observations are included in the Norwegian analysis. For the US, we only use data within 10 years
of an observed law change, we treat all changes in laws in a binary fashion irrespective of what exactly the
change is, and we treat reductions in compulsory schooling requirements symmetrically to increases. Because
of these necessary simplifications, and because of the substantial uncertainty about each individual point
estimate, the US figure in particular should be interpreted with caution.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1036
[JULY
THE ECONOMIC JOURNAL
0.014
0.012
0.01
0.008
0.006
0.004
0.002
0
–0.002
–0.004
–0.006
–5
–4
–3
–2
–1
0
1
2
3
4
Fig. 2. Effect of Compulsory Schooling Law on Teenage Pregnancy, US
0.008
0.006
0.004
0.002
0
–5
–4
–3
–2
–1
0
1
2
3
4
–0.002
–0.004
–0.006
Fig. 3. Effect of Compulsory Schooling Law on Teenage Pregnancy, Norway
The probit marginal effects of compulsory schooling on teenage childbearing (1) are
presented in Table 2.23 The marginal effects for the US are in the top panel. These
numbers reflect the effect of the minimum dropout age specified by the compulsory
schooling law on the probability of having the first birth before each age. To assess the
magnitude of the coefficients, it is important to know the probabilities of births during
these years: The percentage of women who have their first birth before 17 is 2%, before
18 is 6%, before 19 is 11%, before 20 is 17%, and before 21 is 24% (See Table 1). We
find no evidence that the small probability of having a first birth before age 17 is
influenced by the laws. However, the results in the other 4 columns suggest that the
laws have a significant negative effect on the probability of having a first child before
ages 18 to 21. The magnitude of the effects is also quite large. The coefficient of 0.008
on Dropout Age ¼ 16 in the fourth column implies that the effect of compelling
women to stay in school until 16 is to reduce the probability of a teen birth by 4.7%
((0.008100)/0.17). The effect of imposing a law mandating women to stay in school
23
In all the probit models, we report robust standard errors that allow for clustering at the state level in the
US and the municipality level in Norway. Estimates across columns in Table 2 are not independent so one
cannot compare coefficient values across rows using normal inference procedures.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1037
Table 2
Effect of Compulsory Schooling Laws on the Probability of First Birth by A Certain Age:
Probit Marginal Effects
Dependent Variable:
US
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log likelihood
N ¼ 1,584,094
Norway
Reform
Log likelihood
N ¼ 260,641
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.00002
(0.0009)
0.0008
(0.0011)
0.0012
(0.0014)
0.0421*
(0.0029)
171,562
0.0025
(0.0017)
0.0053*
(0.0022)
0.0004
(0.0060)
0.0749*
(0.0053)
330,737
0.0058*
(0.0018)
0.0106*
(0.0027)
0.0004
(0.0128)
0.1035*
(0.0077)
516,080
0.0077*
(0.0024)
0.0147*
(0.0031)
0.0023
(0.0147)
0.1222*
(0.0094)
700,314
0.0095*
(0.0047)
0.0186*
(0.0050)
0.0085
(0.0153)
0.1275*
(0.0106)
847,981
0.0006
(0.0006)
11,456
0.0020
(0.0015)
39,160
0.0047*
(0.0024)
77,676
0.0063
(0.0037)
114,677
0.0087*
(0.0043)
143,187
Notes. Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate
regression. Also included in the specifications are year-of-birth indicators. The US specifications also include
state dummies; the Norway specifications include municipality indicators. Standard errors are all adjusted for
clustering at the state/municipality level. The number of observations actually used in the Norwegian estimation after observations with perfectly predicted outcomes are eliminated is 239,535 for Birth by Age 16 and
259,588 for Birth by Age 17.
*denotes statistically significant at the 5% level.
until 17 is to reduce the probability of a teen birth by 8.8% ((0.015100)/0.17). In
contrast, we do not find any significant effect of having a minimum dropout age of 18.
However, the standard errors are very high for this variable.
The proportion of first births by age in our Norwegian sample is as follows: 1%
before age 17, 4% before age 18, 9% before age 19, 17% before age 20, and 25% before
age 21 (See Table 1). The probit marginal effects for Norway are in the second panel of
Table 2. Note that the effect of the reform was to increase the minimum dropout age
from 14 to 16 in Norway. Once again, there is evidence that the compulsory schooling
law reduced the likelihood of births during the teenage years. The marginal effects
imply that the implementation of the reform reduced the probability of a first birth as a
teenage by about 3.5% ((0.006100)/0.17). This is similar but somewhat smaller than
the 4.7% effect of Dropout Age ¼ 16 in the United States. Generally, the effects of the
reform in Norway are very similar to those of Dropout Age ¼ 16 in the United States.24
24
Researchers often use compulsory schooling laws as instruments for education. This is less compelling
when studying teen fertility than it is for adult outcomes as it involves modelling fertility decisions at, say, age
17 as functions of educational decisions that may be made at much older ages. However, for completeness, we
have used 2SLS to estimate the effects of education on teen childbearing for Norway. (As can be seen in
Appendix Table A2, the first stage is too weak to do this analysis for the US). For Norway, we find a 2SLS
estimate of 0.051 (0.030) for the effects of years of education on the probability of a teen birth, implying
that education has a substantial impact.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1038
THE ECONOMIC JOURNAL
[JULY
To understand our results better, we stratify our sample based on the urban/rural
status of the individuals. One might expect enforcement to be easier in urban areas and
hence the laws may have a larger impact.25 While we can get a precise breakdown of the
urban/rural status in our Norwegian data using the metropolitan status of the individuals from the 1960 census, it is more difficult for the US data. As a proxy for the
urban/rural status in the US, we are forced to use the status at the time of the Census,
when women are aged between 20 and 30. Given that there is significant mobility, we
view this as a rough proxy for the actual urban/rural status of the individual when she
was in school.26
As one might have predicted, the results, presented in Table 3, appear to be stronger
for the urban sample. This is particularly true for Norway, where the effects are much
larger for the urban sample. While the rural results are roughly consistent, they are
never statistically significant. We also tried stratifying our US sample based on the race
of the individual; when we do this, it becomes clear that the compulsory schooling laws
had a more significant effect on teenage childbearing among whites. The results for
non-whites were never statistically significant. This is consistent with the work of Goldin
and Katz (2003) who find smaller effects of compulsory schooling laws on educational
attainment for blacks than whites.27
It is important to note that, although in the US we observe relatively large effects
of compulsory schooling on teenage pregnancy for laws requiring attendance until
age 17, this law does not affect a large fraction of our sample. Thus, our estimates
can explain very little of the aggregate changes in teen fertility shown in Figure 1.
For example, in the US between our 1960 and our 1980 census samples, the
proportion having their first birth as a teen fell from 0.22 to 0.16. Using our
estimates and the changes of compulsory schooling laws over that period,
one would predict the proportion of teen births to fall by less than 0.001 or about
half of 1% of the actual fall. This implies that compulsory schooling legislation has
had a relatively inconsequential effect on changes in teenage fertility rates over
time.
5.1. Robustness/Specification Checks
We have carried out numerous specification checks to verify our findings. They are as
follows.
5.1.1. Inclusion of state-year trends
Because we are identifying off of variation in compulsory schooling across states over
time, it is not possible to include state by time dummies. However, we can allow for
state-specific trends (in the Norwegian case, municipality-specific trends). When we
25
We estimate a larger effect of the laws on educational attainment for urban individuals but the urban/
rural difference is not statistically significant.
26
In the US, we define urban as being resident in a metropolitan area. In Norway, individuals are classified
as urban if their mother lived in one of the main cities and towns in 1960.
27
There was not a significant enough minority population in Norway at the time to enable us to stratify
along these lines.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1039
Table 3
Effect of Compulsory Schooling Laws on the Probability of Birth: Urban/Rural Distinction
US
Urban
N ¼ 1,063,181
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log Likelihood
Rural
N ¼ 520,913
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log likelihood
Norway
Urban
N ¼ 87,752
Reform
Log likelihood
Rural N ¼ 172,889
Reform
Log likelihood
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.0007
(0.0009)
0.0003
(0.0012)
0.0028
(0.0024)
0.0448*
(0.0034)
105,405
0.0016
(0.0017)
0.0057*
(0.0018)
0.0025
(0.0084)
0.0818*
(0.0064)
201,625
0.0019
(0.0030)
0.0100*
(0.0029)
0.0068
(0.0173)
0.1166*
(0.0093)
315,431
0.0031
(0.0055)
0.0146*
(0.0052)
0.0012
(0.0071)
0.1425*
(0.0114)
431,521
0.0030
(0.0089)
0.0163
(0.0087)
0.0033
(0.0182)
0.1556*
(0.0127)
529,597
0.0008
(0.0016)
0.0007
(0.0020)
0.0007
(0.0032)
0.0376
(0.0017)
65,576
0.0002
(0.0033)
0.0033
(0.0038)
0.0004
(0.0040)
0.0643
(0.0028)
127,696
0.0039
(0.0034)
0.0066
(0.0047)
0.0020
(0.0053)
0.0830
(0.0041)
197,982
0.0029
(0.0037)
0.0003
(0.0053)
0.0089
(0.0095)
0.0924
(0.0051)
264,364
0.0031
(0.0064)
0.0097
(0.0084)
0.0061
(0.0115)
0.0862
(0.0054)
312,116
0.0010
(0.0010)
3,643
0.0053*
(0.0026)
11,606
0.0094*
(0.0038)
22,833
0.0212*
(0.0067)
34,015
0.0275*
(0.0089)
43,349
0.0035
(0.0008)
7,805
0.0005
(0.0016)
27,543
0.0027
(0.0028)
54,822
0.0008
(0.0035)
80,626
0.0003
(0.0041)
99,803
Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate regression.
Also included in the specifications are year-of-birth indicators. The US specifications also include state
dummies; the Norway specifications include municipality indicators. Standard errors are all adjusted for
clustering at the state/municipality level.
The number of observations actually used in the Norwegian estimation after observations with perfectly
predicted outcomes are eliminated is 87,286 for Birth by Age 16 for the Urban sample and 152,249 for Birth
by Age 16 and 171,836 for Birth by Age 17 for the Rural sample.
*Denotes statistically significant at the 5% level.
include these trends (Table 4), we get estimates that are quite similar to those in
Table 2.28
5.1.2. Alternative weighting schemes
When using the US Census data, we have 1% samples from 1940, 1950, and 1960, a 2%
sample from 1970 and a 5% sample from the 1980 data. As a result, we are giving more
weight to the most recent cohorts. If there is no difference in the effect of compulsory
28
We have also tried adding state of residence fixed effects and Census year fixed effects in the US sample
and these have had little effect on the estimates.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1040
[JULY
THE ECONOMIC JOURNAL
Table 4
Effect of Compulsory Schooling Laws on the Probability of Birth Including State-Year
Trends
Dependent Variable:
US
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log likelihood
N ¼ 1,584,094
Norway
Reform
Log likelihood
N ¼ 260,641
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.0016*
(0.0006)
0.0008
(0.0011)
0.0042*
(0.0018)
0.0417*
(0.0028)
171,467
0.0003
(0.0016)
0.0032
(0.0019)
0.0020
(0.0079)
0.0744*
(0.0052)
330,582
0.0036
(0.0031)
0.0072
(0.0037)
0.0003
(0.0037)
0.1031*
(0.0076)
515,919
0.0086*
(0.0040)
0.0131*
(0.0046)
0.0087
(0.0177)
0.1219*
(0.0093)
700,142
0.0151*
(0.0060)
0.0233*
(0.0072)
0.0175
(0.0187)
0.1274*
(0.0106)
847,826
0.0002
(0.0002)
11,175
0.0015
(0.0015)
38,830
0.0046*
(0.0021)
77,265
0.0049
(0.0028)
114,222
0.0063
(0.0034)
142,695
Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate regression.
Also included in the specifications are year-of-birth indicators. The US specifications also include state
dummies; the Norway specifications include municipality indicators. Standard errors are all adjusted for
clustering at the state/municipality level. The number of observations actually used in the Norwegian estimation after observations with perfectly predicted outcomes are eliminated is 239,535 for Birth by Age 16 and
259,588 for Birth by Age 17.
*Denotes statistically significant at the 5% level.
schooling laws on teenage childbearing over time, the results should be the same
whether we weight each cohort equally or not. This, however, is testable. In Table 5, we
present the results when we weight each cohort equally (thereby weighting each
observation by the inverse of the number of individuals in that cohort in our sample).
While the results are consistent with those in Table 2, it does seem that, when more
weight is placed on the earlier periods, the more stringent compulsory schooling laws
are more effective.
5.1.3. Effect of future laws on current fertility
Future law changes should have no impact on current fertility behaviour. If they do, it
would suggest that something other than changes in compulsory schooling may be
driving our results. To check this, we have calculated the minimum dropout ages that
exist 10 years into the future, and have added these to the specification. The estimates
are in Table 6.29 Although we see that there are three instances where the future laws
have a statistically significant effect on fertility behaviour (one negative effect, and two
positive effects), the addition of the future laws does not change the effects of the
actual laws. If anything, the results are strengthened by the addition of the future laws,
29
The sample size is smaller in Table 5 because the compulsory schooling law file finishes in 1978 and so
we cannot calculate the dropout ages ten years into the future for cohorts born after 1964.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1041
Table 5
Effect of Compulsory Schooling Laws on the Probability of Birth: Equal Weighting of
Cohorts: Probit Marginal Effects, US
Dependent Variable:
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log likelihood
N ¼ 1,584,094
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.0001
(0.0009)
0.0017
(0.0012)
0.0004
(0.0012)
0.0354*
(0.0023)
5.487e þ 08
0.0008
(0.0023)
0.0051
(0.0025)
0.0099*
(0.0039)
0.0606*
(0.0046)
1.053e þ 09
0.0023
(0.0033)
0.0104*
(0.0038)
0.0202*
(0.0088)
0.0803*
(0.0072)
1.661e þ 09
0.0051
(0.0039)
0.0185*
(0.0060)
0.0294
(0.0149)
0.0853*
(0.0088)
2.279e þ 09
0.0079*
(0.0039)
0.0248*
(0.0052)
0.0365*
(0.0115)
0.0765*
(0.0103)
2.785e þ 09
Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate regression.
Also included in the specifications are year-of-birth indicators and state dummies. Standard errors are all
adjusted for clustering at the state level.
suggesting that the change in fertility we observe is in fact caused by the change in
compulsory schooling laws.
5.1.4. Effect of compulsory schooling on older women
Although there may be some spillover effects of compulsory schooling laws, it would be
surprising if we found very large effects of compulsory schooling on the fertility
decision of women in their 20s. When we estimate the effect of compulsory schooling
laws on the fertility decisions of 21–25 year old (and then separately for 23–25 year old)
women with no prior birth, we find very small and statistically insignificant effects in
both the US and Norway. This reinforces the idea that our results are not being driven
by omitted state-specific characteristics.
5.1.5. Alternative measures of compulsory schooling
While we have used the minimum dropout age as our indicator for compulsory
schooling in the US, other work has used a variety of measures and we test the
sensitivity of our results to this choice. To do so, we apply the same estimation
strategy but use the required number of years of schooling (defined as the minimum dropout age minus the maximum enrolment age 7 years prior) as our
measure of compulsory education instead. We split the years of compulsory
schooling into 4 categories – less than 9, 9, 10, and 11 or more. We exclude the less
than 9 category from the specification. Table 7 presents these results. Consistent
with our earlier findings, the estimates show that the probability of early childbearing is negatively affected by the number of years of compulsory education. The
results for years of compulsory schooling are robust to all the specification checks
discussed above.
In Table 8, we report estimates where we use the minimum age at which an individual could get a work permit as our measure of compulsory schooling. We include
two dummy variables – one for whether the dropout age was 15 and the other for
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1042
[JULY
THE ECONOMIC JOURNAL
Table 6
Effect of Compulsory Schooling Laws on the Probability of Birth Including Future
Legislation: Probit Marginal Effects, US
Dependent Variable:
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
FutureLaws
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log likelihood
N ¼ 1,001,121
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.0006
(0.0008)
0.0002
(0.0008)
0.0012
(0.0015)
0.0024
(0.0018)
0.0050*
(0.0016)
0.0076*
(0.0032)
0.0051*
(0.0020)
0.0101*
(0.0019)
0.0174*
(0.0073)
0.0087*
(0.0025)
0.0175*
(0.0027)
0.0215
(0.0148)
0.0113*
(0.0051)
0.0236*
(0.0051)
0.0315*
(0.0133)
0.0002
(0.0007)
0.0010
(0.0014)
0.0041*
(0.0015)
0.0403*
(0.0030)
107,232
0.0027
(0.0020)
0.0008
(0.0028)
0.0006
(0.0030)
0.0728*
(0.0057)
209,129
0.0047
(0.0022)
0.0010
(0.0030)
0.0004
(0.0035)
0.1013*
(0.0085)
332,203
0.0105*
(0.0039)
0.0013
(0.0050)
0.0052
(0.0054)
0.1170*
(0.0102)
458,272
0.0127*
(0.0060)
0.0042
(0.0072)
0.0073
(0.0072)
0.1181*
(0.0113)
557,592
Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate regression.
Also included in the specifications are year-of-birth indicators and state dummies. Standard errors are all
adjusted for clustering at the state level.
*Denotes statistically significant at the 5% level.
whether the age was greater than 15. The omitted category is a dropout age of less than
15. We find that the presence of a dropout age of 15 has a statistically significant
negative effect on early fertility. Overall, we find that changes in compulsory schooling
laws impact fertility, irrespective of how they are defined.30
5.1.6. Inclusion of labour market controls
A final concern may be that our results are picking up other factors that are occurring
in the state or municipality and that are correlated with changes in compulsory
schooling laws. As a check of this, we estimate our regressions controlling for labour
market characteristics. In the US, these are the proportion of people working in
farming in the state, the proportion working in manufacturing in the state and the
labour force participation rate in the state. Unfortunately, these variables are calculated
from the census every 10 years and values for the inter-census years are interpolated
using a linear model. When we control for these variables, our results weaken somewhat
and become much noisier; this is likely because the required interpolation causes the
labour market variables to be highly persistent and highly collinear with the alsopersistent law variables. For Norway, we include a control for the municipality unemployment rate, the only variable we have that varies by municipality and year over the
30
Recent work by Goldin and Katz (2003) suggests that child labour laws may be more significant than the
compulsory schooling laws in terms of affecting school attendance. However, in our sample, this is not the
case; among women in our sample, the compulsory schooling laws were as effective as the child labour laws in
influencing fertility.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1043
Table 7
Effect of Compulsory Schooling Laws on the Probability of Birth: Required Years of
Schooling (Minimum Dropout Age-Maximum Enrolment Age), US Data
Dependent Variable:
9 Years of Schooling
10 Years of Schooling
11þ Years of Schooling
White
Log Likelihood
N ¼ 1,584,094
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.0006
(0.0010)
0.0006
(0.0011)
0.0020
(0.0024)
0.0421*
(0.0029)
171,563
0.0044*
(0.0016)
0.0047*
(0.0023)
0.0054
(0.0054)
0.0748*
(0.0053)
330,734
0.0085*
(0.0019)
0.0089*
(0.0035)
0.0073
(0.0103)
0.1034*
(0.0077)
516,075
0.0122*
(0.0025)
0.0114*
(0.0047)
0.0148
(0.0123)
0.1222*
(0.0094)
700,307
0.0140*
(0.0032)
0.0167*
(0.0046)
0.0174
(0.0137)
0.1275*
(0.0106)
847,972
Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate regression.
Also included in the specifications are year-of-birth indicators and state dummies. Standard errors are all
adjusted for clustering at the state level.
Table 8
Effect of Child Labour Laws on the Probability of Birth, US Data
Dependent Variable:
Dropout age ¼ 15
Dropout age >15
White
Log Likelihood
N ¼ 1,584,094
Birth by
Age 16
Birth by
Age 17
Birth by
Age 18
Birth by
Age 19
Birth by
Age 20
0.0006
(0.0007)
0.0003
(0.0012)
0.0421*
(0.0029)
171,564
0.0043*
(0.0010)
0.0013
(0.0023)
0.0749*
(0.0053)
330,742
0.0100*
(0.0012)
0.0018
(0.0037)
0.0103
(0.0077)
516,089
0.0137*
(0.0021)
0.0000
(0.0050)
0.1222*
(0.0094)
700,324
0.0097
(0.0062)
0.0006
(0.0057)
0.1276*
(0.0107)
848,001
Estimates are marginal effects from probit maximum likelihood. Each column denotes a separate regression.
Also included in the specifications are year-of-birth indicators and state dummies. Standard errors are all
adjusted for clustering at the state level.
*Denotes statistically significant at the 5% level.
12-year period we are using. When we include this variable, our results remain essentially unchanged.
6. Why Do Compulsory Schooling Laws affect Timing of Births?
Given that we find an effect of compulsory schooling laws on teenage fertility, the next
step it to try to uncover mechanisms through which this relationship is working.
Consider a static model of schooling and fertility decisions. At the beginning of their
teenage years, young women choose their schooling level and their fertility behaviour.
In the absence of institutional constraints, these decisions are made optimally and
depend on the utility function of each individual as well as her ability. If, however,
a compulsory schooling law is in place, this constrains the educational choice of some
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1044
THE ECONOMIC JOURNAL
[JULY
women and leads them to choose greater education than would have been chosen
otherwise. In turn, this new optimal educational level may be associated with a new set
of fertility choices.31
In particular, because it is likely to be quite costly to be in school as a young mother,
an exogenous increase in education of the individual may be associated with a postponement of fertility. We call this the Ôincarceration effectÕ; while women are in school,
they do not have the desire/time/opportunity to have a child.32
In addition, since more education increases human capital, this is also a mechanism
through which increases in education may lead to postponed fertility.33 Additional
education increases the opportunity cost of having a teen birth, since the wage rate is
higher. While this leads to both income and substitution effects, the consensus in the
female labour supply literature is that substitution effects are more important so more
education should reduce teen pregnancy; see Blundell and MaCurdy (1999) for a
review of the labour supply literature. We call the fact that the additional schooling may
make you ÔsmarterÕ and hence decide to postpone childbearing the Ôcurrent human
capital effectÕ; we call the fact that expectations about the future acquisition of human
capital are changed by compulsory schooling laws and this may change fertility decisions the Ôfuture human capital effectÕ.
If the effects of the compulsory schooling laws occur solely due to the ÔincarcerationÕ
effect, then the laws should have no impact on behaviour at ages above which the laws
induce schooling. To examine this, we estimate probit models of the probability of
having a first birth at age x, conditional on having no birth prior to that. We estimate
this model for x equal to 16, 17, 18, 19 and 20. If the laws impact the probability of first
birth at ages above which they bind, then this is strong evidence that the ÔincarcerationÕ
effect is not the only effect.34
If compulsory schooling laws have spillover effects (that is, they affect education at
levels above which they bind), identification of the underlying mechanisms becomes
more difficult. There is some evidence of this for the US (Lang and Kropp, 1986). In
contrast, Black et al. (2005) find no evidence of such spillovers as a result of the
Norwegian reform. While education spillovers may make the interpretation of our US
results more difficult, in practice they are relatively small. Thus, the ÔincarcerationÕ
effect implies that the effect of compulsory schooling laws on childbearing should be
31
It is important to note that this Ôrational choiceÕ approach assumes women make optimal decisions on
timing of births taking into account all the costs and benefits involved. This is often discussed in conjunction
with an alternative approach that sees many teenage pregnancies as ÔmistakesÕ resulting from thoughtless
behaviour, lack of knowledge about the long-run consequences, or lack of knowledge about birth control. It is
this view that fertility behaviour may not be optimal that underscores much of the policy interest in this topic.
Note that, particularly in the early sample period for the US, a birth in the late teens was often within-wedlock
and may not have been considered to be a Ôbad thingÕ.
32
Jacob and Lefgren (2003) discuss the incarceration effect in the context of education and its effect on
criminal behaviour.
33
Happel et al. (1984) model the timing of children and argue that, if capital markets are perfect, the
timing of first child depends on the rate at which earnings depreciate due to absence from the labour market,
and the initial level of earnings at the start of the woman’s life cycle. If women start with very low earning
power, and skills depreciate with absence from the market, then it is optimal to have children early. On the
other hand, if initial earnings are high, postponing childbirth is optimal. Thus, in this framework, women
with more human capital are more likely to postpone childbirth.
34
Another way to put this is that if the ÔincarcerationÕ effect is the only mechanism, fertility effects at older
ages can only be interpreted as a rejection of the exogeneity of the compulsory schooling laws.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1045
Table 9
Effect of Compulsory Schooling Laws on the Probability of Birth Conditional on Not
Already Having a Child
Dependent Variable
US
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
Log likelihood
N
Norway – full sample
Reform
Log likelihood
N
Norway – urban sample
Reform
Log likelihood
N
Birth at
16/No
prior birth
Birth at
17/No
prior birth
Birth at
18/No
prior birth
Birth at
19/No
prior birth
Birth at
20/No
prior birth
0.0001
(0.0006)
0.0009
(0.0008)
0.0002
(0.0010)
0.0271*
(0.0020)
130,642
1,572,513
0.0025*
(0.0009)
0.0045*
(0.0012)
0.0015
(0.0049)
0.0349*
(0.0029)
220,385
1,545,369
0.0035*
(0.0013)
0.0057*
(0.0013)
0.0005
(0.0078)
0.0344*
(0.0034)
300,485
1,493,288
0.0021
(0.0019)
0.0047*
(0.0018)
0.0007
(0.0054)
0.0292*
(0.0033)
362,007
1,414,844
0.0024
(0.0036)
0.0056
(0.0040)
0.0061
(0.0050)
0.0182*
(0.0033)
378,221
1,311,693
0.0006
(0.0006)
10,378
236,747
0.0014
(0.0012)
32,289
256,869
0.0029
(0.0017)
54,056
251,249
0.0022
(0.0025)
66,474
236,876
0.0032
(0.0025)
69,513
217,128
0.0011
(0.0010)
3,304
87,058
0.0045*
(0.0020)
9,375
87,976
0.0045*
(0.0022)
15,598
85,113
0.0132*
(0.0046)
19,296
81,201
0.0088*
(0.0045)
20,702
75,848
Estimates are marginal effects from ordered probit estimation. Each column denotes a separate regression.
The sample includes women between 20 and 30 years of age. Also included in the specifications are year-ofbirth indicators. The US specifications also include state dummies; the Norway specifications include
municipality indicators. Standard errors are adjusted for clustering at the state/municipality level. The
number of observations reported is the number actually used in the Norwegian estimation after observations
with perfectly predicted outcomes are eliminated.
*Denotes statistically significant at the 5% level.
much larger at ages where the law binds than in subsequent years.35 One further caveat
is that compulsory schooling laws have an impact on potential fathers and this may be
an independent force leading to a reduction in teenage births. We are unable to study
this possibility with our data.36
Table 9 presents the probit estimates of the probability of a birth at a particular age
conditional on no prior birth.37 Given that women are pregnant for about 9 months,
the ÔincarcerationÕ model implies that the Dropout Age ¼ 16 should impact births at
age 16 and 17, but should have little impact on births at higher ages.38 However we
find that Dropout Age ¼ 16 has a small and statistically insignificant effect on the
35
A second issue is that conditioning on individuals who have no prior birth creates a selected sample. We
have verified that we get almost identical results if we include all individuals in the sample for this analysis.
36
There is some evidence that compulsory schooling laws delayed age of first marriage in the US
(Devereux and Tripathi, 2006), which suggests that some of the reduction in teen childbearing may result
from delayed marriage.
37
This hazard-type specification complements the earlier CDF-style approach by focusing more directly on
when exactly women have their first births and how the timing is influenced by compulsory schooling laws.
38
If people do actually drop out of school on their 16th birthday, this compulsory schooling law should
only impact births at age 16 through the ÔincarcerationÕ effect.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1046
THE ECONOMIC JOURNAL
[JULY
probability of first birth at age 16, but has a statistically significant negative effect on
births at ages 17 and 18. Likewise, although Dropout Age ¼ 17 does have a negative
effect at age 17, it has, if anything, larger negative effects at ages 18 and 19.
In the Norwegian data, the reform raised the minimum school leaving age from 14 to
16 for most people. Despite this, there is a negative effect of the reform on the
probability of giving birth at age 18 (although this is statistically insignificant), which is
too old for the ÔincarcerationÕ effect to be relevant. Earlier, in Table 3, we found that
the reform had a much bigger impact on Norwegians in urban areas. Therefore, we do
a separate investigation of the mechanisms for this urban sample (also in Table 9). We
find large statistically significant negative effects of the reform on the probability of
giving birth at ages 17, 18, 19, and 20. The latter two marginal effects are particularly
large, which is the opposite of what the ÔincarcerationÕ effect would predict.
Thus, the evidence for the ÔincarcerationÕ effect of compulsory schooling laws is very
weak in this probit analysis and suggests that the human capital effects are likely playing
a role. We can be certain that whether or not there is an ÔincarcerationÕ effect, there are
also other mechanisms that influence fertility behaviour.39 Unfortunately, the nature of
our data prohibits us from distinguishing much beyond this point.
7. Conclusions
Many studies find that early fertility adversely affects women’s economic outcomes such
as the level of completed schooling, labour market participation, and wages. However,
there is limited information about policy relevant factors that might be important
determinants of early fertility decisions. This article attempts to increase our knowledge
by studying the role of compulsory schooling laws.
We find that minimum school requirements have a significantly negative effect on
the probability of having a child as a teenager both in the US and in Norway. Our
results are robust to a number of specification checks. It is noteworthy that our
estimates are fairly similar in two countries – the US and Norway – that are so
different institutionally. These findings suggest that policy interventions to increase
female education at the lower tail of the educational distribution may be an effective
means of reducing rates of teenage childbearing, regardless of the welfare structure
in place.
In addition to studying the effects of compulsory schooling laws on teenage fertility
choice, we also examine different mechanisms through which the compulsory
schooling legislation may be affecting fertility behaviour. The first mechanism we
consider is an ÔincarcerationÕ effect or the fact that educational attendance reduces
time available to engage in risky behaviour. Alternative mechanisms are related to
human capital theory where both current and expected human capital may impact
39
In Appendix Table A4, we present the equivalent estimates for the US where each cohort is weighted
equally. Once again, there is evidence against a pure incarceration effect as Dropout Age ¼ 17 affects fertility
behaviour at 19 and 20, and Dropout Age ¼ 18 affects behaviour at age 20. There is also a shred of evidence
for the Ôfuture human capital effectÕ in that Dropout Age ¼ 18 has a statistically significant negative effect on
the probability of a birth at age 17. That is, women who know that they will have to stay in school until age 18
are less likely to have a child at age 17 than other women with the same amount of schooling who do not face
this future compulsory schooling.
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1047
teenage fertility choice. Our results suggest that the effect of compulsory schooling laws
goes beyond a pure ÔincarcerationÕ effect.
UCLA, IZA and NBER
University College Dublin, CEPR and IZA
Norwegian School of Economics, Center for the Economics of Education, LSE and IZA
Submitted: 17 March 2005
Accepted: 29 March 2007
Appendix
60
Reformed_municip
50
40
30
20
10
0
1959 1960 1961 1962 1963 1964 1965 1966 1967 1968 1969 1970 1971 1972 1973
Reform implementation, year/municipalities
Fig. A1. The Number of Municipalities Implementing the Education Reform, by Year, Norway
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1048
THE ECONOMIC JOURNAL
40
Poor_municip
[JULY
Rich_municip
30
20
10
0
1959 1960 1961 1962 1963 1964 1965 1966 1967 1968 1969 1970 1971 1972 1973
Reform implementation, by average family income
Fig. A2. Reform Implementation Poor vs. Rich Municipalities Based on Average Family Income,
Norway
40
Loweduc_municip
Higheduc_municip
30
20
10
0
1959 1960 1961 1962 1963 1964 1965 1966 1967 1968 1969 1970 1971 1972 1973
Reform implementation, by average level of education
Fig. A3. Reform Implementation in High vs. Low Education Municipalities Based on Average Years
Father’s of Education in the Municipality, Norway
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
Small_municip
40
1049
Large_municip
30
20
10
0
1959 1960 1961 1962 1963 1964 1965 1966 1967 1968 1969 1970 1971 1972 1973
Reform implementation, by size
Fig. A4. Reform Implementation in Small vs. Large Municipalities, Norway
60
teenmothers_low
teenmothers_high
50
40
30
20
10
0
1961
1962 1963 1964 1965 1966 1967 1968 1969 1970
Reform implementation, high/low teenmother municipalities
1971
Fig. A5. Reform Implementation in Municipalities with High vs. Low Rates of Teenage Fertility,
Norway
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1050
[JULY
THE ECONOMIC JOURNAL
Table A1
Minimum Dropout Ages for the US by State
Alabama
Arizona
Arkansas
California
Colorado
Connecticut
Delaware
District of Columbia
Florida
Georgia
Idaho
Illinois
Indiana
Iowa
Kansas
Kentucky
Louisiana
Maine
Maryland
Massachusetts
Michigan
Minnesota
Mississippi
Missouri
Montana
Nebraska
Nevada
New Hampshire
New Jersey
New Mexico
New York
North Carolina
North Dakota
Ohio
Oklahoma
Oregon
Pennsylvania
Rhode Island
South Carolina
South Dakota
Tennessee
Texas
Utah
Vermont
Virginia
Washington
West Virginia
Wisconsin
Wyoming
Dropout
Age: 1924
Dropout
Age: 1934
Dropout
Age: 1944
Dropout
Age: 1954
Dropout
Age: 1964
Dropout
Age: 1974
16
16
15
16
16
16
16
14
16
14
18
16
16
16
16
16
14
17
16
16
16
16
14
16
16
16
18
16
16
16
16
14
17
18
18
16
16
16
14
17
16
14
18
16
14
16
16
16
16
16
16
16
16
16
16
16
16
16
14
18
16
16
16
16
16
14
17
16
16
16
16
17
16
16
16
18
16
16
16
16
14
17
18
18
18
16
16
14
17
16
14
18
16
15
16
16
16
17
16
16
16
16
16
16
16
16
16
14
16
16
16
16
16
16
14
14
16
16
16
16
16
14
16
16
18
16
16
16
16
14
17
8
18
16
18
16
16
17
16
16
18
16
15
16
16
16
17
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
18
16
16
17
16
16
17
18
18
18
17
16
16
17
16
16
18
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
0
16
16
16
17
16
16
17
16
16
16
18
18
18
17
16
0
16
16
16
18
16
16
16
16
16
17
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
16
0
16
16
16
17
16
16
17
16
16
16
18
18
18
17
16
16
16
17
17
18
16
17
16
16
18
17
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
2008 ]
COMPULSORY SCHOOLING LAWS AND TEENAGE BIRTHS
1051
Table A2
Effect of Compulsory Schooling Laws on Educational Attainment
Dependent Variable:
Norway: Education
Clustering at
Municipality Level
(1)
0.1218
(0.0217)
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
N ¼ 260,641
US: Education
Clustering at
State Level
US: Education
Clustering at
State-Year Level
(2)
0.4041
(0.2520)
0.4709
(0.2865)
0.4245
(0.3045)
0.7298*
(0.0715)
N ¼ 1,270,753
(3)
0.4041*
(0.0590)
0.4709*
(0.0696)
0.4245*
(0.0959)
0.7298*
(0.0228)
N ¼ 1,270,753
Each column denotes a separate regression. The sample includes women between 22 and 30 years of age. Also
included in the specifications are year-of-birth indicators. The US specifications also include state dummies;
the Norway specifications include municipality indicators. Standard errors are adjusted for clustering at the
state/municipality level in columns (1) and (2). Standard errors are adjusted for clustering at the state-year
level in column (3).
*denotes statistically significant at the 5% level.
Table A3
Timing of the Implementation of the Reform in Norway
Dependent Variable: Year of Reform
County 2
County 3
County 4
County 5
County 6
County 7
County 8
County 9
County 10
County 11
County 12
County 13
County 14
County 15
County 16
County 17
County 18
County 19
Share of Fathers with Some College
Share of Mothers with Some College
Father’s Income (mean)
Mother’s Income (mean)
Father’s Age (mean)
Mother’s Age (mean)
Size of Municipality/100
Unemployment Rate 1960
Share Workers in Manufacturing 1960
Share Workers in Private Services 1960
Coefficient
Standard error
1.89
4.77
0.41
0.05
0.50
1.10
1.82
1.04
1.21
0.01
1.09
0.05
1.52
1.41
0.16
0.93
0.12
2.72
1.40
13.16
0.006
0.01
0.08
0.15
0.00
8.32
1.99
4.11
0.65
5.23
0.70
0.67
0.62
0.63
0.64
0.64
0.71
0.63
0.60
0.70
0.59
0.58
0.60
0.57
0.65
0.71
4.00
8.58
0.004
0.01
0.15
0.18
0.00
12.15
3.45
6.75
Ó The Author(s). Journal compilation Ó Royal Economic Society 2008
1052
[JULY
THE ECONOMIC JOURNAL
Table A3
(Continued)
Coefficient
Standard error
2.75
0.014
1971.14
2.15
0.022
7.11
Share Labour Vote 1961
Teenage fertility
Constant term
Robust standard errors. All variables are municipality level variables.
Table A4
Effect of Compulsory Schooling Laws on the Probability of Birth Conditional
on Not Already Having a Child, Equal Weighting of Cohorts, US Data
Dependent
Variable
Dropout age ¼ 16
Dropout age ¼ 17
Dropout age ¼ 18
White
N
Log likelihood
Birth at
16/No
prior birth
Birth at
17/No
prior birth
Birth at
18/No
prior birth
Birth at
19/No
prior birth
Birth at
20/No
prior birth
0.0000
(0.0007)
0.0013
(0.0010)
0.0011
(0.0013)
0.0218*
(0.0017)
1,572,513
4.113e þ 08
0.0008
(0.0015)
0.0033
(0.0019)
0.0093*
(0.0031)
0.0260*
(0.0027)
1,545,369
6.995e þ 08
0.0014
(0.0015)
0.0056*
(0.0022)
0.0109
(0.0055)
0.0226*
(0.0036)
1,493,288
9.789e þ 08
0.0030
(0.0021)
0.0091*
(0.0038)
0.0120
(0.0081)
0.0100*
(0.0031)
1,414,844
1.206e þ 09
0.0034
(0.0025)
0.0083*
(0.0030)
0.0106*
(0.0039)
0.0040
(0.0035)
1,311,693
1.299e þ 09
Estimates are marginal effects from ordered probit estimation. Each column denotes a separate regression.
The sample includes women between 20 and 30 years of age. Also included in the specifications are yearof-birth indicators and state dummies. Standard errors are adjusted for clustering at the state level.
*Denotes statistically significant at the 5% level.
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