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Abstract

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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 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 ‘incarceration effect’; 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 ‘human capital effect’; 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 ‘incarceration’ 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. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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 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.3Figure 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.

image

Figure 1. Teenage Birth Rates Per 100 15–19 Year Olds

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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 largely under state and local control (Baicker, 2005). Targeted primarily at the children (and not the parents), eligibility was often limited by ‘suitable home’ 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 (Rønsen and Strøm, 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 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

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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
     maximum age by which a child must be enrolled,
  • 2
     minimum age at which a child may drop out,
  • 3
     minimum years of schooling before dropping out,
  • 4
     minimum age for a work permit, and
  • 5
     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.9Appendix 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.

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).12Appendix Figure A1 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

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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:

  • image(1)

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 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:

  • image(2)

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

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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 + 16). Thus, we restrict our Census sample to women aged between 20 and 30.

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 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.

Table 1. Descriptive Statistics
VariableMeanStd. Dev.MinMax
US
Birth cohort1948.1412.3419101960
Age at census24.803.162030
Education12.302.52017
White0.860.3401
Child before 170.020.1501
Child before 180.060.2301
Child before 190.110.3101
Child as teenager0.170.3801
Child before 210.240.4301
Dropout age is  <160.040.1901
Dropout age is 160.750.4301
Dropout age is 170.120.3201
Dropout age is 180.090.2801
Enrolment age is 60.140.3501
Enrolment age is 70.660.4701
Enrolment age is 8+0.200.4001
N = 1,584,094    
Norway
Birth Cohort19533.3519471958
Age in 200047.013.354253
Education11.502.58521
Child before 170.010.0901
Child before 180.040.1901
Child before 190.090.2901
Child as teenager0.170.3801
Child before 210.250.4301
Reform implemented0.520.5001
N = 260,641    

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 = 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 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

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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.

image

Figure 2. Effect of Compulsory Schooling Law on Teenage Pregnancy, US

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image

Figure 3. Effect of Compulsory Schooling Law on Teenage Pregnancy, Norway

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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 = 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% ((0.008×100)/0.17). The effect of imposing a law mandating women to stay in school until 17 is to reduce the probability of a teen birth by 8.8% ((0.015×100)/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.

Table 2. Effect of Compulsory Schooling Laws on the Probability of First Birth by A Certain Age: Probit Marginal Effects
Dependent Variable:Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

  2. *denotes statistically significant at the 5% level.

US
Dropout age = 16−0.00002−0.0025−0.0058*−0.0077*−0.0095*
(0.0009)(0.0017)(0.0018)(0.0024)(0.0047)
Dropout age = 17−0.0008−0.0053*−0.0106*−0.0147*−0.0186*
(0.0011)(0.0022)(0.0027)(0.0031)(0.0050)
Dropout age = 180.0012−0.0004−0.0004−0.0023−0.0085
(0.0014)(0.0060)(0.0128)(0.0147)(0.0153)
White−0.0421*−0.0749*−0.1035*−0.1222*−0.1275*
(0.0029)(0.0053)(0.0077)(0.0094)(0.0106)
Log likelihood−171,562−330,737−516,080−700,314−847,981
N = 1,584,094     
Norway
Reform−0.0006−0.0020−0.0047*−0.0063−0.0087*
(0.0006)(0.0015)(0.0024)(0.0037)(0.0043)
Log likelihood−11,456−39,160−77,676−114,677−143,187
N = 260,641     

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% ((0.006×100)/0.17). This is similar but somewhat smaller than the 4.7% effect of Dropout Age = 16 in the United States. Generally, the effects of the reform in Norway are very similar to those of Dropout Age = 16 in the United States.24

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

Table 3. Effect of Compulsory Schooling Laws on the Probability of Birth: Urban/Rural Distinction
 Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

  2. 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.

  3. *Denotes statistically significant at the 5% level.

US
Urban
N = 1,063,181     
Dropout age = 160.0007−0.0016−0.0019−0.0031−0.0030
(0.0009)(0.0017)(0.0030)(0.0055)(0.0089)
Dropout age = 17−0.0003−0.0057*−0.0100*−0.0146*−0.0163
(0.0012)(0.0018)(0.0029)(0.0052)(0.0087)
Dropout age = 180.00280.00250.00680.0012−0.0033
(0.0024)(0.0084)(0.0173)(0.0071)(0.0182)
White−0.0448*−0.0818*−0.1166*−0.1425*−0.1556*
(0.0034)(0.0064)(0.0093)(0.0114)(0.0127)
Log Likelihood−105,405−201,625−315,431−431,521−529,597
Rural
N = 520,913     
Dropout age = 160.0008−0.0002−0.0039−0.0029−0.0031
(0.0016)(0.0033)(0.0034)(0.0037)(0.0064)
Dropout age = 17−0.0007−0.0033−0.0066−0.0003−0.0097
(0.0020)(0.0038)(0.0047)(0.0053)(0.0084)
Dropout age = 180.0007−0.0004−0.00200.00890.0061
(0.0032)(0.0040)(0.0053)(0.0095)(0.0115)
White−0.0376−0.0643−0.0830−0.0924−0.0862
(0.0017)(0.0028)(0.0041)(0.0051)(0.0054)
Log likelihood−65,576−127,696−197,982−264,364−312,116
Norway
Urban
N = 87,752     
Reform−0.0010−0.0053*−0.0094*−0.0212*−0.0275*
(0.0010)(0.0026)(0.0038)(0.0067)(0.0089)
Log likelihood−3,643−11,606−22,833−34,015−43,349
Rural N = 172,889     
Reform−0.0035−0.0005−0.00270.00080.0003
(0.0008)(0.0016)(0.0028)(0.0035)(0.0041)
Log likelihood−7,805−27,543−54,822−80,626−99,803

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 include these trends (Table 4), we get estimates that are quite similar to those in Table 2.28

Table 4. Effect of Compulsory Schooling Laws on the Probability of Birth Including State-Year Trends
Dependent Variable:Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

  2. *Denotes statistically significant at the 5% level.

US
Dropout age = 160.0016*−0.0003−0.0036−0.0086*−0.0151*
(0.0006)(0.0016)(0.0031)(0.0040)(0.0060)
Dropout age = 170.0008−0.0032−0.0072−0.0131*−0.0233*
(0.0011)(0.0019)(0.0037)(0.0046)(0.0072)
Dropout age = 180.0042*0.00200.0003−0.0087−0.0175
(0.0018)(0.0079)(0.0037)(0.0177)(0.0187)
White−0.0417*−0.0744*−0.1031*−0.1219*−0.1274*
(0.0028)(0.0052)(0.0076)(0.0093)(0.0106)
Log likelihood−171,467−330,582−515,919−700,142−847,826
N = 1,584,094     
Norway
Reform−0.0002−0.0015−0.0046*−0.0049−0.0063
(0.0002)(0.0015)(0.0021)(0.0028)(0.0034)
Log likelihood−11,175−38,830−77,265−114,222−142,695
N = 260,641     
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 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.

Table 5. Effect of Compulsory Schooling Laws on the Probability of Birth: Equal Weighting of Cohorts: Probit Marginal Effects, US
Dependent Variable:Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

Dropout age = 160.0001−0.0008−0.0023−0.0051−0.0079*
(0.0009)(0.0023)(0.0033)(0.0039)(0.0039)
Dropout age = 17−0.0017−0.0051−0.0104*−0.0185*−0.0248*
(0.0012)(0.0025)(0.0038)(0.0060)(0.0052)
Dropout age = 18−0.0004−0.0099*−0.0202*−0.0294−0.0365*
(0.0012)(0.0039)(0.0088)(0.0149)(0.0115)
White−0.0354*−0.0606*−0.0803*−0.0853*−0.0765*
(0.0023)(0.0046)(0.0072)(0.0088)(0.0103)
Log likelihood−5.487e + 08−1.053e + 09−1.661e + 09−2.279e + 09−2.785e + 09
N = 1,584,094     
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, suggesting that the change in fertility we observe is in fact caused by the change in compulsory schooling laws.

Table 6. Effect of Compulsory Schooling Laws on the Probability of Birth Including Future Legislation: Probit Marginal Effects, US
Dependent Variable:Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

Dropout age = 160.0006−0.0024−0.0051*−0.0087*−0.0113*
(0.0008)(0.0018)(0.0020)(0.0025)(0.0051)
Dropout age = 17−0.0002−0.0050*−0.0101*−0.0175*−0.0236*
(0.0008)(0.0016)(0.0019)(0.0027)(0.0051)
Dropout age = 180.0012−0.0076*−0.0174*−0.0215−0.0315*
(0.0015)(0.0032)(0.0073)(0.0148)(0.0133)
FutureLaws
Dropout age = 16−0.00020.00270.00470.0105*0.0127*
(0.0007)(0.0020)(0.0022)(0.0039)(0.0060)
Dropout age = 17−0.00100.0008−0.00100.00130.0042
(0.0014)(0.0028)(0.0030)(0.0050)(0.0072)
Dropout age = 18−0.0041*0.0006−0.00040.00520.0073
(0.0015)(0.0030)(0.0035)(0.0054)(0.0072)
White−0.0403*−0.0728*−0.1013*−0.1170*−0.1181*
(0.0030)(0.0057)(0.0085)(0.0102)(0.0113)
Log likelihood−107,232−209,129−332,203−458,272−557,592
N = 1,001,121     
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.

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:Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

9 Years of Schooling−0.0006−0.0044*−0.0085*−0.0122*−0.0140*
(0.0010)(0.0016)(0.0019)(0.0025)(0.0032)
10 Years of Schooling−0.0006−0.0047*−0.0089*−0.0114*−0.0167*
(0.0011)(0.0023)(0.0035)(0.0047)(0.0046)
11+ Years of Schooling−0.0020−0.0054−0.0073−0.0148−0.0174
(0.0024)(0.0054)(0.0103)(0.0123)(0.0137)
White−0.0421*−0.0748*−0.1034*−0.1222*−0.1275*
(0.0029)(0.0053)(0.0077)(0.0094)(0.0106)
Log Likelihood−171,563−330,734−516,075−700,307−847,972
N = 1,584,094     

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 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

Table 8. Effect of Child Labour Laws on the Probability of Birth, US Data
Dependent Variable:Birth by Age 16Birth by Age 17Birth by Age 18Birth by Age 19Birth by Age 20
  1. 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.

  2. *Denotes statistically significant at the 5% level.

Dropout age = 15−0.0006−0.0043*−0.0100*−0.0137*−0.0097
(0.0007)(0.0010)(0.0012)(0.0021)(0.0062)
Dropout age >15−0.0003−0.0013−0.00180.0000−0.0006
(0.0012)(0.0023)(0.0037)(0.0050)(0.0057)
White−0.0421*−0.0749*−0.0103−0.1222*−0.1276*
(0.0029)(0.0053)(0.0077)(0.0094)(0.0107)
Log Likelihood−171,564−330,742−516,089−700,324−848,001
N = 1,584,094     
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 also-persistent 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 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?

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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 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 ‘incarceration effect’; 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 ‘smarter’ and hence decide to postpone childbearing the ‘current human capital effect’; 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 ‘future human capital effect’.

If the effects of the compulsory schooling laws occur solely due to the ‘incarceration’ 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 ‘incarceration’ 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 ‘incarceration’ effect implies that the effect of compulsory schooling laws on childbearing should be 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 ‘incarceration’ model implies that the Dropout Age = 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 = 16 has a small and statistically insignificant effect on the 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 = 17 does have a negative effect at age 17, it has, if anything, larger negative effects at ages 18 and 19.

Table 9. Effect of Compulsory Schooling Laws on the Probability of Birth Conditional on Not Already Having a Child
Dependent VariableBirth at 16/No prior birthBirth at 17/No prior birthBirth at 18/No prior birthBirth at 19/No prior birthBirth at 20/No prior birth
  1. 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-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. The number of observations reported is the number actually used in the Norwegian estimation after observations with perfectly predicted outcomes are eliminated.

  2. *Denotes statistically significant at the 5% level.

US
Dropout age = 16−0.0001−0.0025*−0.0035*−0.0021−0.0024
(0.0006)(0.0009)(0.0013)(0.0019)(0.0036)
Dropout age = 17−0.0009−0.0045*−0.0057*−0.0047*−0.0056
(0.0008)(0.0012)(0.0013)(0.0018)(0.0040)
Dropout age = 180.0002−0.00150.0005−0.0007−0.0061
(0.0010)(0.0049)(0.0078)(0.0054)(0.0050)
White−0.0271*−0.0349*−0.0344*−0.0292*−0.0182*
(0.0020)(0.0029)(0.0034)(0.0033)(0.0033)
Log likelihood−130,642−220,385−300,485−362,007−378,221
N1,572,5131,545,3691,493,2881,414,8441,311,693
Norway – full sample
Reform−0.0006−0.0014−0.0029−0.0022−0.0032
(0.0006)(0.0012)(0.0017)(0.0025)(0.0025)
Log likelihood−10,378−32,289−54,056−66,474−69,513
N236,747256,869251,249236,876217,128
Norway – urban sample
Reform−0.0011−0.0045*−0.0045*−0.0132*−0.0088*
(0.0010)(0.0020)(0.0022)(0.0046)(0.0045)
Log likelihood−3,304−9,375−15,598−19,296−20,702
N87,05887,97685,11381,20175,848

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 ‘incarceration’ 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 ‘incarceration’ effect would predict.

Thus, the evidence for the ‘incarceration’ 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 ‘incarceration’ 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

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix

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 ‘incarceration’ 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 teenage fertility choice. Our results suggest that the effect of compulsory schooling laws goes beyond a pure ‘incarceration’ effect.

Footnotes
  • 1
  • 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).

  • 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%.

  • 4

     This system was introduced in 1964 and became a part of the social security system in 1971.

  • 5

     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).

  • 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.

  • 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).

  • 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.

  • 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.

  • 17

     See Møen et al. (2003) for a description of the data set.

  • 18

     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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 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.

  • 31

     It is important to note that this ‘rational choice’ 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 ‘mistakes’ 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 ‘bad thing’.

  • 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 ‘incarceration’ 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.

  • 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 ‘incarceration’ effect.

  • 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 = 17 affects fertility behaviour at 19 and 20, and Dropout Age  = 18 affects behaviour at age 20. There is also a shred of evidence for the ‘future human capital effect’ in that Dropout Age = 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.

References

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix
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Appendix

  1. Top of page
  2. Abstract
  3. 1. Background Information
  4. 2. The Compulsory Schooling Laws
  5. 3. Empirical Methodology: Probability of Having First Birth as a Teenager
  6. 4. Data
  7. 5. Results for the Probit Models
  8. 6. Why Do Compulsory Schooling Laws affect Timing of Births?
  9. 7. Conclusions
  10. References
  11. Appendix
  • image(A1)

[  The Number of Municipalities Implementing the Education Reform, by Year, Norway ]

  • image(A2)

[  Reform Implementation Poor vs. Rich Municipalities Based on Average Family Income, Norway ]

  • image(A3)

[  Reform Implementation in High vs. Low Education Municipalities Based on Average Years Father's of Education in the Municipality, Norway ]

  • image(A4)

[  Reform Implementation in Small vs. Large Municipalities, Norway ]

  • image(A5)

[  Reform Implementation in Municipalities with High vs. Low Rates of Teenage Fertility, Norway ]

Table A1. Minimum Dropout Ages for the US by State
 Dropout Age: 1924Dropout Age: 1934Dropout Age: 1944Dropout Age: 1954Dropout Age: 1964Dropout Age: 1974
Alabama161616161616
Arizona161616161616
Arkansas151616161616
California161616161616
Colorado161616161616
Connecticut161616161616
Delaware161616161616
District of Columbia141616161616
Florida161616161616
Georgia141414161616
Idaho181816161616
Illinois161616161616
Indiana161616161616
Iowa161616161616
Kansas161616161616
Kentucky161616161616
Louisiana141414161616
Maine171714161616
Maryland161616161616
Massachusetts161616161616
Michigan161616161616
Minnesota161616161616
Mississippi1417161600
Missouri161614161616
Montana161616161616
Nebraska161616161616
Nevada181818181717
New Hampshire161616161616
New Jersey161616161616
New Mexico161616171717
New York161616161616
North Carolina141414161616
North Dakota171717171616
Ohio18188181818
Oklahoma181818181818
Oregon161816181818
Pennsylvania161618171717
Rhode Island161616161616
South Carolina14141616016
South Dakota171717171616
Tennessee161616161617
Texas141416161617
Utah181818181818
Vermont161616161616
Virginia141515161617
Washington161616161616
West Virginia161616161616
Wisconsin161616161618
Wyoming161717161717
Table A2. Effect of Compulsory Schooling Laws on Educational Attainment
Dependent Variable:Norway: Education Clustering at Municipality LevelUS: Education Clustering at State LevelUS: Education Clustering at State-Year Level
  1. 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).

  2. *denotes statistically significant at the 5% level.

 (1)(2)(3)
Dropout age = 160.12180.40410.4041*
(0.0217)(0.2520)(0.0590)
Dropout age = 17 0.47090.4709*
 (0.2865)(0.0696)
Dropout age = 18 0.42450.4245*
 (0.3045)(0.0959)
White 0.7298*0.7298*
 (0.0715)(0.0228)
N = 260,641N = 1,270,753N = 1,270,753
Table A3. Timing of the Implementation of the Reform in Norway
 CoefficientStandard error
  1. Robust standard errors. All variables are municipality level variables.

Dependent Variable: Year of Reform
County 2−1.890.65
County 34.775.23
County 4−0.410.70
County 50.050.67
County 6−0.500.62
County 7−1.100.63
County 8−1.820.64
County 9−1.040.64
County 10−1.210.71
County 110.010.63
County 12−1.090.60
County 13−0.050.70
County 141.520.59
County 15−1.410.58
County 160.160.60
County 17−0.930.57
County 180.120.65
County 19−2.720.71
Share of Fathers with Some College1.404.00
Share of Mothers with Some College13.168.58
Father's Income (mean)−0.0060.004
Mother's Income (mean)−0.010.01
Father's Age (mean)0.080.15
Mother's Age (mean)−0.150.18
Size of Municipality/100−0.000.00
Unemployment Rate 1960−8.3212.15
Share Workers in Manufacturing 19601.993.45
Share Workers in Private Services 19604.116.75
Share Labour Vote 19612.752.15
Teenage fertility0.0140.022
Constant term1971.147.11
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 VariableBirth at 16/No prior birthBirth at 17/No prior birthBirth at 18/No prior birthBirth at 19/No prior birthBirth at 20/No prior birth
  1. 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-of-birth indicators and state dummies. Standard errors are adjusted for clustering at the state level.

  2. *Denotes statistically significant at the 5% level.

Dropout age = 160.0000−0.0008−0.0014−0.0030−0.0034
(0.0007)(0.0015)(0.0015)(0.0021)(0.0025)
Dropout age = 17−0.0013−0.0033−0.0056*−0.0091*−0.0083*
(0.0010)(0.0019)(0.0022)(0.0038)(0.0030)
Dropout age = 180.0011−0.0093*−0.0109−0.0120−0.0106*
(0.0013)(0.0031)(0.0055)(0.0081)(0.0039)
White−0.0218*−0.0260*−0.0226*−0.0100*0.0040
(0.0017)(0.0027)(0.0036)(0.0031)(0.0035)
N1,572,5131,545,3691,493,2881,414,8441,311,693
Log likelihood−4.113e + 08−6.995e + 08−9.789e + 08−1.206e + 09−1.299e + 09