This study has been supported by a grant for the study of Law and Economics from the National Science Foundation to the National Bureau of Economic Research. The authors wish to thank Gary S. Becker for helpful comments, Ann Bartel for her fine research assistance and insights, Elisabeth Parshley for her assistance, and H. Irving Forman for charting the graphs. We have also benefitted from comments by members of the Labor Workshop at Columbia University and the Industrial Organization Workshop at the University of Chicago. This is not an official National Bureau publication as the findings reported herein have not undergone the full critical review accorded the National Bureau's studies, including approval by the Board of Directors.

¹ Two studies that have briefly attempted to measure the effects of compulsory schooling laws are Stigler, G., Employment and Compensation in Education (National Bureau of Economic Research, 1950)Google Scholar, Appendix B, and U.S. Bureau of the Census, Education of the American Population, by Folger, J. and Nam, C. (Washington, D.C.: U.S. Government Printing Office, 1967), pp. 24–27.Google Scholar Stigler analyzed enrollment rates in 1940 and concluded (p. 70) “that the influence of legislation is a relatively weak factor, whose presumptive significance comes largely from the correlation of maximum age in the statute with incomes and racial composition.” Folger's and Nam's analysis of enrollment rates for selected states from 1890 to 1914 supported Stigler's conclusion.

² For a detailed account of the Massachusetts Law, see Ensign, Forest, Compulsory School Attendance and Child Labor (Iowa City: Athens Press, 1921).Google Scholar

³ See Ogburn, W. F., Progress and Uniformity in Child Labor Legislation (1912) and Ensign for the history and provisions of these laws.Google Scholar

⁴ Note also that it is nearly impossible to determine the dates of various child labor laws within a state. (See Ogburn on this point.) This prevents a.time series analysis which relies on a comparison of periods before and after legislation.

⁵ The consumption aspects of schooling are neglected to simplify the presentation. Their inclusion would not alter the predictions on the effects of schooling laws.

⁶ This approach is discussed in greater detail in Becker, Gary, Human Capital and the Personal Distribution of Income (Ann Arbor: University of Michigan, 1967).Google Scholar

⁷ Several possible reasons for increasing costs of units of human capital are: (1) diminishing marginal productivity (due to the individual's limited mental and physical capacity) of resources used to produce human capital investments; (2) limitations on an individual's own time (an input into the investment function) and the resulting greater use of imperfect market substitutes as one's investing time becomes exhausted in a given period; and (3) the rising opportunity cost of time as one acquires more units of human capital. The latter could be offset if acquiring human capital raised the marginal product of one's time and other resources in producing more human capital. Note also that the finiteness of one's life will ultimately cause the marginal return per unit to decline.

⁸ We have already indicated that these laws usually require an individual to remain in- school until a specified age. There is no direct correspondence between this age and either units of human capital or dollar investments. For example, a person may be attending but doing no work and hence producing few or no units of human capital. The exposition of the effect of compulsory schooling laws, which makes use of Figure 1, is simplified by assuming that a person compelled to stay in school is producing units of human capital. However, this assumption is not crucial to our empirical analysis since we do not investigate the effect of school laws on earnings. The latter has been briefly analyzed by Chiswick, Barry in “Minimum Schooling Legislation and the Cross-Sectional Distribution of Income,” The Economic Journal, LXXIX (Sept., 1969), 495–507.CrossRefGoogle Scholar

⁹ For a more rigorous incorporation of these factors into analyzing the effects of legislation see Landes, William M., “The Effect of State Fair Employment Laws on the Economic Position of Nonwhites,” American Economic Review, LVII (May, 1967), 578–90.Google Scholar

¹⁰ If penalties were also imposed on the parents of the child or the child himself, the supply curve for child labor would shift upwards. This might more than offset the reduction in demand so that the wage for child labor would rise. However, the net wage which we define as the wage received minus the expected penalties imposed on parents or child, would fall. And it is the net wage that is relevant in determining the choice between employment and other activities.

¹¹ This assumes a negligible impact of the child labor law on the potential wage rates of persons above the legal minimum. Suppose, however, the law applied only to children under 14. We might expect an increase in the wages of children older than 14 as employers shift their demand to this group. This, in turn, would lower the demand curve in Figure 2 below DD for school investments beyond the legal minimum age, and reduce these investments.

¹² Note our algebraic specification assumes the school law shifts down the supply curve by a constant amount at all investment levels less than the legal minimum. A similar assumption applies to the child labor law.

¹³ It is instructive to derive equation (4) by first aggregating individuals within a given state and then aggregating across states.

(1) Within a State. For a state without school and child labor laws, the average value of

equals the average value of α_i among the i individuals (i = 1, …, n) in that state. When both schooling and child labor laws exist the average

which we denote by

is derived as follows:

where n_g = number of individuals who would invest less than the minimum required by the schooling law in the law's absence, nc = number who would invest less than the minimum required by the child labor law in the law's absence, k_g = (n_g/n) and k_cc = (n_c/n). Note that

and

The average effect, for example, of the schooling law would equal the product of the average effect among individuals subject to the law (i.e.,

) times the proportion of the school age population subject to the law (i.e., k_a). If a state had only a schooling law, the terms denoting the child labor law would drop out. Similarly, if only a child labor law existed, the terms denoting the schooling law would drop out.

(2) Across States. Let N = the number of states, N_g= number with school laws, and N_c = number with child labor laws. We have

and dividing by N yields

where

¹⁴ Our analysis for 1880 is limited to the 38 states that had achieved statehood by 1880 (see Table 1). Detailed data were available only for these states. Note that in 1880 more than 95 percent of the population in the United States lived in the 38 states.

¹⁵ E/P probably overstates the true proportion of 6–16 year olds who are enrolled since some persons under 6 and over 16 are included in the numerator and they are likely to exceed the number of persons 6–16 enrolled in schools other than elementary and secondary schools.

¹⁶ A level of statistical significance of at least .10 will be referred to as significant throughout the paper.

¹⁷ Note that states with laws are all outside the South.

¹⁸ Note also that the R² for A/E is much lower than for the other dependent variables. This occurs because (1) the independent variables tend to affect both attendance and enrollment in the same direction and (2) the variation in A/E among states is much smaller than for the other dependent variables.

¹⁹ These estimates were computed as follows. Since

we have

Regression coefficients of the school law variable on E/P (which equals.065 with a t-value of 1.38) and A/E are used as estimates of Δ(E/P) and Δ(A/E) respectively where Δ denotes the change in the variable. The regression equation for E/P (public school enrollment) is not presented in Table 3 because it is very similar to the equation for E'/P and the latter is a more comprehensive measure of enrollment. Values for E/P and A/E in (ii) should equal what they would be in the absence of a law. This is estimated by taking the 1880 mean values for E/P and A/E in states with school laws and deducting the regression coefficient on the law variable in that particular regression. The change in A/P associated, for example, with a change in enrollment holding constant A/E is equal to

and the percentage change is calculated accordingly.

²⁰ The mean enrollment rate in states with schooling laws in 1880 is equal to.975 and the predicted enrollment rate in these states had they not passed laws is equal to.975 minus.085, the regression coefficient on the school law variable. The percentage change is simply.085/(.975 —.085).

²¹ A 75 percent reduction no doubt exaggerates the relative impact of the school law in view of the extreme sensitivity of this estimate to the size of the enrollment rate and the likely overestimate of the latter (see fn .15). For example, a similar calculation derived from the regression on public school enrollment indicates a reduction in the proportion not enrolled from .16 to .09 or more than 40 percent.

²² The relative effects of school laws on attendance and non-attendance in public schools are shown in the table below:

²³ The table below illustrates the calculation of the relative effects of the school law on DA/E and DA/P for states with school laws.

²⁴ These estimates are derived from the following two equations:

Note that-the larger relative effect of days open on Δ(DA/E) than on Δ(DA/P) is accounted for by the earlier finding that the school law variable had a smaller effect on A/E than on A/P.

²⁵ The correlation coefficients across states in 1880 are as follows:

²⁶ Days attended may also be subject to sizable error in measuring investment in schooling. The mere fact that a person in one state is spending more days per year in school than a person in another state is not sufficient to determine if a difference in the accumulation of human capital is taking place. Hours of attendance per day and school quality (not taken account of by state expenditures on schooling) may differ among states in a way to eliminate differences in schooling based on days attended.

²⁷ Data on schooling by states are not available before 1870. Hence, we cannot compute regressions for a year in which no states had passed laws.

²⁸ Positive regression coefficients on the 1880 school law variable in the 1870 regression might still be consistent with this conclusion since two states had laws in 1870. Since this would require no effect of the 1880 school law variable in 1870 in the eleven states that passed laws between 1870 and 1880, the.regression coefficient on SL in 1870 would have to be approximately 2/13 as big as the coefficients in the 1880 equations. (This follows from the derivation of β₁ in footnote 13.)

²⁹ Non-significant regression coefficients on SL in 1870 would not provide conclusive proof because other factors (not held constant in the regression analysis) may have caused both the passage of compulsory school legislation and higher levels of schooling.

³⁰ The child labor law variable (CL) is the same for 1870 as for 1880. The empirical effects of child labor will be discussed later.

³¹ We performed an additional check on our result by recomputing the DA/P regressions in 1870 and 1880 without Massachusetts and Vermont, the states with school laws in 1870. These regressions were very similar to the ones estimated for all 38 states in 1870 and 1880, and hence support the finding that the higher levels of schooling in states with school laws in 1880 existed prior to these laws in 1870. The regression coefficient and t-values of the school law variable when Massachusetts and Vermont are excluded are presented below.

³² Although our conclusion agrees with Stigler's (see fn .1), our analysis differs from his. When Stigler held constant percent of non-white children and per capita income across states, he argued that (p. 70) “there is no evidence of a correlation between legislation and school enrollments.” In contrast, we found a positive relation across states between legislation and enrollments in 1880 even after percent of non-white population and per capita income were held constant. Since we also observed an equally strong relationship in 1870, we concluded that the legislation had no effect. Of course, our data differs from Stigler's. Stigler examined enrollment of persons 16–17 in 1940 when all states had laws. Since a dummy variable indicating the presence or absence of a law was not possible, Stigler distinguished among states on the basis of maximum age for compulsory attendance.

³³ An alternative explanation is that there was virtually no enforcement of schooling laws. According to this view, had there been enforcement we would have observed (1) larger effects in 1880 than in 1870 for the school law variable, and (2) significant positive effects for the (1870–1880) regressions. Unfortunately, we have no evidence on enforcement to test this hypothesis. Even if data were available it would be difficult to distinguish the latter hypothesis from the one put forth in the text..For example, suppose data on prosecutions of school law violations showed that there were few prosecutions. This would be consistent with both little enforcement or few violations!

³⁴ Legislation may have had effects on schooling that do not readily show up in aggregate data. For example, persons in later age brackets (12–14 years of age) could have been deterred from leaving school by these laws, and yet this would have had a small impact on the schooling levels of all school age persons. However, since we do not even find a small effect in the aggregate data, it appears unlikely that significant effects on disaggregated data would have been found.

³⁵ As noted earlier, a cross-section analysis in 1890 that compared states with and without schooling laws would not be meaningful since nearly all states outside the South had laws by 1890.

³⁶ The regression coefficient and t-value for the South dummy (R) are not presented in Table 5. They are as follows:

³⁷ See Solmon, L., “Opportunity Costs and Models of Schooling in the Nineteenth Century,” Southern Economic Journal, XXXVII, 1 (July 1970), 66–83CrossRefGoogle Scholar; Fishlow, A., “The American Common School Revival: Fact or Fancy?” in Rosovsky, H., ed., Industrialization in Two Systems: Essays in Honor of Alexander Gerschenkron (New York: Wiley, 1966)Google Scholar; Fishlow, A., “Levels of Nineteenth-Century American Investment in Education,” The Journal Of Economic History, XXVI, 4 (Dec. 1966), 418–36; and the monographs by G. Stigler and J. Folger and C. Nam.CrossRefGoogle Scholar

³⁸ Other measures of urban-rural differences across states are possible; for example, Fishlow in “Levels ….” utilized the percent of total state income emanating from agriculture. About 80 percent of the variation across states in the latter variable in 1880 can be explained by variations in per capita income (Y) and density (D). Thus, the inclusion of both Y and D in our regressions largely takes account of urban-rural differences that are measured by the percent of income emanating from agriculture.

³⁹ See L. Solmon, Table 4 for urban-rural differences in days open in 1880 and 1890.

⁴⁰ See the article by Fishlow, and E. W. Knight, Public Education in the South, (Ginn, 1922).

⁴¹ The division of the South into two groups might seem to indicate that increases in E/P, A/P and DA/P from 1900 to 1920 were partly due to schooling laws. We observe larger increases in these variables in 1900 to 1910 than 1910 to 1920 for states enacting laws before 1910,. and larger increases in 1910 to 1920 than 1900 to 1910 for states passing laws after 1910. Nevertheless, we find it difficult to attribute these increases to the laws because there were increases in E/P, A/P and DA/P prior to 1900 of the same magnitude as the largest increases after 1900. One should note further that all conclusions from Table 6 are tenuous since changes in other variables have not been held constant.

⁴² One might speculate as to why teachers and school officials would favor compulsory schooling legislation in view of our finding that these laws had no effect on levels of schooling. One answer is optimism or simply ignorance on the part of teachers and school officials. A more reasonable answer is that a compulsory schooling law is a way of coercing a small minority into increasing their schooling. The law would then produce a negligible increase in average schooling levels, which is not observable in the aggregate data.

⁴³ The correlations of the year the law was passed with 1870 schooling levels are as follows:

A/E is excluded from the table since it remained approximately constant in each state in the period under consideration.

⁴⁴ The greater decline in the standard deviations of E/P compared to the other variables is somewhat spurious. With increases over time in E/P, its standard deviations among states will decline over time simply because E/P rapidly approaches a limit in each state of about 1. However, if we were to compare the standard deviation of E/P in column (2) of Table 9 with a year later than 1870, we would largely eliminate what we are trying to show. For example, if 1890 is taken as the year of comparison, enrollment rates in 1890 among states passing laws before 1890 are relatively similar and hence the standard deviation of enrollment rates among all states in 1890 would have already been greatly reduced.