The Impact of Repealing Sunday Closing Laws on Educational Attainment€¦ · The Impact of...

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The Impact of Repealing Sunday Closing Laws on Educational Attainment

(Forthcoming in the Journal of Human Resources)

Dara N. Lee §

University of Missouri-Columbia

Abstract

Adolescents face daily trade-offs between human capital

investment, labor, and leisure. This paper exploits state variation in

the repeal of Sunday closing laws to examine the impact of a

distinct and plausibly exogenous rise in the quantity of competing

diversions available to youth on their educational attainment. The

results suggest that the repeals led to a significant decline in both

years of education and the probability of high school completion. I

explore increased employment opportunities and risky behaviors as

potential mechanisms. Further, I find a corresponding decline of

the repeals on adult wages.

JEL codes: I21, J13, J22

§ Email: [email protected]. I thank Daniele Paserman, Kevin Lang, Michael Luca, seminar

participants at Boston University, as well as two anonymous referees, for their valuable

comments and suggestions.

mailto:[email protected]

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I. Introduction

Economists and policy makers have devoted considerable effort toward examining the

determinants of educational attainment. Most of the existing economic literature focuses on

determinants within school boundaries, such as class size, peer effects, school inputs, and teacher

quality.1

However, adolescents face daily trade-offs between a variety of time-competing

options, which go beyond school to include employment, responsibilities at home, and

socializing with friends. In particular, teenagers in the United States have a relatively high degree

of autonomy in deciding what to do with their time outside of school, which amounts to almost

half of their waking hours (Larson and Verna 1999). The amount of time devoted to educational

investment depends on the many competing demands on their time and changing developmental

needs. How, if at all, are youth education outcomes affected by time-competing diversions?

This paper exploits state variation in the repeal of Sunday closing laws, also known as

“blue laws”, to examine the impact of a distinct and exogenous rise in the number of competing

options available to youth on their educational attainment. Blue laws refer to laws that restrict

retail activities on Sunday, the day of religious observance for the majority of the U.S. While

blue laws were traditionally in place in nearly all states, a large number of states have repealed

them over the past 50 years. The repeals were driven by varied and idiosyncratic reasons, but

such reasons were arguably independent of policies related to education. The repeal of blue laws

therefore presents a unique opportunity to investigate the effect of competing options on

education outcomes.

The impact of repealing blue laws on educational attainment is a priori unclear. On one

1 Refer to the Handbook of Economics of Education series for a comprehensive summary of

recent findings on these areas.

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hand, allowing retail activity on Sundays raises the opportunity cost of studying for youth by

offering alternatives for work, leisure, and consumption. Teenagers now have a wider selection

of activities to occupy them on Sunday, such as going shopping or socializing with friends at the

mall.2 There could also returns to coordination – if teens work or hang out on Sundays at the

mall, other youth may be drawn to do so as well if their utility from such activities benefits from

the presence of peers (Jenkins and Osberg 2005). Further, many retail stores hire teenagers

(Porterfield and Winkler 2007), so that the opportunity cost of studying on Sundays is even

higher when accounting for potential lost wages. In addition, Gruber and Hungerman (2008,

henceforth GH) show that the repeal of blue laws was associated with increases in risky

behaviors such as higher drug and alcohol consumption, which could decrease both the incentive

and ability to study. On the other hand, the increased availability of weekend jobs could allow

financially disadvantaged but motivated students to pursue their academic objectives

independently of their family's income. Youth who choose to work while in school may also

learn to manage time more effectively, work in a team environment, or acquire other skills that

could affect their education outcomes and future wages (Michael and Tuma 1984).

Using Census microdata from the Integrated Public Use Microdata Series (Ruggles et al.

2008), I adopt a differences-in-differences approach to compare the educational attainment of

individuals in a state who were young enough to have been affected by the repeals versus those

who were not, relative to other states in the sample. I find that the repeal of blue laws led to a

2 It is a well-documented social phenomenon in both academic literature (Lewis 2004; Matthews

et al. 2000) and popular media that youth tend to congregate at shopping malls on weekends.

This is a phenomenon perhaps best represented by classic teen movies such as “Clueless”,

“Mallrats” and “Fast Times at Ridgemont High”.

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statistically significant decrease of approximately 0.11 years in completed education, and a 1.2

percentage point decrease in the probability of completing high school. These effects are

economically significant, even when compared to estimates from targeted education programs. I

also find a corresponding decline in adult wages and occupational standing measures. These

results do not seem to be driven by declines in education prior to the law change, and hold when

including state-specific education and economic controls, birth cohort and state of birth fixed

effects, as well as state-year time trends. Thus, I argue that the increase in time-competing

diversions due to the repeal of blue laws led to the decline in educational attainment in youth.

I explore several channels to explain the observed decline in education outcomes. First, I

examine the role of youth employment, using data from the Current Population Survey (CPS).

The repeal of blue laws drew teens into the labor force, and especially into the retail industry.

However, I find no impact on youth employment on the intensive margin. The results suggest

that labor force participation could be one mechanism through which the repeal of blue laws led

marginal youth to invest less in education. Second, I provide a back-of-an-envelope calculation

to show that increased drug and alcohol use associated with the repeals (GH) could explain part

of the reduction in education outcomes. Finally, I propose that declining church attendance due

to the repeal of blue laws could also have affected educational performance.

The contributions of this paper are two-fold. This paper is a first step in examining a

question that should be of broad interest to labor economists and education policy-makers alike:

how do time-competing options in teens’ free time affect their human capital investment? In an

era of declining high school completion rates (Heckman and LaFontaine 2007), it is essential to

examine how youth determine their educational investment decisions during their formative

teenage years. Studies of time use demonstrate that teenagers spend most of their free time on

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social and non-productive activities (Shann 2001; Sener and Bhat 2007) – if the set of time-

competing diversions in their free time expands to include more recreational and employment

opportunities, would teens choose those that lead to lower education outcomes, even at the cost

of lower future income? The repeal of blue laws provides a unique setting for investigating this

question, and the results suggest that, on an aggregate level, the answer is yes. The negative and

economically significant impact on both educational attainment and wages highlights the need

for further research, and also suggests there may be scope for policy intervention.

Second, it is important to study of the repeal of blue laws from a historical perspective.

The repeal of blue laws was by no means a minor event or constrained to the United States.

Sunday closing laws were in place in almost all of the United States, and variants of them still

hold in many European countries. A number of papers have demonstrated the wide-ranging

impact of the repeal of blue laws. GH find that the increased opportunity cost of church

attendance on Sundays led to lower church attendance and donations, as well as increased

participation in risky behaviors. In other work, Gerber, Gruber, and Hungerman (2010) find that

the repeal of blue laws led to lower voting turnout, which suggest that church attendance may

have causal influence on political participation. Cohen-Zada and Sander (2011) show that

repealing blue laws led to a measurable and lasting decline in the level of religious participation

of white women and in their happiness. While the broader question of interest of this paper is

how competing diversions affect youth educational attainment, this paper also contributes to a

growing body of work that shows the repeal of blue laws had significant impacts on different

aspects of society.

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II. Data and Identification Strategy

I use the 1990 5% and 2000 5% Census samples (Ruggles et al. 2008) from the Integrated

Public Use Microdata Series (IPUMS) to examine how the repeal of blue laws affected education

outcomes. Since the dependent variable of interest is final educational attainment, I restrict the

analysis to individuals between the ages 25 and 60, who should have completed their formal

schooling. The empirical analysis is restricted to sixteen states where a discrete and significant

change in their blue laws could be identified, and eight states that never had blue laws. The main

reason for the restriction is because many states had blue laws that were decided at the county or

city level. Other states were not included in the regression sample because the exact year the

laws were repealed could not be verified. Table 1 documents the 16 states with the year of repeal

for each state. The eight states that never had blue laws in place are Arizona, California,

Colorado, Idaho, Nevada, New Mexico, Oregon, and Wyoming.

In order to explore the impact on youth employment, I use data from the March Annual

Demographic Survey for the years 1962 to 2000, restricting the sample to teens between the ages

14 to 18 and the same 24 states as the education analysis. The March CPS contains key variables

of interest such as current work, industry and hours worked last week, but it lacks data on current

earnings. To complement the March data, I also provide results using the CPS May Supplement

Files, which cover the years 1968-1987, and the CPS Merged Outgoing Rotation Groups, which

began in 1979. The three datasets together help provide a more complete picture of how the

repeal of blue laws affected youth employment.

Table 2 presents summary statistics on key variables. Years of completed schooling are

defined by assigning a single number for typical years of education completed using the

educational attainment variable in the IPUMS data (or the median number of years if a range is

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given).3 The high school and grade completion variables are equal to 1 (and zero otherwise) if

the individual completed at least that level of education. Annual earnings refer to the total pre-tax

wage and salary income for the previous year. Weekly earnings are annual earnings divided by

the number of weeks that the respondent reported to have worked during the previous year.

Summary statistics of youth employment using the CPS data are presented in Panel B. It should

be noted the means are higher using the MORGs because the dataset does not cover 14 and 15

year olds, and the average age in the sample is thus older. As it can be seen, the retail industry is

a popular choice for teens: among those in the labor force, around a third is in the retail industry.

I employ a differences-in-differences empirical strategy to compare the education

outcomes of youth that were “treated” by the repeals versus those who were not, relative to

individuals in other states in the sample. More specifically, I define the treatment group in a state

as all individuals who were younger than 14 in the year of the repeal, and the control group as

those who were older than 18 in the state. I focus on age 14 because that is the youngest age at

which teens in U.S. are allowed to work. The following few years are also the formative middle

and high school years during which peer effects play a large role (Steinberg and Cauffmann

1996) and the decision of whether to continue to college is made. Individuals who were between

the ages 14 and 18 in the year of repeal belonging to the state are omitted from the sample

because the effect of the repeals on their education outcomes was likely muted. To give an

example, in the case of Iowa where blue laws were repealed in 1955, the treated group would be

all individuals who were born after 1941, i.e., they are younger than 14 before the repeal in 1955,

3 Specifically, the years of education is defined as 12 for having graduated high school or

completing the GED, for an associate’s degree, 16 for a bachelor’s degree, 18 for master’s

degree, 20 for a professional degree, and 21 for a doctorate.

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and the control group consists of individuals who were older than 18 before 1955. Then the

second difference will be to individuals of the same birth cohorts in other states in the sample,

where Sunday closing laws have yet to be repealed.4 Since I am examining how the repeals

affect youth in their teens but observe their educational attainment as adults, I base the main

analysis using state of birth as the state identifier, which should be a more appropriate proxy than

state of residence for the legal environment during adolescent years. Using state of birth also

avoids selective migration bias induced by career decisions; for example, if individuals move to

another state to take advantage of new employment opportunities induced by the repeal of blue

laws.

The identification strategy rests upon the case that the repeals were not correlated with

changes in education policies that could directly affect educational attainment. I argue that this

assumption is satisfied for several reasons. First, the repeals were unlikely to be driven by

reasons related to education policies. To give a brief background, the Supreme Court upheld the

constitutionality of blue laws in its 1961 landmark case McGowan v. Maryland, but also stated

that blue laws could be found unconstitutional if their classification of prohibited activities rested

“on grounds wholly irrelevant to the achievement of the State’s objective,” which was to

promote the secular values of “health, safety, recreation, and general well-being” through a

common day of rest.5 Blue laws in a number of states were repealed through challenging their

4 For example, since Virginia did not repeal blue laws until 1975, 20 years after Iowa’s repeal,

the cohorts born between 1932 and 1961 in Virginia were not treated by the repeals and can thus

serve as the second difference for both Iowa’s treated and untreated cohorts born in the same

years.

5 McGowan v. Maryland, 366 U.S. 420 (1961)

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constitutionality based on the Maryland ruling. Other reasons for blue law repeal were actions by

a key individual or lobbying by regulated industries (GH). Price and Yandle (1987) suggest that

increasing female labor force participation and higher demand for Sunday shopping, as well as

declining support from labor unions, could have contributed to the repeal of blue laws. Given the

existing research, it seems reasonable to assume that the reasons for repealing blue laws were not

systematically related to education. Nonetheless, I control for a number of school quality

measures in certain specifications, which should help capture any state-level varying policy

attitudes towards education.

In addition, I test this identifying assumption empirically by examining the correlation

between the repeal of blue laws and education variables, as well as a number of socioeconomic

variables. In essence, I predict the changes in the laws for the period of 1950-2000 as a function

of pupil-teacher ratio, average public school teacher salaries, average expenditures per student,

state characteristics, state and year fixed effects (results not shown). The coefficients on the

education variables (and of other state characteristics), are all statistically insignificant, providing

evidence that the repeal of blue laws was not correlated with changes in education policies.6

Finally, I consider the major education policy changes that have been widely documented in the

labor economics literature in the Section V, including compulsory schooling and minimum

kindergarten entry age, and show that these changes are not driving the results.

The basic regression framework is as follow:

(1)

6 This is consistent with Cohen-Zada and Sander (2011), who also do not find statistically

significant relationships between the repeal of blue laws and a host of state characteristics.

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where is the completed years of schooling for individual i in state j belonging to year of

birth cohort b, observed in Census year y. is a dummy variable indicating whether the

individual belongs to the treated cohort b in state of birth j, i.e., is set to unity if blue

laws were repealed in state of birth j by the time the individual belonging to birth year cohort b

turned 14. is then the coefficient of interest – it assesses whether the repeal of blue laws causes

a deviation from a state’s mean of educational attainment relative to other states where blue laws

have yet to be repealed. and are the state of birth and birth year cohort fixed effects.

represents Census year fixed effects. Since I am identifying the final completed years of

education of individuals in after they turn 25, I include only two (time-invariant) individual

characteristics in – gender and race. includes a set of state-specific demographic,

economic, and education controls associated with the birth cohort at age 14, including the

percentage of state population under 5, between 6 and 18, 45 to 65, and above 65, population,

inflation-adjusted disposable income per capita, rate of insured unemployment, inflation-adjusted

per capita retail sales, pupil-teacher ratio, inflation-adjusted average teacher salaries and

inflation-adjusted average expenditure per pupil in public elementary and secondary schools.7

is the usual error term.

To shed light on how repealing blue laws affected educational attainment, I first provide

some graphical evidence of the impact of repeals. Figure 1 depicts the simple means of years of

7 Education data were obtained from Historical Trends: State Education Facts, 1969 to 1989,

published by the National Center for Education Statistics (NCES), and other years of the Digest

of Education Statistics, also published by NCES. Data from a few missing years are linearly

interpolated.

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schooling of cohorts who were between 14 and 18 years old in the beginning of every decade

since 1950. The figures essentially provide visual snapshots of the treated and control cohorts in

repeal states versus control states. For example, Figure 1.1 depicts the final educational

attainment of those who were 14-18 year olds in 1960 (the “before” group) and 1970 (“after”

group), in states which repealed blue laws in the 1960s, (Kansas, Washington, and Florida),

versus the other states in the sample. There are two things to note. First, the figures help capture

the general trend of educational attainment from the 1950s to 1990s. From 1950-1970, the older

cohorts achieved less total schooling than the younger cohorts. The trend reverses after 1970,

when the total schooling of the younger cohorts falls behind (Figure 1.3). Second, the figures

help show that the negative impact of repealing blue laws on education is driven primarily by the

“second” difference and also by the earlier repeals in 1950s and 1960s. To illustrate, the older

cohorts (those who were 14-18 year olds in 1950) in Figure 1.1 had lower educational attainment

overall, but the increase in schooling from the older cohorts to the younger cohorts (14-18 year

olds in 1960) in the repeal states is noticeably smaller than the increase between the two cohorts

in the control states. In Figures 1.3 and 1.4, there is less of a visible difference in schooling

between the younger and older cohorts across the repeal and control states.

Next, Figure 2 provides an “eyeball” robustness check using cohorts who were 24 to 28

year olds at the beginning of each decade. These cohorts should have achieved their final

educational attainment and thus should not have been affected by the repeal of blue laws.

Reassuringly, there are no obvious differences in the educational attainment between the younger

and older cohorts in the repeal states versus control states in all four panels. I also empirically

run this as a falsification test by including a placebo dummy, which is set to unity if the repeal

occurred in the individual’s state of birth before the individual turned 24, in certain

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specifications.

III. Regression Results

The results from estimating Equation (1) are presented in Table 3. Since the repeal

dummy varies on the state of birth/birth year level, but is constant across individuals within state

of birth/birth year cells, estimating Equation (1) directly using OLS may overstate the precision

of the estimates in the presence of group error terms (Bertrand, Duflo and Mullainathan 2004,

Donald and Lang 2007). The other issue is that the main analysis is performed on 16 to 24 states,

which may not count as a large number of clusters. As noted by Donald and Lang (2007), the t-

statistics generated by the standard clustering method for correcting for common group errors are

asymptotically normally distributed only as the number of groups goes to infinity. This paper

employs the two-step procedure in Donald and Lang (2007), which is efficient and produces t-

statistics with t-distributions under general assumptions and if the number of members of each

group is sufficiently large.8,9

The first dependent variable I examine is the number of years of completed schooling.

Column (1) shows the basic difference-in-difference regression, controlling for state of birth,

8 In the first step, years of education are regressed on all individual level variables and a

complete set of state of birth/birth year dummies. In the second step the estimated coefficients on

these dummies are regressed on other state-level variables, state and year fixed effects, with

standard errors clustered at the state level.

9 Standard errors obtained by estimating Equation (1) directly and clustered by state to account

for serial correlation within state (Bertrand, Duflo and Mullainathan 2004) give very similar

results and can be available by request.

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birth year, and Census year fixed effects.10

The result indicates that the repeal of blue laws

significantly reduced educational attainment by around 0.18 years. Column (2) adds on

individual, state-specific socioeconomic and education controls, which reduces the magnitude of

the effect of the repeals slightly to -0.15, but the estimate remains statistically significant at 1

percent. The regression model in Column (3) includes time trends to capture any state-specific

trends in schooling, which reduces the coefficient on Repeal further to -011. In Column (4), I add

the eight states which never had blue laws as an additional control group, which yields similar

estimates. Finally, I run a falsification test by including a placebo dummy in the estimation,

where the dummy is set to unity if the repeal occurred before the age of 24. The majority of

individuals should have completed their education by age 24 and thus their educational

attainment should not be affected by the placebo dummy when the actual repeal dummy is

included in the regression. If educational attainment was affected by other policy changes that

occurred before the repeal of the blue laws,11

or if there was a downward trend in educational

attainment in states at the time of the repeal but not in the control states, then the estimation

could show (spurious) negative coefficients. It can be seen in Column (5) that the coefficient on

the placebo dummy is much smaller in magnitude and statistically insignificant. Further, the null

hypothesis that the two estimates (Repeal and Placebo) are equal can be rejected at the 1 percent

level. Overall, the results suggest repealing blue laws led to a decline of around 0.11 – 0.15 years

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Adding age fixed effects has a negligible effect on the estimates.

11 For example, one may be concerned that the repeal was enacted following some type of state

budget cut as a way to generate extra revenue on Sundays, but the state budget cut could also

have reduced school resources, which could generate spurious results of the repeal negatively

“impacting” educational outcomes.

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of education.12

Table 4 examines the impact on the probability of high school completion using the same

specifications as in Table 3, estimated as linear probability models.13

With no additional controls,

the repeal of blue laws led to a statistically significant 1.93 percentage points decline in the

probability of completing high school (Column 1). Including individual characteristics and state

specific controls leaves the estimate at around 1.65 percentage points (Columns 2). The addition

of state-year trends reduces the magnitude of effect to approximately 1.3 percentage points. In

Column (4), I estimate the model with the full set of controls by expanding the state sample to

include the eight states that never had blue laws. As in Table 3, I run a falsification test by

including a placebo dummy in Column (5), and the coefficient on the placebo dummy is again

very close to zero and statistically insignificant. The results from Table 4 indicate that the repeal

of blue laws led to an approximately 1.2-1.7 percentage point decline in the probability of

completing high school, which represents a 1.6 percent reduction.

In the context of existing related literature, these estimates on educational attainment are

economically significant and even comparable to some targeted education programs. For

example, Cascio (2007) investigates the long-term effects of a large public investment in

universal early education in the U.S. and finds that white children aged five after the typical state

reform were 2.5 percent less likely to be high school dropouts. Duflo (2001) examines a large

national school expansion program in Indonesia and estimates that each new school constructed

per 1,000 children was associated with an increase of 0.12 to 0.19 in years of education. Vidal-

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Analysis based on state of residence and restricting the sample to individuals who were born in

the same state yields estimates that are larger in magnitude but otherwise similar.

13 Estimates obtained using probit and logit models yield similar results.

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Fernández (2010) finds that a one-subject increase in minimum academic standards in order to

participate in school sports led to a 2 percentage point increase in the probability of high school

graduation for boys.

Table 5 attempts to shed light on when repealing blue laws had the greatest impact on an

individual’s academic career. The regressions are estimated using a linear probability model.14

The magnitude of the estimate of Repeal increases as the dependent variable goes from

completing 10th

grade to completing high school, and drops again when the dependent variable

moves from completing high school to completing the first year of college. The null hypothesis

that the coefficients on Repeal across the models in Columns 3 and 4 (completing high school

versus completing the first year of college as the dependent variable) are equal can be rejected at

the 5 percent level. The results indicate that the effect of repealing blue laws was mainly on

completing high school rather than college.

Did the reduction in educational attainment translate into lower adult earnings? Table 6

presents the reduced form impact of repealing blue laws on wage and salary income,

occupational income score, and the Duncan socioeconomic index, controlling for gender, race,

marital status, family size, and the same set of controls in previous regressions, as well as fixed

effects for birth cohort, Census year, state of birth, and state of residence, using the same sample

of 25 to 60 year olds and 24 states. The results suggest that the repeal of blue laws led to

statistically significant reductions of 1.21 percent in annual wages and 1 percent in weekly

wages. This corresponds to a reduction of 0.42 percent on the occupational income score and 1.2

percent on the Duncan socioeconomic index. The estimate on income is consistent with what the

conventionally accepted 10 percent return to schooling would predict. The results imply that

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Results from using a probit or logit model are similar.

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there was indeed a permanent and negative effect of the repeals that extended to adult earnings.

The results may be surprising – it would seem reasonable to assume that the long-run

returns to high school graduation are higher than the short-run benefits of shopping or even part-

time work. However, the results are in line with Oreopoulous (2007), who provide evidence that

dropouts drop out “too soon”: lifetime wealth increases by about 15% with an extra year of

compulsory schooling. Students compelled to stay in school are also less likely to report being in

poor health, unemployed, and unhappy. The results are consistent with the possibility that

adolescents ignore or heavily discount future consequences when deciding to drop out of school.

Experimental evidence also support that adolescents have more time-inconsistent preferences

and are more likely to opt for instant gratification than adults (Lahav et al. 2010). The results are

also consistent with Cohen-Zada and Sander (2011), who demonstrate the repeal of blue laws led

to a significant decline in happiness from less frequent church attendance, especially among

women. The effect is lasting, i.e., people do not choose to return to church although they are less

happy. The authors argue that activities such as shopping may provide higher immediate

satisfaction and people with low self-control or present-biased preferences may prefer the lower

immediate satisfaction from shopping over the larger future satisfaction from religious

participation. As blue laws are repealed and the set of choices of time-competing options

expands, teenagers who tend to be more susceptible to distractions or short-run earning

opportunities may invest less in education and ultimately achieve fewer years of schooling.

IV. Potential channels

IV.A. Increased Labor Force Participation

One possible channel for the decline in years of schooling is through increased labor

force participation – as retail activity extends to Sundays, youth could take advantage of the

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newly available employment opportunities on weekends. Marginal youth may expect their future

discounted lifetime earnings to be higher from entering the labor force full time rather than

completing high school. Working more could also compete with time spent on educational

investment and lead to worse educational outcomes. Further, the retail industry is a popular

industry for teens because of flexible hours and limited credential requirements (Bernhardt 1999,

Card 1991).

Existing research on the relationship between employment and school leaving decisions

has produced inconclusive results. On one hand, there is evidence that differences in

employment experience at ages below 16 have a positive impact on subsequent wages (Ruhm

1997) and wage differentials later in life (Michael and Tuma 1984). On the other hand, Rothstein

(2007) and Eckstein and Wolpin (1999) find that employment during high school leads to worse

school performance. Oettinger (1999) also finds similar results, and further shows summer

employment did not affect grades, suggesting that school year employment affected grades by

"crowding out" study time.

I first use the March CPS to test the impact of repealing blue laws on employment. The

sample is an unbalanced panel of the only eight states (among the 16 repeal states and the eight

“never” states) that are uniquely identified between 1962 and 1976, and all 24 states from 1977-

2000. The eight states include California, Florida, Indiana, Ohio, Oregon, Pennsylvania,

Tennessee, and Texas, among which Ohio, Pennsylvania, Texas, and Florida are repeal states.

The other 16 states are grouped regionally and cannot be distinguished from the other states in

the group until 1977. Thus, the regression sample includes the 8 states that are identifiable before

1977 and then incorporate the rest of the states post-1977. The Repeal dummy is defined to be 1

after a state repealed its blue laws. I omit the observations in the year of repeal for that state.

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The results are reported in Panel A of Table 7. The results suggest that the repeals

affected youth employment on the extensive margin by drawing teens into the labor market and

especially into the retail industry. However, the repeal of blue laws did not appear to affect youth

employment on the intensive margin. Conditional on being the labor force, neither overall hours

worked last week nor weeks worked last year changed significantly, but hours and weeks worked

in retail increased, suggesting there may have been substitution of hours towards the retail

industry after deregulation. I also experimented with using only the post-1977 years with all the

24 states, and using only the 8 states that were uniquely identified in the post-1977 years, so that

the sample is balanced. The results (not shown) are qualitatively similar.15

Since the March CPS does not contain data on current earnings, I utilize the CPS Mays

and MORGs to investigate whether youth earnings were affected. First, I estimate the impact of

repeals on the dependent variables as in Panel A, using the same set of controls and specification.

The results are presented in Panels B and C of Table 7. As it can be seen, the effect of the repeals

on youth employment on the extensive margin fades as the sample period shifts to cover later

years. In Panel B, there is still evidence of substitution of hours towards the retail industry, but

no impact on overall labor force participation is found. There is no discernible impact on any of

the employment variables when the MORGs sample is used. I do not find any effect on hourly or

weekly earnings in either sample.

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In both samples, the estimate on retail and hours worked in retail are positive and significant.

In the post-77 sample, the estimates on overall labor force participation and weeks worked in

retail are positive but statistically insignificant. The more pronounced results from using the full

sample could both be due to the larger sample size and that the earlier repeals had a stronger

effect.

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One interpretation of these results is that the earlier repeals increased labor force

participation among teens, and also led teens who were already in the labor force to substitute

work hours into the retail industry. Since it is unclear why working in the retail industry per se

would lead teens to do worse in school, a possible mechanism through which the earlier repeals

affected educational attainment could be through drawing youth into the labor force. Work could

have displaced time spent on educational investment, or led marginal youth to drop out of school

altogether, thus contributing to the observed decline in educational attainment.

These results are consistent with Goos (2005), who uses the Census of Retail Trade data

to show that deregulation increases employment by around 4.4 percent in deregulated industries.

The results are also in line with those in Skuterud (2005), who finds Sunday shopping

deregulation increases employment in retail using data from Canada. On the other hand, Gruber

and Hungerman do not find any effect of blue laws on employment using the National

Longitudinal Survey of Youth (GH footnote 17). Similarly, Cohen-Zada and Sander (2011) do

not find an impact on overall hours worked using data from the General Social Survey. However,

these results are not inconsistent with mine, as the samples used in both papers do not start until

after 1978, and I also do not find any impact on employment using the MORGs sample, which

covers the years 1979 to 2000.

IV.B. Alcohol and drug use

Another possible channel for the decline in educational attainment is increased alcohol

and illicit drug use among teens. According to the U.S. Department of Education, drug and

alcohol addiction are consistently ranked among the top three reasons for dropping out. GH find

a strong association between the repeal of blue laws and risky behaviors among church attendees

using NLSY data. In particular, they find that repealing blue laws led to an overall 0.015 (s.e. =

20

0.017) increase in the probability that the respondent had six or more drinks in one sitting in past

30 days, 0.032 (s.e.=0.013) and 0.022 (s.e.=0.008) in the probability the respondent tried

marijuana and cocaine in the last 30 days respectively. Teens may be particularly drawn to such

risky behaviors because the adolescent brain is more vulnerable than the adult brain to the effects

of addictive substances because of the extensive neuromaturational processes that are occurring

during this period (Lubman et al. 2007). The temporal gap between puberty, which impels

adolescents toward thrill seeking, and the slow maturation of the cognitive-control system, which

regulates these impulses, also makes adolescence a time of heightened vulnerability for risky

behavior (Dahl 2004). Could the increase in risky behaviors linked with the repeal of blue laws

have led to the decline in educational attainment?

A number of studies have demonstrated causal impacts of drinking and drug use on

academic outcomes. For example, Cook and Moore (1993) use state beer tax and the minimum

purchase age as instruments and find using NLSY data that youth who are frequent drinkers

complete 2.3 fewer years of education. Chatterji (2003) uses data from the National Education

Longitudinal Study in conjunction with state drug policies and 8th

grade school characteristics as

instruments for drug use during high school. She finds that marijuana use is associated with a

reduction in educational attainment of about 0.2 to 0.3 years and cocaine use with a reduction of

0.2 to 0.4 years. If we accept these estimates as causal, then a back-of-the-envelope calculation

would yield a decrease of 0.015 x 2.3 (drinking) + 0.032 x 0.2 (marijuana) + 0.022 x 0.2

(cocaine), leading to a decline of 0.045 year of education.16

This implies increased alcohol and

drug use could have contributed to the observed decline in educational attainment.

16

This estimate can be considered as an upper bound as this assumes the estimates are separately

additive, when in fact drinking may affect education through increased drug use as well.

21

IV.C. Decreased church attendance

A final channel that I discuss is the impact of lower church attendance on educational

attainment. GH find repealing blue laws led to a significant negative impact on church

attendance using data from the General Social Survey. They propose that the higher opportunity

cost of time that comes with the expansion of retail activities on Sundays led to the decline in

church attendance. There is considerable empirical evidence linking educational attainment and

religiosity, although the direction of causality is difficult to determine (Brown and Taylor 2007;

Loury 2004; Sacerdote and Glaeser 2001). From a theoretical perspective, it is possible that

church attendance increases education in a club-goods effect model (Iannaccone 1992). The idea

is that in order to prevent free-riding, the club (or church) requires some kind of high cost

behavior as a screening device. Assuming that adolescents attend church with their families,

parents may be incentivized to encourage their children to study harder or pay more attention to

their school performance in order to gain acceptance as model church-goers. As church

attendance fell with the rise of market alternatives on Sundays, parents may have felt less

pressure to ensure their children are performing to a “socially acceptable” level in school.

However, the question of whether church attendance as a child and teen could affect educational

performance is left for future research.

V. Robustness Checks

In addition to including the placebo dummy to the regression framework, I perform a

series of robustness checks to evaluate the sensitivity of the results on educational attainment.

First, I estimate the basic framework (Equation 1) leaving out each state at a time to test

whether it is not one state that is driving the results. Along a similar vein, I perform the same test

leaving out each birth decade cohort (e.g. all cohorts born in a particular decade) at a time. The

22

estimates from both tests (Table 8) remain similar and statistically significant at all times.17

It can

be seen from the latter exercise (Panel B) that the results are driven more by the earlier repeals

than the later ones, which is consistent with Figure 1.

Second, I consider large-scale education reforms that may have affected the cohorts in

this study. The reforms of lesser concern are those that would increase educational attainment.

For example, raising the minimum dropout age, Head Start, or providing universal kindergarten

programs have been shown to improve education outcomes (Cascio 2007; Garces et al., 2002;

Oreopoulos 2007). However, even if these changes were correlated with the repeal of blue laws,

programs that increase educational attainment should not be a source of concern as they operate

against the effect of repealing blue laws, i.e., the estimates would simply be upward biased. Of

more concern are policies that could have decreased education. In particular, there have been

steady increases in the minimum school entry age (i.e., the youngest age at which a child is

eligible to enter kindergarten) in a number of states since the early 1950s. As Angrist and

Krueger (1991) have noted, the older students in a class tend to have lower total schooling than

their younger peers because they start school at an older age and can drop out relatively earlier.18

The increase in the minimum school entry age could thus lead to an average decline in

educational attainment among the cohorts entering school after the law change, even if they were

17 All results in this section are also robust to using a sample of only the 16 repeal states.

18 Some economists have posited that entering school at a later age could in fact benefit

educational outcomes because the children are more mentally prepared for the academic rigors in

formal schooling (Bedard and Dhuey 2006; Elder and Lubotsky 2007). However, the general

finding is that the impact of increasing minimum age entry laws lasts up until middle school (as

measured by tests scores) but not necessarily through final educational attainment.

23

not directly affected. As a robustness check, I estimate Equation (1) controlling for the age (in

months) of the youngest member of the cohort eligible for school entry.19

For example, Florida

changed its kindergarten minimum entry law in 1985. Before 1985, a child had to turn 5 years

old before February 1 of the school year, which means the youngest children entering

kindergarten at the beginning of the school year in September were 4 years 7 months old. In

1985, Florida changed the law so that a child had to turn 5 by September 1 in order to be eligible

to enter kindergarten that year, which means the youngest children entering kindergarten were 60

months. I present the results in Table 9 (Columns 1 and 2), where Column 2 includes state-year

time trends. The sample in these restrictions is restricted to 21 states where there was a distinct

state-wide change in minimum age entry law, or if there were state-wide entry laws but no

changes, during the sample period. The coefficient on the minimum school entry age shows no

effect on schooling with the inclusion of time trends, but a negative effect is observed with time

trends.20

Of more interest is the coefficient on the Repeal dummy, which is largely unaffected.

The minimum dropout age has generally increased across states over the last century, but

there have been a few exceptions. Therefore, I run a second specification check where I control

for the minimum dropout age associated with the cohort at age 14. The intuition is similar to the

previous test: if certain states have been lowering the minimum dropout age and such changes

are correlated with the repeals, then the effect of repealing blue laws on education could be

19

This specification follows Bedard and Dhuey (2007). Since quarter of birth data are not

available in the 1990 and 2000 Census, this measure is a proxy for the actual age of entrance.

Refer to Bedard and Dhuey (2007) Appendix Table 1 for changes to school entry cutoff dates.

20 Bedard and Dhuey (2007) do not find a significant impact of the minimum school entry age on

educational attainment.

24

spurious. I present the results with and without time trends in Columns 3 and 4. Interestingly, the

estimates of the dropout age on education decrease in magnitude considerably with the inclusion

of time trends. More importantly, the coefficient on Repeal is smaller in magnitude, but does not

lose statistical significance. These specification checks help corroborate that the observed impact

of repealing blue laws on schooling is not driven by concurrent changes in education policies.

VI. Conclusion

In this study, I combine cross-state and temporal variation in the repeal of Sunday

closing laws to investigate how the quantity of time-competing options affects youth educational

attainment. By extending retail activity to Sundays, the repeal of blue laws provided teenagers

with substantially more recreational activities and employment opportunities. The results show

the repeal of blue laws led to a significant decline in years of completed education and high

school completion rates. I demonstrate that the repeal of blue laws increased labor force

participation among teens, which could help explain part of the decline in education. In addition,

I provide a back-of-the-envelope calculation that indicates risky behaviors such as binge drinking

and drug use could have been contributing factors to the decline in educational attainment. One

consistent interpretation of the results is that allowing retail activity on Sundays provided youth

with substantially more recreational activities and employment opportunities that competed with

their educational investment time, leading to lower educational attainment. However, due to

limitations of cross-sectional data, further research using panel time-use data would be needed to

discern the precise mechanisms.

From a policy perspective, these results highlight the need for student incentives to

extend beyond the classroom. For example, recent research has shown that structured time use

outside of the classroom, such as after-school programs and organized extracurricular activities,

25

can positively affect educational outcomes (Borman and Dowling 2006; Lipscomb 2007).

Making certain extra-curricular activities, such as the right to participate in school sports or earn

their driver’s license, contingent on school enrollment or academic performance, have also

demonstrated potential as strategies for improving education outcomes (Barua and Vidal-

Fernandez 2011; Vidal-Fernandez 2010).

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30

Figures & Tables

Table 1 — Years of Repeal

State Year of Repeal

Iowa 1955

Kansas 1965

Washington 1966

Florida 1969

Ohio 1973

Utah 1973

Virginia 1975

Indiana 1977

South Dakota 1977

Pennsylvania 1978

Tennessee 1981

Vermont 1982

Minnesota 1985

South Carolina 1985

Texas 1985

North Dakota 1991

Source: Gruber and Hungerman (2008)

31

Table 2 — Descriptive Statistics of Selected Variables

Variable Mean s.d.

Panel A — Adult Outcomes (ages 25-60)

Years of Completed Schooling 13.20 (2.59)

High school Completion 0.86 (0.35)

10th Grade Completion 0.95 (0.22)

11th Grade Completion 0.92 (0.27)

1st Year of College Completion 0.49 (0.50)

Wage & Salary Income (in $2000) 26,087.32 (32197.50)

Weekly Wage & Salary Income (in $2000) 720.78 (1252.23)

Occupational Income Score 25.28 (12.31)

Duncan Socioeconomic Index 39.47 (25.57)

Repeal 0.21 (0.41)

Sample size

Panel B — Youth Employment

Sample: March CPS May CPS MORGs

Ages: 14-18 14-18 16-18

Years: 1962-2000 1968-1987 1979-2000

Labor Force Participation 0.31 0.37 0.50

(0.46) (0.48) (0.50)

In Retail Industry 0.13 0.14 0.31

(0.34) (0.35) (0.46)

15.28 19.39 23.07

(14.16) (13.53) (13.11)

2.65

(1.92)

6.64 6.19

(3.98) (2.04)

159.61 152.89

(171.70) (119.95)

Repeal 0.41 0.38 0.61

(0.49) (0.49) (0.49)

Sample size 221,991 113,821 217,360

4,676,768

– Sample includes the 16 repeal states in Table 1 and 8 states that never had blue

– Underlying data in Panel A are from the 1990 and 2000 5% Census.

Hourly Earnings (in $2000),

if in labor force

Weekly Earnings (in $2000),

if in labor force

– Standard deviations in parentheses. Summary statistics are tabulated using sample person weights.

– Weeks worked intervals (Panel B): 1=1-13, 2=14-26, 3=27-39, 4=40-47, 5=48-49, 6=50-52

Weeks Worked Last Year, Intervalled,

if in labor force

Hours Worked Last Week,

if in labor force

32

Figure 1 — Educational Attainment of Individuals between Ages 14 and 18 in 1950, 1960, 1970,

and 1980, Repeal States versus Control States

1.1

1.2

1.3

1.4

12

12.2

12.4

12.6

12.8

13

13.2

13.4

13.6

Years

of S

chooling

1950 Repeal States All Other States

14-18 y.o. in 1950

14-18 y.o. in 1960

12.7

12.8

12.9

13

13.1

13.2

13.3

13.4

13.5

13.6

Years

of S

chooling


14-18 y.o. in 1960

14-18 y.o. in 1970

12.8

12.9

13

13.1

13.2

13.3

13.4

13.5

Years

of S

chooling


14-18 y.o. in 1970

14-18 y.o. in 1980

12.8

12.9

13

13.1

13.2

13.3

13.4

13.5

Years

of S

chooling


14-18 y.o. in 1980

14-18 y.o. in 1990

33

Figure 2 — Educational Attainment of Individuals between Ages 24 and 28 in 1950, 1960, 1970,

and 1980, Repeal States versus Control States

2.1

2.2

2.3

2.4

11

11.2

11.4

11.6

11.8

12

12.2

12.4

12.6

12.8

13

Years

of S

chooling


24-28 y.o. in 1950

24-28 y.o. in 1960

12

12.2

12.4

12.6

12.8

13

13.2

13.4

13.6

Years

of S

chooling


24-28 y.o. in 1960

24-28 y.o. in 1970

12

12.2

12.4

12.6

12.8

13

13.2

13.4

13.6

Years

of S

chooling


24-28 y.o. in 1970

24-28 y.o. in 1980

12.8

12.9

13

13.1

13.2

13.3

13.4

Years

of S

chooling


24-28 y.o. in 1980

24-28 y.o. in 1990

34

Table 3 — Effect of Repeal on Years of Schooling

(1) (2) (3) (4) (5)

Repeal -0.179*** -0.146*** -0.108*** -0.107*** -0.110***

(0.0482) (0.0291) (0.0146) (0.0194) (0.0202)

Placebo -0.0190

(0.0195)

Individual and State Controls

Time Trends

With "Never" States

Sample size 3,054,941 3,054,941 3,054,941 4,200,754 4,200,754

* significant at 10% ** significant at 5% *** significant at 1%

– All regressions include fixed effects for year of birth, state of birth, and Census year.

– Underlying data are from the 1990 and 2000 5% Census.

Years of schooling

– Individual controls include dummies for gender, race, and hispanic origin. State controls include

percentage of state population aged under 5, 6-18, 45-65, over 65, foreign born, black, rate of insured

unemployment, per capita disposable income, per capita retail sales, pupil-teacher ratio, average public

elementary and secondary school teacher salaries, and average expenditure per student, associated with

the cohort at age 14.

– Standard errors in parentheses. Standard errors are produced using the Donald and Lang (2007) two-

step procedure.

35

Table 4 — Effect of Repeal on High School Completion

(1) (2) (3) (4) (5)

Repeal -0.0193** -0.0165*** -0.0129*** -0.0119*** -0.0127***

(0.0067) (0.0046) (0.00236) (0.0029) (0.0027)

Placebo -0.0048

(0.0033)

Individual and State Controls

Time Trends

With "Never" States

Sample size 3,054,941 3,054,941 3,054,941 4,200,754 4,200,754


– All regressions include fixed effects for year of birth, state of birth, and Census year.

– Underlying data are from the 1990 and 2000 5% Census.

High School Competion

– Individual controls include dummies for gender, race, and hispanic origin. State controls include

percentage of state population aged under 5, 6-18, 45-65, over 65, foreign born, black, rate of

insured unemployment, per capita disposable income, per capita retail sales, pupil-teacher ratio,

average public elementary and secondary school teacher salaries, and average expenditure per

student, associated with the cohort at age 14.

– Standard errors in parentheses. Standard errors are produced using the Donald and Lang (2007)

two-step procedure.

36

Table 5 — Effect of Repeal on Different Stages of Academic Career

10th Grade

Completion

11th Grade

Completion

High School

Completion

1st Year of

College

Completion

(1) (2) (3) (4)

Repeal -0.0065** -0.0090*** -0.0119*** -0.0054**

(0.0024) (0.0027) (0.0029) (0.0027)

Sample Size 4,200,754 4,200,754 4,200,754 4,200,754


– Standard errors in parentheses. Standard errors are produced using the Donald and

Lang (2007) two-step procedure.

– All regressions include fixed effects for year of birth, state of birth, Census year, and

state-specific time trends.

– All regressions control for gender, race, hispanic origin, percent of state population

aged under 5, 6-18, 45-65, over 65, foreign born, black, rate of insured unemployment,

per capita disposable income, and per capita retail sales, pupil-teacher ratio, average

public elementary and secondary school teacher salaries, and average expenditure per

student, associated with the cohort at age 14.

– Underlying data are from the 1990 and 2000 5% Census. Sample includes the 16

states in Table 1 and the 8 states that never had blue laws.

37

Table 6 — Effect of Repeal on Earnings & Occupational Standing Measures

Log

Annual Earnings,

in 2000 $

Log

Weekly

Earnings,

in 2000 $

Log

Occupation

Income Score

Log

Socioeconomic

Index

(1) (2) (2) (3)

Repeal -0.0121** -0.0103** -0.0042*** -0.0123***

(0.0051) (0.0045) (0.0017) (0.0045)

Sample size 3,290,377 3,289,525 3,810,643 3,810,643


– Underlying data are from the 1990 and 2000 5% Census. Sample includes the 16 states in

Table 1 and the 8 states that never had blue laws.

– All regressions include fixed effects for year of birth, state of birth, state of residence, state-

specific time trends, and Census year fixed effects.

– Individual controls include gender, marital status, race, hispanic origin, family size, dummy for

farm household, and dummy for metro area household.

– State controls include percentage of state population aged under 5, 6-18, 45-65, over 65, foreign

born, black, rate of insured unemployment, per capita disposable income, and per capita retail

sales, pupil-teacher ratio, average public elementary and secondary school teacher salaries, and

average expenditure per student, associated with the birth cohort at age 14.

– Standard errors in parentheses. Standard errors are produced using the Donald and Lang

(2007) two-step procedure.

38

Table 7 — Effect of Repeal on Youth Employment

Labor Force

Participation

In Retail

Industry

Hours

Worked

Last Week

Hours Worked

in Retail

Last Week

Weeks

Worked

Last Year,

Intervalled

Weeks

Worked in

Retail Last

Year,

Intervalled

(1) (2) (3) (4) (5) (6)

Panel A - March CPS (1962-2000)

Repeal 0.0144* 0.0145** -0.5318 0.4314* -0.0480 0.0602*

(0.0071) (0.0058) (0.3713) (0.2103) (0.0374) (0.0316)

Sample size 217,543 217,543 69,303 69,303 69,271 69,271

Panel B - CPS May Extracts (1968-1987)

Labor Force

Participation

In Retail

Industry

Hours

Worked

last week

Hours worked

in Retail

last week

Hourly

Earnings, in

2000 $

Weekly

Earnings,

in 2000$

Repeal 0.0070 0.0102** -0.3817 0.3706* -0.1318 -2.1434

(0.0060) (0.0049) (0.3120) (0.2052) (0.1439) (4.5872)

Sample size 109,849 109,849 41,072 41,072 10,815 34,722

Panel C - CPS Merged Outgoing Rotation Groups (1979-2000)

Labor Force

Participation

In Retail

Industry

Hours

Worked

last week

Hours worked

in Retail

last week

Hourly

Earnings,

in 2000 $

Weekly

Earnings,

in 2000$

Repeal 0.0046 0.0067 -0.5700 0.2704 -0.0897 -7.3667

(0.0140) (0.0122) (0.4802) (0.3290) (0.1236) (4.7079)

Sample size 214,873 214,946 110,385 110,385 110,385 110,385


– All regressions control for gender, race, marital status, state-specific unemployment rate, per capita

disposable income, and per capita retail sales, pupil-teacher ratio, average public elementary and

secondary school teacher salaries, and average expenditure per student.


step procedure.

– The samples in Panels A and B are unbalanced panels of 8 states (CA, FL, IN, OH, OR, PA, TN, TX)

that are uniquely identified among the 16 repeal and 8 "never" states before 1977. The other 16 states

enter the sample after 1977.

– All regressions include fixed effects for year of birth, state, age, and year fixed effects.

39

Table 8 — Robustness Check: Are Results Driven by a Particular State or Cohort?

Panel A: Dropping Each State at a Time

Omitted State Iowa Kansas Washington Florida

-0.1024*** -0.1055*** -0.1041*** -0.1051***

(0.0198) (0.0197) (0.0213) (0.0196)

Ohio Utah Virginia Indiana

-0.1138*** -0.1071*** -0.1026*** -0.1156***

(0.0226) (0.0188) (0.0201) (0.0188)

South Dakota Pennsylvania Tennessee Vermont

-0.1089*** -0.0997*** -0.1002*** -0.1072***

(0.0196) (0.0226) (0.0208) (0.0195)

Minnesota South Carolina Texas North Dakota

-0.1149*** -0.1063*** -0.0832*** -0.1070***

(0.0181) (0.0200) (0.0210) (0.0209)

Arizona California Colorado Idaho

-0.1096*** -0.1013*** -0.1086*** -0.1055***

(0.0195) (0.0179) (0.0191) (0.0188)

Nevada New Mexico Oregon Wyoming

-0.1066*** -0.1141*** -0.1029*** -0.1064***

(0.0193) (0.0179) (0.0188) (0.0193)

Panel B — Dropping each Birth Decade Cohort at a Time

1930's 1940's 1950's 1960's 1970's

-0.104*** -0.0988*** -0.114*** -0.123*** -0.107***

(0.0182) (0.0195) (0.0286) (0.0350) (0.0194)


Omitted Birth

Decade Cohort

– All regressions control for gender, race, hispanic origin, percent of state population aged under 5, 6-

18, 45-65, over 65, foreign born, black, rate of insured unemployment, per capita disposable income,

and per capita retail sales, pupil-teacher ratio, average public elementary and secondary school

teacher salaries, and average expenditure per student, associated with the cohort at age 14.

– Standard errors in parentheses. Standard errors are produced using the Donald and Lang (2007)

two-step procedure.

– Underlying data are from the 1990 and 2000 5% Census. Sample includes the 16 states in Table 1

and 8 states that never had blue laws.

– Each cell represents a separate regression. Dependent variable is number of years of schooling.

Birth decade cohort refers to all cohorts born in the particular decade.

– All regressions include fixed effects for year of birth, state of birth, state of residence, state-specific

time trends, and Census year fixed effects.

40

Table 9 — Robustness Check: Controlling for Minimum Kindergarten Entry Age and

Compulsory Schooling

(1) (2) (3) (4)

Repeal -0.1314*** -0.1267*** -0.0794*** -0.0936***

(0.0215) (0.0172) (0.0349)

Minimum School Entry Age -0.0131 -0.0419***

(0.0330) (0.0128)

Dropout Age = 16 0.1305*** 0.0142

(0.0299) (0.0261)

Dropout Age = 17 0.2561*** 0.0685*

(0.0483) (0.0364)

Dropout Age = 18 0.0761 0.0284

(0.0528) (0.0322)

Time Trends

Sample size 3,389,931 3,389,931 4,200,754 4,200,754


Years of Schooling


step procedure.

– All regressions control for gender, race, hispanic origin, percent of state population aged under 5, 6-18, 45-

65, over 65, foreign born, black, rate of insured unemployment, per capita disposable income, and per capita

retail sales, pupil-teacher ratio, average public elementary and secondary school teacher salaries, and

average expenditure per student, associated with the cohort at age 14.

– Underlying data are from the 1990 and 2000 5% Census. Sample includes the 16 states in Table 1 and

the 8 states that never had blue laws.

– The omitted category in the regression in Columns 3 and 4 is Dropout Age = 15.

– All regressions include fixed effects for year of birth, state of birth, Census year.

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