Manajemen | Fakultas Ekonomi Universitas Maritim Raja Ali Haji 286.full

The Impact of Repealing

Sunday Closing Laws on

Educational Attainment

Dara N. Lee

A B S T R A C T

Adolescents face daily tradeoffs 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 signifi cant decline in both years of education and the probability of high school completion. I explore increased employment and risky behaviors as potential mechanisms. Further, I fi nd a corresponding decline of the repeals on adult wages.

I. Introduction

Economists and policymakers 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 ef-fects, school inputs, and teacher quality.1 _{However, adolescents face daily tradeoffs} be-tween a variety of time- competing options, which go beyond school to include employ-ment, 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?

1. Refer to the Handbook of Economics of Education series for a comprehensive summary of recent fi ndings on these areas.

Dara N. Lee is an assistant professor of economics at the University of Missouri. The author would like to thank Kevin Lang, Michael Luca, Daniele Paserman, seminar participants at Boston University, as well as two anonymous referees, for their valuable comments and suggestions. The data used in this article can be obtained beginning October 2013 through September 2016 from the author at leedn@missouri.edu. [Submitted April 2010; accepted May 2012]

SSN 022 166X E ISSN 1548 8004 8 2013 2 by the Board of Regents of the University of Wisconsin System T H E J O U R N A L O F H U M A N R E S O U R C E S • 48 • 2

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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 United States. 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 there-fore 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 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 shop-ping or socializing with friends at the mall.2 _{There also could be returns to} coordina-tion—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 bene_fi ts from the presence of peers (Jenkins and Osberg 2005). Further, many retail stores hire teenagers (Porter_fi eld 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 _fi nancially disadvantaged but motivated students to pursue their academic objectives independently of their family’s income. Youth who choose to work while in school also may 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 _fi nd that the repeal of blue laws led to a statistically signi_fi cant decrease of approximately 0.11 years in completed education, and a 1.2 percentage point decrease in the probabil-ity of completing high school. These effects are economically signi_fi cant, even when compared to estimates from targeted education programs. I also _fi nd 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 includ-ing state- speci_fi c education and economic controls, birth cohort, and state of birth

fi xed 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.

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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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 Popula-tion Survey (CPS). I _fi nd some evidence that the repeal of blue laws drew teens into the labor force, especially into the retail industry. However, I _fi nd no impact on youth employment on the intensive margin. The results suggest that labor force participation may have been 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 calcula-tion to show that increased drug and alcohol use associated with the repeals (GH) could explain part of the reduction in educational attainment. Finally, I propose that declining church attendance due to the repeal of blue laws also could have affected educational performance.

The contributions of this paper are twofold. This paper is a _fi rst 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 educa-tional investment decisions during their formative teenage years. Studies of time use demonstrate that teenagers spend most of their free time on social and nonproductive 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 investigat-ing this question, and the results suggest that, on an aggregate level, the answer is yes. The negative and economically signi_fi cant 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 perspec-tive. 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 _fi nd that the increased opportunity cost of church attendance on Sundays led to lower church at-tendance and donations, as well as increased participation in risky behaviors. In other work, Gerber, Gruber, and Hungerman (2008) _fi nd that the repeal of blue laws led to lower voting turnout, which suggest that church attendance may have causal in_fl uence 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 signi_fi cant impacts on different aspects of society.

II. Data and Identi

fi

cation Strategy

I use the 1990 5 percent and 2000 5 percent Census samples (Ruggles et al. 2008) from the Integrated Public Use Microdata Series (IPUMS) to examine how

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the repeal of blue laws affected education outcomes. Because the dependent variable of interest is _fi nal 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 16 states where a discrete and signi_fi cant change in their blue laws could be identi_fi ed, 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 veri_fi ed. 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 Files from the CPS 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 anal-ysis. The March CPS contains key variables of interest such as current work, industry, and hours worked last week, but lacks data on current earnings. To complement the March data, I also provide results using the CPS May Supplement Files, which cover the years 1968–87, and the CPS Merged Outgoing Rotation Groups (MORGs), 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 de_fi ned by assigning a single number for typical years of education completed us-ing the educational attainment variable in the IPUMS data (or the median number of

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

Table 2

Descriptive Statistics of Selected Variables

Variable Mean

Standard Deviation 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 and salary income (in $2000) 26,087.32 (32,197.50) Weekly wage and salary income

(in $2000)

720.78 (1,252.23)

Occupational income score 25.28 (12.31)

Duncan socioeconomic index 39.47 (25.57)

Repeal 0.21 (0.41)

Sample size 4,676,768

Panel B—Youth employment

Source: March CPS May CPS MORGs

Ages: 14–18 14–18 16–18

Years: 1962–2000 1968–87 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)

Hours worked last week, if in labor force

15.28 19.39 23.07

(14.16) (13.53) (13.11)

Weeks worked last year, intervalled, if in labor forcea

2.65

(1.92)

Hourly earnings (in $2000), if in labor force

6.64 6.19

(3.98) (2.04)

Weekly earnings (in $2000), if in labor force

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

Notes: Standard deviations in parentheses. Summary statistics are tabulated using sample person weights. Underlying data in Panel A are from the 1990 and 2000 5 percent Census. Sample includes the 16 repeal states in Table 1 and eight states that never had blue laws.

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years if a range is 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 pretax 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 strategy to compare the education outcomes of youth that were “treated” by the repeals versus those who were not, relative to in-dividuals in other states in the sample. More speci_fi cally, I de_fi ne 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 United States 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 be-cause 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, that is, they are younger than 14 before the repeal in 1955, 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 identi_fi er, 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 individu-als move to another state to take advantage of new employment opportunities induced by the repeal of blue laws.

The identi_fi cation 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 satis_fi ed for several reasons. First, the repeals were un-likely 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 classi_fi cation of prohibited activities rested “on grounds wholly irrelevant to the achievement of the State’s objective,” which was to promote the secular values of 3. Specifi cally, the years of education is defi ned 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.

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.

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“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 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 shop-ping, as well as declining support from labor unions, could have contributed to the re-peal 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. Nonethe-less, I control for a number of school- quality measures in certain speci_fi cations, which should help capture any state- level varying policy attitudes towards education.

In addition, I test this identifying assumption empirically by examining the correla-tion between the repeal of blue laws and educacorrela-tion 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 the pupil- teacher ratio, average public school teacher salaries, average expenditures per student, state characteristics, state and year _fi xed effects (results not shown). The coef_fi cients on the education variables (and of other state characteristics), are all statistically insigni_fi cant, providing evidence that the re-peal 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 the results are not driven by these changes.

The basic regression framework is as follow:

(1) S_ijby = αj +δb+ γy + Repealjbβ+ Xijbθ+Zjbρ +εijby

where S_ijby is the completed years of schooling for individual i in state j belonging to year of birth cohort b, observed in Census year y. Repeal_jb is a dummy variable indi-cating whether the individual belongs to the treated cohort b in state of birth j, that is, Repeal_jb 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.β is then the coef_fi cient of inter-est—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. α_j and δ_r are the state of birth and birth year cohort _fi xed effects. γ_y repre-sents Census year _fi xed effects. Since I am identifying the _fi nal completed years of education of individuals in after they turn 25, I include only two (time- invariant) in-dividual characteristics in X_ijbr—gender and race. Z_jb includes a set of state- speci_fi c demographic, economic, and education controls associated with the birth cohort at age 14, including the percentage of state population younger than 5, between 6 and 18, 45 to 65, and older than 65, population, in_fl ation- adjusted disposable income per capita, rate of insured unemployment, in_fl ation- adjusted per capita retail sales, pupil- teacher ratio, in_fl ation- adjusted average teacher salaries and in_fl ation- adjusted

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

6. This is consistent with Cohen- Zada and Sander (2011), who also do not fi nd statistically signifi cant rela-tionships between the repeal of blue laws and a host of state characteristics.

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age expenditure per pupil in public elementary and secondary schools.7_ε

ijby is the usual error term.

To shed light on how repealing blue laws affected educational attainment, I _fi rst provide some graphical evidence of the impact of repeals. Figure 1 depicts the simple means of years of schooling of cohorts who were between 14- and 18- years- old in the beginning of every decade since 1950. The _fi gures essentially provide visual snapshots of the treated and control cohorts in repeal states versus control states. For example, Figure 1.1 depicts the _fi nal educational attainment of those who were 14–18- year- olds in 1960 (the “before” group) and 1970 (“after” group), in states that repealed blue laws in the 1960s, (Kansas, Washington, and Florida), versus the other states in the sample. Two things to note: First, the _fi gures help capture the general trend of educational attainment from the 1950s to 1990s. From 1950–70, 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 _fi gures help show that the negative impact of repealing blue laws on education is driven primar-ily 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 notice-ably 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 _fi nal educational attainment and thus should not have been affected by the repeal of blue laws. Reassuringly, there are no obvious differences in the educational attain-ment between the younger and older cohorts in the repeal states versus control states in all four panels. I also empirically run this as a falsi_fi cation 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 speci_fi cations.

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, Du_fl o, 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 asymptoti-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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1.1 1.2

1.3 1.4

Figure 1

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295

2.1 2.2

2.3 2.4

Figure 2

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cally normally distributed only as the number of groups goes to in_fi nity. This paper employs the two- step procedure in Donald and Lang (2007), which is ef_fi cient and produces t- statistics with t- distributions under general assumptions and if the number of members of each group is suf_fi ciently large.8,9

The _fi rst dependent variable I examine is the number of years of completed school-ing. Column 1 shows the basic difference- in- difference regression, controlling for state of birth, birth year, and Census year _fi xed effects.10 _{The result indicates that the} repeal of blue laws signi_fi cantly reduced educational attainment by around 0.18 years. Column 2 adds on individual, state- speci_fi c socioeconomic and education controls, which reduces the magnitude of the effect of the repeals slightly to –0.15, but the estimate remains statistically signi_fi cant at 1 percent. The regression model in Column 3 includes time trends to capture any state- speci_fi c trends in schooling, which reduces the coef_fi cient on Repeal further to –0.11. In Column 4, I add the eight states which never had blue laws as an additional control group, which yields similar estimates. 8. In the fi rst 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 predicted values of these dummies are regressed on other state- level variables, state and year fi xed 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, Dufl o, and Mullainathan 2004) give very similar results and are available by request.

10. Adding age fi xed effects has a negligible effect on the estimates.

Table 3

Effect of Repeal on Years of Schooling

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

Notes: * signifi cant at 10 percent ** signifi cant at 5 percent *** signifi cant at 1 percent. Standard errors in parentheses. Standard errors are produced using the Donald and Lang (2007) two- step procedure. All regres-sions include fi xed effects for year of birth, state of birth, and Census year. Individual controls include dum-mies for gender, race, and Hispanic origin. State controls include percentage of state population aged younger than 5, 6–18, 45–65, older than 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. Underlying data are from the 1990 and 2000 5 percent Census.

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Finally, I run a falsi_fi cation 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 ma-jority 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 coef_fi cients. It can be seen in Column 5 that the coef_fi cient on the placebo dummy is much smaller in magnitude and statistically insigni_fi cant. Further, the null hypothesis that the two estimates (Repeal and Placebo) are equal can be rejected at the 1 percent level. Over-all, the results suggest repealing blue laws led to a decline of around 0.11–0.15 years of education.12

Table 4 examines the impact on the probability of high school completion using the same speci_fi cations as in Table 3, estimated as linear probability models.13 _{With no} ad-ditional controls, the repeal of blue laws led to a statistically signi_fi cant 1.93 percent-age point decline in the probability of completing high school (Column 1). Including individual characteristics and state speci_fi c controls leaves the estimate at around 1.65 percentage points (Columns 2). The addition of state- year trends reduces the mag-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 also could have reduced school resources, which could generate spurious results of the repeal negatively “impacting” educational outcomes. 12. 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 from probit and logit models are similar.

Table 4

Effect of Repeal on High School Completion

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 Note: see notes from Table 3.

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nitude 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 falsi_fi cation test by including a placebo dummy in Column 5, and the coef_fi cient on the placebo dummy is again very close to zero and statistically insigni_fi cant. 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 attain-ment are economically signi_fi cant and even comparable to some targeted education programs. For example, Cascio (2009) investigates the long- term effects of a large public investment in universal early education in the United States and _fi nds that white children aged _fi ve after the typical state reform were 2.5 percent less likely to be high school dropouts. Du_fl o (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- Fernández (2011) _fi nds that a one- subject increase in minimum academic standards in order to participate in school sports led to a two 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 prob-ability model.14 _{The magnitude of the estimate of Repeal increases as the dependent} variable goes from completing tenth grade to completing high school, and drops again when the dependent variable moves from completing high school to completing the

fi rst year of college. The null hypothesis that the coef_fi cients on Repeal across the models in Columns 3 and 4 (completing high school versus completing the _fi rst 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? 14. Using probit and logit models yield similar results.

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

Note: see notes from Table 3. All regressions include fi xed effects for year of birth, state of birth, Census year, and state- specifi c time trends. Sample includes the 16 states in Table 1 and the eight states that never had blue laws.

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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 re-gressions, as well as _fi xed 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 sug-gest that the repeal of blue laws led to statistically signi_fi cant 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 socio-economic index. The estimate on income is consistent with what the conventionally accepted 10 percent return to schooling would predict. The results imply that 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 bene_fi ts 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 percent 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 un-happy. The results are consistent with the possibility that adolescents ignore or heav-ily 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 grati_fi cation 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 signi_fi cant decline in happiness from less frequent church attendance, especially among women. The effect is lasting—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 shop-ping over the larger future satisfaction from religious participation. As blue laws are

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

Notes: see notes from Table 3. All regressions include fi xed effects for year of birth, state of birth, state of residence, state- specifi c time trends, and Census year fi xed effects. Additional controls include marital status, family size, dummy for farm household, and dummy for metro area household. Sample includes the 16 states in Table 1 and the eight states that never had blue laws.

The Journal of Human Resources 300

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

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 newly available employment opportunities on weekends. Marginal youth may ex-pect their future discounted lifetime earnings to be higher from entering the labor force full time rather than completing high school. Working more also could 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 fl exible hours and limited credential requirements (Card 1991).

Existing research on the relationship between employment and school leaving deci-sions has produced inconclusive results. On one hand, there is evidence that differ-ences in employment experience at ages younger than 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) fi nd that employment during high school leads to worse school performance. Oettinger (1999) also fi nds similar results, and further shows summer employment did not affect grades, suggesting that school year employment affected grades by “crowding out” study time. I fi rst 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 identifi ed between 1962 and 1976, and all 24 states from 1977 to 2000. The eight states include California, Florida, Indiana, Ohio, Oregon, Pennsylvania, Tennessee, and Texas, among which Ohio, Pennsylva-nia, 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 eight states that are identi_fi able before 1977 and then incorporate the rest of the states post- 1977. The Repeal dummy is defi ned to be 1 after a state repealed its blue laws. I omit the observations in the year of repeal for that state. 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 in the labor force, neither overall hours worked last week nor weeks worked last year changed signi_fi cantly, 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 eight states that were uniquely identifi ed in the post- 1977 years, so that the sample is balanced. The results (not shown) are qualitatively similar.15

15. In both samples, the estimate on working in retail and hours worked in retail are positive and signifi cant. In the post- 77 sample, the estimates on overall labor force participation and weeks worked in retail are

posi-Lee

301

Table 7

Effect of Repeal on Youth Employment Panel A—March CPS (1962–2000)a

Labor Force Participation

(1)

In Retail Industry

(2)

Hours Worked Last Week

(3)

Hours Worked in Retail Last Week

(4)

Weeks Worked Last Year, Intervalled

(5)

Weeks Worked in Retail Last Year,

Intervalled (6) 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 (1968–87)b

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

The Journal of Human Resources

302

Table 7 (continued)

Panel C—CPS Merged Outgoing Rotation Groups (1979–2000)c

Labor Force Participation

(1)

In Retail Industry

(2)

Hours Worked Last Week

(3)

Hours Worked in Retail Last Week

(4)

Weeks Worked Last Year, Intervalled

(5)

Weeks Worked in Retail Last Year,

Intervalled (6) 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 Notes: * signifi cant at 10 percent ** signifi cant at 5 percent *** signifi cant at 1 percent. Standard errors in parentheses. Standard errors are produced using the Donald and Lang (2007) two- step procedure. All regressions include fi xed effects for year of birth, state, age, and year fi xed effects. All regressions control for gender, race, marital status, state- specifi c 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.

a, b. The samples in Panels A and B are unbalanced panels of eight states (CA, FL, IN, OH, OR, PA, TN, TX) that are uniquely identifi ed among the 16 repeal and eight “never” states before 1977. The other 16 states enter the sample after 1977.

Lee 303

Because 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 speci_fi cation. 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 ex-tensive 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 _fi nd any effect on hourly or weekly earnings in either sample.

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 educa-tional investment, or led marginal youth to drop out of school altogether, thus contrib-uting 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 deregu-lated industries. The results are also in line with those in Skuterud (2005), who _fi nds Sunday shopping deregulation increases employment in retail using data from Canada. On the other hand, Gruber and Hungerman do not _fi nd any effect of blue laws on employment using the National Longitudinal Survey of Youth (GH footnote 17). Simi-larly, Cohen- Zada and Sander (2011) do not _fi nd an impact on overall hours worked using data from the General Social Survey. However, these results are not inconsistent with mine. The samples used in GH and Cohen- Zada and Sander (2011) begin in 1979 and 1973 respectively; likewise, I do not _fi nd any impact on employment using the MORGs sample, which covers a comparable period from 1979 to 2000.

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 _fi nd a strong association between the repeal of blue laws and risky behaviors among church attendees using NLSY data. In particular, they _fi nd that re-pealing blue laws led to an overall 0.015 (standard error = 0.017) increase in the probability that the respondent had six or more drinks in one sitting in past 30 days, 0.032 (standard error =0.013) and 0.022 (standard error =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 due to the exten-sive neuromaturational processes that are occurring during this period (Lubman et al. tive but statistically insignifi cant. 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.

The Journal of Human Resources 304

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 _fi nd that youth who are frequent drinkers complete 2.3 fewer years of education using NLSY data. Chatterji (2003) uses data from the National Education Longitudinal Study in conjunction with state drug poli-cies and eighth grade school characteristics as instruments for drug use during high school. She _fi nds that marijuana use is associated with a reduction in educational at-tainment 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 × 2.3 (drinking) + 0.032 × 0.2 (marijuana) + 0.022 × 0.2 (co-caine), 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. C. Decreased church attendance

A _fi nal channel that I discuss is the impact of lower church attendance on educational attainment. GH _fi nd repealing blue laws led to a signi_fi cant 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 link-ing educational attainment and religiosity, although the direction of causality is

dif-fi cult to determine (Brown and Taylor 2007; Loury 2004). From a theoretical perspec-tive, 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 encour-age 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 frame-work, I perform a series of robustness checks to evaluate the sensitivity of the results on 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.

Lee 305

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 (all cohorts born in a par-ticular decade) at a time. The estimates from both tests (Table 8) remain similar and statistically signi_fi cant 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 attain-ment should not be a source of concern as they operate against the effect of repealing blue laws, that is, 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 (the youngest age at which a child is eli-gible 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 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} mini-mum 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 four years, seven months old. In 1985, Florida changed the law so that a child had to turn _fi ve 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 statewide change in minimum age entry law, or if there were statewide entry laws but no changes, during the sample period. The coef_fi cient 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 coef_fi cient on the Repeal dummy, which is largely unaffected.

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 benefi t educational out-comes because the children are more mentally prepared for the academic rigors in formal schooling (Bedard and Dhuey 2007; Elder and Lubotsky 2007). However, the general fi nding is that the impact of increasing minimum age entry laws lasts up until middle school (as measured by tests scores) but not necessarily through fi nal educational attainment.

19. This specifi cation 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 fi nd a signifi cant impact of the minimum school entry age on educa-tional attainment.

The Journal of Human Resources 306

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 Omitted birth Decade cohort

1930s 1940s 1950s 1960s 1970s

0.104*** –0.0988*** –0.114*** –0.123*** –0.107***

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

Notes: see notes from Table 3. 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 in-clude fi xed effects for year of birth, state of birth, state- specifi c time trends, and Census year. Sample includes the 16 states in Table 1 and the eight states that never had blue laws.

Lee 307

The minimum dropout age has generally increased across states over the last cen-tury, but there have been a few exceptions. Therefore, I run a second speci_fi cation 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 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 coef_fi cient on Repeal is smaller in magnitude but does not lose statistical signi_fi cance. These speci_fi cation 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 af-fects 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 signi_fi cant

Table 9

Robustness Check: Controlling for Minimum Kindergarten Entry Age and Compulsory Schooling

Years of 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

Notes: see notes from Table 3. The omitted category in the regression in Columns 3 and 4 is Dropout Age = 15. All regressions include fi xed effects for year of birth, state of birth, Census year. Sample includes the 16 states in Table 1 and the eight states that never had blue laws.

The Journal of Human Resources 308

decline in years of completed education and high school completion rates. I provide some evidence 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 offer a back- of- the- envelope calculation that indicates risky behaviors such as binge drink-ing and drug use could have been contributdrink-ing 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 em-ployment 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 extra-curricular activities, can positively affect educational outcomes (Borman and Dowling 2006; Lipscomb 2007). Making certain extracurricular activities, such as the right to participate in school sports or earn their driver’s license, contingent on school enroll-ment or academic performance, also have demonstrated potential as strategies for im-proving education outcomes (Barua and Vidal- Fernandez 2012; Vidal- Fernandez 2011).

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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 (all cohorts born in a par-ticular decade) at a time. The estimates from both tests (Table 8) remain similar and statistically signi_fi cant 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 attain-ment should not be a source of concern as they operate against the effect of repealing blue laws, that is, 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 (the youngest age at which a child is eli-gible 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 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}

mini-mum 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 four years, seven months old. In 1985, Florida changed the law so that a child had to turn _fi ve 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 statewide change in minimum age entry law, or if there were statewide entry laws but no changes, during the sample period. The coef_fi cient 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 coef_fi cient on the Repeal dummy, which is largely unaffected. 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 benefi t educational out-comes because the children are more mentally prepared for the academic rigors in formal schooling (Bedard and Dhuey 2007; Elder and Lubotsky 2007). However, the general fi nding is that the impact of increasing minimum age entry laws lasts up until middle school (as measured by tests scores) but not necessarily through fi nal educational attainment.

19. This specifi cation 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 fi nd a signifi cant impact of the minimum school entry age on educa-tional attainment.

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 Omitted birth Decade cohort

1930s 1940s 1950s 1960s 1970s

0.104*** –0.0988*** –0.114*** –0.123*** –0.107***

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

Notes: see notes from Table 3. 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 in-clude fi xed effects for year of birth, state of birth, state- specifi c time trends, and Census year. Sample includes the 16 states in Table 1 and the eight states that never had blue laws.

The minimum dropout age has generally increased across states over the last cen-tury, but there have been a few exceptions. Therefore, I run a second speci_fi cation 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 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 coef_fi cient on Repeal is smaller in magnitude but does not lose statistical signi_fi cance. These speci_fi cation 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 af-fects 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 signi_fi cant Table 9

Robustness Check: Controlling for Minimum Kindergarten Entry Age and Compulsory Schooling

Years of 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

Notes: see notes from Table 3. The omitted category in the regression in Columns 3 and 4 is Dropout Age = 15. All regressions include fi xed effects for year of birth, state of birth, Census year. Sample includes the 16 states in Table 1 and the eight states that never had blue laws.

decline in years of completed education and high school completion rates. I provide some evidence 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 offer a back- of- the- envelope calculation that indicates risky behaviors such as binge drink-ing and drug use could have been contributdrink-ing 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 em-ployment 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 extra-curricular activities, can positively affect educational outcomes (Borman and Dowling 2006; Lipscomb 2007). Making certain extracurricular activities, such as the right to participate in school sports or earn their driver’s license, contingent on school enroll-ment or academic performance, also have demonstrated potential as strategies for im-proving education outcomes (Barua and Vidal- Fernandez 2012; Vidal- Fernandez 2011).

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