ESSAYS IN LABOR ECONOMICS
by
DREW THOMAS MCNICHOLS
A DISSERTATION
Presented to the Department of Economics
and the Graduate School of the University of Oregon
in partial fulfillment of the requirements
for the degree of
Doctor of Philosophy
June 2019
DISSERTATION APPROVAL PAGE
Student: Drew Thomas McNichols
Title: Essays in Labor Economis
This dissertation has been accepted and approved in partial fulfillment of the
requirements for the Doctor of Philosophy degree in the Department of Economics by:
Benjamin Hansen Chair
Michael Kuhn Core Member
Glen Waddell Core Member
Aaron Gullickson Institutional Representative
and
Janet Woodruff-Borden Vice Provost and Dean of the Graduate School
Original approval signatures are on file with the University of Oregon Graduate
School.
Degree awarded June 2019
ii
©c 2019 Drew Thomas McNichols
iii
DISSERTATION ABSTRACT
Drew Thomas McNichols
Doctor of Philosophy
Department of Economics
June 2019
Title: Essays in Labor Economis
This dissertation includes three essays in labor economics.
Youth Employment Opportunities and Crime: Criminal involvement has been
shown to peak at a young age. While Becker’s theory of the rational criminal is
often referenced as a justification for increasing punishments and policing, his
model also suggests that improving labor market options reduces criminality. For
this reason, I estimate the impact of youth labor market opportunities on arrest
rates. I instrument for shocks in local employment demand with national industry
trends using a shift share approach. My estimates suggest that a 1 percent increase
in labor market opportunities leads to a 1.08 percent decrease in arrests for 14-18-
year-olds.
Information and the Persistence of the Gender Wage Gap; Early Evidence
from California’s Salary History Ban: Reductions in wage disparities across race
and gender have stagnated in the recent decades. Recent popular focus on these
inequalities has led to demands for policy interventions to reduce pay gaps. The
most recent legislation intended to improve wage equality prohibits employers from
asking about previously earned salaries. The intent of this legislation is to redress
iv
persistent pay inequalities. Salary history bans (SHBs) have been implemented in
varying degrees (public and private) in multiple cities and states. I use a synthetic
control approach to measure the impact of a statewide SHB in California. After the
passing of a statewide SHB, statewide female-male earnings ratios increased from
0.77 (where they have been stagnant for the last 12 years) to 0.81. Moreover, I
find these results are driven by an increase of the earnings ratio in male-dominated
industries.
Marijuana Legalization and Violent Crime: Marijuana legalization has spread
rapidly across the United States. Recently, after decades of decreases, violent crime
rates have rebounded slightly in the United States. We test whether marijuana
legalization has contributed to increased violence using a synthetic control design
approach using the first two recreational marijuana adopters: Colorado and
Washington. Using data from the Supplemental Homicide Reports and Uniform
Crime and Reports, we largely find evidence that crime trends closely follow those
predicted by synthetic control methods.
This dissertation includes previously unpublished co-authored material.
v
CURRICULUM VITAE
NAME OF AUTHOR: Drew Thomas McNichols
GRADUATE AND UNDERGRADUATE SCHOOLS ATTENDED:
University of Oregon, Eugene, OR
Oklahoma City University, Oklahoma City, OK
DEGREES AWARDED:
Doctor of Philosophy, Economics, 2019, University of Oregon
Master of Science, Economics, 2015, University of Oregon
Bachelor of Science, Mathematics, 2012, Oklahoma City University
Bachelor of Science, Economics, 2012, Oklahoma City University
AREAS OF SPECIAL INTEREST:
Labor Economics
Applied Mircoeconomics
Econometrics
GRANTS, AWARDS AND HONORS:
Research Kleinsorge Fellowship Award, University of Oregon, 2018
First Year Kleinsorge Fellowship Award, University of Oregon, 2014
vi
ACKNOWLEDGEMENTS
I thank my advisor, family, and friends for all the support along the way.
vii
TABLE OF CONTENTS
Chapter Page
I. YOUTH EMPLOYMENT OPPORTUNITIES AND CRIME . . . . . . 1
Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1
Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 2
Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5
Methodology and Estimation . . . . . . . . . . . . . . . . . . . . . 7
Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18
Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 30
II. INFORMATION AND THE PERSISTENCE OF THE
GENDER WAGE GAP; EARLY EVIDENCE FROM
CALIFORNIA’S SALARY HISTORY BAN . . . . . . . . . . . . . . . 33
Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33
Background on SHBs . . . . . . . . . . . . . . . . . . . . . . . . . 36
Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 38
Methodolgy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 39
Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 44
Conculsion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 90
viii
Chapter Page
III. MARIJUANA LEGALIZATION AND VIOLENT CRIME . . . . . . . 92
Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92
Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 95
Data and Methods . . . . . . . . . . . . . . . . . . . . . . . . . . . 97
Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 101
Conclusions and Policy Implications . . . . . . . . . . . . . . . . . 129
REFERENCES CITED . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 134
ix
LIST OF FIGURES
Figure Page
1. Employment Trends . . . . . . . . . . . . . . . . . . . . . . . . . . . . 8
2. Arrest Trends . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 9
3. Industry Composition by State . . . . . . . . . . . . . . . . . . . . . . 12
4. Instrument Relevance . . . . . . . . . . . . . . . . . . . . . . . . . . . . 13
5. Instrument Relevance After Year 2000 . . . . . . . . . . . . . . . . . . 14
6. Instrument Compared to Actual . . . . . . . . . . . . . . . . . . . . . . 15
7. Female to Male Median Earnings Ratio of Full-Time Workers . . . . . 33
8. California Cross Validation . . . . . . . . . . . . . . . . . . . . . . . . . 43
9. Composition of Synthetic California . . . . . . . . . . . . . . . . . . . . 44
10. California Female to Male Earnings Ratio . . . . . . . . . . . . . . . . 47
11. Average Weekly Earnings by Gender . . . . . . . . . . . . . . . . . . . 50
12. Average Weekly Hours Worked by Gender . . . . . . . . . . . . . . . . 52
13. Average Weekly Hourly Wage by Gender . . . . . . . . . . . . . . . . . 53
14. Average Weekly Earnings Ratio by Industry Type . . . . . . . . . . . . 56
15. Actual California - Synthetic California vs Placebo States by
Industry Type . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 57
16. Average Weekly Earnings by Gender Within Female
Dominated Industries . . . . . . . . . . . . . . . . . . . . . . . . . . . . 59
17. Average Weekly Earnings by Gender Within Male
Dominated Industries . . . . . . . . . . . . . . . . . . . . . . . . . . . . 61
18. Average Weekly Hours Worked by Gender Within Female
Dominated Industries . . . . . . . . . . . . . . . . . . . . . . . . . . . . 62
19. Average Weekly Hours Worked by Gender Within Male
Dominated Industries . . . . . . . . . . . . . . . . . . . . . . . . . . . . 64
x
Figure Page
20. Average Hourly Wage by Gender Within Female
Dominated Industries . . . . . . . . . . . . . . . . . . . . . . . . . . . . 65
21. Average Hourly Wage by Gender Within Male
Dominated Industries . . . . . . . . . . . . . . . . . . . . . . . . . . . . 67
22. Average Weekly Earnings Ratio by Industry Type . . . . . . . . . . . . 69
23. Actual California - Synthetic California vs Placebo States by
Industry Type . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 70
24. Average Weekly Earnings Ratio by Age . . . . . . . . . . . . . . . . . . 71
25. Actual California - Synthetic California vs Placebo States by Age . . . 72
26. Average Weekly Earnings by Gender Among Individuals Below Age 35 74
27. Average Weekly Earnings by Gender Among Individuals Above Age 35 75
28. Average Weekly Hours Worked by Gender Among Individuals Below 35 77
29. Average Weekly Hours Worked by Gender Among Individuals Above 35 78
30. Average Hourly Wage by Gender Among Individuals Below 35 . . . . . 80
31. Average Hourly Wage by Gender Among Individuals Above Age 35 . . 81
32. Employment Probabilities by Sex . . . . . . . . . . . . . . . . . . . . . 83
33. Actual California - Synthetic California vs Placebo States by Sex . . . 84
34. Sensitivity Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 89
35. Marijuana Laws by State . . . . . . . . . . . . . . . . . . . . . . . . . . 96
36. Reported Murders per 100,000 by State . . . . . . . . . . . . . . . . . . 98
37. Reported Murders per 100,000 by State, Demeaned . . . . . . . . . . . 98
38. Reported Homicides per 100,000 by State, Demeaned . . . . . . . . . . 99
39. Reported Gun Homicides per 100,000 by State, Demeaned . . . . . . . 99
40. Reported Gang Homicides per 100,000 by State, Demeaned . . . . . . . 99
41. Colorado Synthetic Control for Murder (UCR) Reported, Demeaned . . 103
42. Washington Synthetic Control for Murder (UCR) Reported, Demeaned 105
xi
Figure Page
43. Colorado Synthetic Control for Homicide Reported, Demeaned . . . . . 107
44. Washington Synthetic Control for Homicide Reported, Demeaned . . . 109
45. Colorado Synthetic Control for Drug Related Homicide Reported,
Demeaned . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 110
46. Washington Synthetic Control for Drug Related Homicide Reported,
Demeaned . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 112
47. Colorado Synthetic Control for Gang Related Homicide Reported,
Demeaned . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 114
48. Washington Synthetic Control for Gang Related Homicide Reported,
Demeaned . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 115
49. Colorado Synthetic Control for Gun Homicide Reported, Demeaned . . 117
50. Washington Synthetic control for Gun Homicide Reported, Demeaned . 118
51. Colorado Synthetic Control for Non-gun Homicide Reported,
Demeaned . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 120
52. Washington Synthetic Control for Non-gun Homicide Reported,
Demeaned . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122
53. Colorado Synthetic Control for Homicide with
Known Offender Reported, Demeaned . . . . . . . . . . . . . . . . . . 123
54. Washington Synthetic Control for Homicide with
Known Offender Reported, Demeaned . . . . . . . . . . . . . . . . . . 125
55. Colorado Synthetic Control for Homicide with
Unknown Offender Reported, Demeaned . . . . . . . . . . . . . . . . . 126
56. Washington Synthetic Control for Homicide with
Unknown Offender Reported, Demeaned . . . . . . . . . . . . . . . . . 128
xii
LIST OF TABLES
Table Page
1. Actual Employment Growth Predicted by
Estimated Employment Growth . . . . . . . . . . . . . . . . . . . . . . 17
2. Effects of Employment Opportunities on Crime . . . . . . . . . . . . . 19
3. Effect Size of 100 New Employment Opportunities on Arrests . . . . . 20
4. Juvenile Crime by Race . . . . . . . . . . . . . . . . . . . . . . . . . . 22
5. Grouping of Offenses . . . . . . . . . . . . . . . . . . . . . . . . . . . . 24
6. Effects of Employment Opportunities on Crime by
Offense Group and Age . . . . . . . . . . . . . . . . . . . . . . . . . . . 25
7. The Effect of Employment Opportunities on Arrests by Offense for 14-18
Year Olds . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 27
8. The Effect of Employment Opportunities on Arrests by Offense for 19-21
Year Olds . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28
9. The Effect of Employment Opportunities on Arrests by Offense for 14-21
Year Olds . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 29
10. Salary History Ban Laws by Date and Region . . . . . . . . . . . . . . 37
11. Cross Validation Weights . . . . . . . . . . . . . . . . . . . . . . . . . . 45
12. Change in Average Weekly Female to Male Earnings Ratio . . . . . . . 48
13. Change in Average Weekly Earnings and Hours Worked . . . . . . . . 49
14. Change in Hourly Wage by Sex and Industry . . . . . . . . . . . . . . . 54
15. Change in Employment Probability by Sex and Industry . . . . . . . . 83
16. Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87
17. Robustness Using CPS Replicate Weights . . . . . . . . . . . . . . . . 88
18. Syntheic Control Results for Marijuana Legalization . . . . . . . . . . . 102
19. Differences in Differences Results for Marijuana Legalization . . . . . . 130
xiii
Table Page
20. Differences in Differences Results for Marijuana Legalization
Partial Treatment . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 131
xiv
CHAPTER I
YOUTH EMPLOYMENT OPPORTUNITIES AND CRIME
Introduction
The age profile of criminal activity peaks in late teenage years, then falls
(Hirschi and Gottfredson, 1983; Steffensmeier and Ulmer, 2008). Decreasing
juvenile criminal participation is therefore an important public policy objective.
While criminal sentences are more severe for young adults than juveniles, criminal
participation has been shown to drop only slightly across this age threshold due to
harsher punishments (Lee and McCrary, 2005; McCrary and Lee, 2009). Juvenile
incarceration has been shown to reduce the likelihood of high school completion
and increase the likelihood of adult incarceration (Aizer and Doyle, 2015). This
evidence suggests that the “stick” may not be the most effective tool for reducing
crime, and may actually increase future crime. Becker’s model suggests the “carrot”
may also reduce incentives to engage in criminal behaviors by increasing the payoff
to non-crime activities. This makes the steady decline in youth employment over
the last few decades particularly concerning (Mixon Jr. and Stephenson, 2016).
The employment-population ratio for 16-19-year-olds is at an all-time low and is
expected to be even lower by 2024 (Morisi, 2017). Employment may be becoming
more difficult for youth to attain (Goodman, 2008). According to Becker’s model,
Decreased opportunities in the labor market could increase the incentive to
participate in the criminal market. This paper tests this potential mechanism for
youth. Specifically, I look at the effects of changes in labor market opportunities on
juvenile and young adult arrests.
1
Theoretically, whether youth employment results in more or less crime is
unclear. First, I discuss the possible mechanisms through which employment could
reduce crime, then I offer some ways in which employment could cause crime.
Time spent working could simply incapacitate individuals from committing crime.
Additionally, if youth are concerned about losing their job if caught committing
crime, there might be a deterrence effect of employment on crime. On the other
hand, employment could stimulate crime if the workplace represents the first time
individuals come in contact with a cash register or if new employees learn illegal
activities from existing employees or customers. The average juvenile does not have
a job, which means working youth receive greater income than do their non-working
peers. Additional income could be a catalyst for juvenile delinquency. Particularly,
this income could be used to purchase alcohol, which has a well-established positive
relationship with crime (Carpenter, 2005, 2007; Carpenter and Dobkin, 2015).
The paper proceeds as follows: Section 2.2 provides background on SHB
policies. Section 3.3 describes the data. Section 2.4 presents my empirical
methodology. Section 3.4 describes my results. Section 2.6 discusses and concludes.
Background
Since Becker’s (1968) introduction of the theory of the rational criminal,
economists have been testing the model’s predictions empirically. The empirical
literature that has developed can broadly be split into two categories, one of
which tests the responsiveness of crime to changes in punishments or policing
(the stick) (Levitt, 1995; Chiras and Crea, 2004; Evans and Owens, 2007; Corman
and Mocan, 2005; Kessler and Levitt, 1999), and the other of which tests the
responsiveness of crime to local labor market conditions (the carrot). Research
2
analyzing the response of crime to labor market opportunities utilizes two distinct
methods of measuring the opportunity cost of crime. One method looks at the
responsiveness of crime to unemployment; the other looks at the responsiveness
of crime to changes in wages. Wages are thought to be the legal opportunity cost
of committing crime, while unemployment is a proxy for the opportunity cost
of crime. Unemployment generates incentives to participate in criminal activity
through the consumption smoothing motive. Additionally, being unemployed could
trigger frustration and anger, which subsequently leads to violent behavior (Agnew,
1992).
In the empirical research examining the relationship between unemployment
and crime, most studies find small positive effects for property crime and no
effect for violent crime (Raphael and Rudolf, 2001; Fougere et al., 2009; Lin,
2008; Gronqvist, 2013). These empirical estimates are small and sensitive to the
population and time period being studied, despite the clear theoretical predictions
(Chalfin and McCrary, 2017).
In the body of research analyzing the effects of wages on crime, the effects are
much larger and robust (Grogger, 1998; Doyle et al., 1999; Machin and Meghir,
2004). Within the wage literature, some studies consider only changes in the
minimum wage and its effect on crime (Corman and Mocan, 2005; Hansen and
Machin, 2002; Fernandez and Pepper, 2014). Most of these studies find a strong
negative relationship between minimum wages and crime. Gould et al. (2002) span
the two literatures by looking at wages and unemployment contemporaneously.
They find higher wages and lower unemployment reduce property crime for male
youths.
3
Employment measures like wages and unemployment are equilibrium
observations, which means they occur at the intersection of labor supply and
labor demand. Using these observed labor equilibria as an explanation for changes
in crime confounds whether changes in crime that are attributed to changes in
employment conditions are driven by shocks to labor supply or labor demand;
a crucial question from a policy perspective. To disentangle the effect of shifts
in demand, one can use use demand shifting events that affect only the demand
side of the economy or an instrumental variable that is highly correlated with the
employment measure but is only driven by shifts from the demand side of the
economy. I create an instrument for shocks in labor demand, following the shift
share method first used by Bartik (1991) and later by Katz and Murphy (1992);
Blanchard et al. (1992). I construct estimated quarterly employment demand at the
state level. I use predicted changes in employment demand to explain changes in
crime. The panel analysis is similar to approaches used in research on employment
conditions and crime. These studies often consider the level of unemployment,
which is the number of people who are looking for a job but remain jobless. I
exploit predicted changes in employment demand, which measures predicted
changes in labor market opportunities, to isolate a causal impact on arrests.
Existing research considering youth employment opportunities and crime
utilizes concentrated populations, for example Heller (2014) finds that teen
employment does reduce crime in a randomized control trial among disadvantaged
youth in Chicago. Gelber et al. (2014) find aligned results looking at summer
employment lotteries in New York City. The job corps has also been show to be
an effective way to decrease crime, though at a negative net benefit due to the cost
of the program (Schochet et al., 2008). This paper analyzes systematic changes in
4
employment opportunities for the entire U.S. population of employed youth over a
14-year time period.
Data
I use the Federal Bureau of Investigation’s Uniform Criminal Reporting
(UCR) monthly files, which report the number of men and women arrested by age,
type of offense1, and agency at the monthly level from 2000-20122. Arrest data has
both its benefits and drawbacks. Arrests may not be the best measure of criminal
activity, because not all crime that occurs results in an arrest. Arrests are also
highly dependent on the level of policing. However, Cook et al. (2014) suggest they
provide a reasonably accurate measure of criminal activity. An advantage to using
arrests instead of reports is that arrests, unlike reports, generate individual-specific
information like sex, age, and race.
The UCR arrest files are voluntarily reported at the agency level. While these
agencies voluntarily report crime data through the UCR program or directly to the
FBI, between 88 and 96 percent of the U.S. population is covered by agencies that
do report to the UCR (Maltz, 1999). Proper use of these data requires thorough
cleaning. To ensure the arrest observations are as clean as possible, I plot agencies’
shares of state arrests over time. This allows me to see how much each agency
contributes to total state arrests for each time period. I drop agencies that have
erratic reporting patterns, agencies that report only in month 12 of a year, and
1There are 29 offense categories and14 sub offense categories; this results in 43 offense
classifications.
2These data are available for download from the NACJD.
5
agencies that drop out of voluntary reporting during the sample.3 Arrest counts are
aggregated to the quarterly level to match the employment data.
Quarterly Workforce Indicator (QWI) data are used for quarterly employment
totals by state, industry4, and age group. Stable counts of employment, which
are measured as jobs that are held for the duration of the quarter, are my key
employment variable. The QWI job counts are aggregated from employment data
reported by firms to each state’s Unemployment Insurance wage reporting system5.
The Longitudinal Employer Household Dynamics (LEHD) program creates a
longitudinal employment and earnings database with demographic characteristics
by matching records from state unemployment insurance programs to Census
Bureau data. These data are aggregated to the quarterly level to create the QWI.
Population data come from The National Cancer Institute’s Surveillance,
Epidemiology, and End Results Program (SEER). I obtain population estimates
by state, age, sex, and year for the duration of my panel. The SEER data are a
modification of the intercensal and vintage 2015 annual estimates produced by the
US Census Bureau’s Population Estimates Program. I aggregate these data to the
3I drop the following agencies from their respective states: Hoover and Mobile from Alabama;
Arvada, Grand Junction and Greeley from Colorado; Boston from Massachusetts; Apple Valley,
Eagan, Minneapolis, and St Paul from Minnesota; Nassau, and New York from New York;
Columbus, Lima and Toledo from Ohio; and Seattle from Washington. Additionally, I drop
Rhode Island before 2005, and Wisconsin before 2003. Washington DC and Illinois are dropped
completely. These agencies are all dropped due to inconsistent reporting.
4The 20 industry categories include: (1) Agriculture, Forestry, Fishing and Hunting;
(2) Mining, Quarrying, and Oil and Gas Extraction; (3) Utilities; (4) Construction; (5)
Manufacturing; (6) Wholesale Trad; (7) Retail Trade; (8) Transportation and Warehousing;
(9) Information; (10) Finance and Insurance; (11) Real Estate and Rental and Leasing; (12)
Professional, Scientific, and Technical Services; (13) Management of Companies and Enterprises;
(14) Administrative and Support and Waste Management and Remediation Services; (15)
Educational Services; (16) Health Care and Social Assistance; (17) Arts, Entertainment,
and Recreation; (18) Accommodation and Food Services; (19) Other Services (except Public
Administration); (20) Public Administration.
5Consequently, these data do not include informal employment opportunities, which may be of
importance for youth and young adults.
6
state level and group them by sex and age so they can be merged with the UCR
and QWI data.
The number of sworn officers employed in each state-year is obtained from the
UCR Law Enforcement Officer Killed in Action (LEOKA) files. Police employees
are used as a proxy for the amount of policing in a particular state. My final
sample consists of quarterly observations of arrests and employment for 46 states
from 1998 to 2012 with two age-bins (14-18 and 19-21), and sex identifiers.
Figure 1 shows national employment levels and the corresponding growth rate
for each age group and sex at the quarterly level for the duration of my sample.
Figure 2 shows national arrest levels and the corresponding growth rate for each
age group and sex at the quarterly level for the duration of my sample. Both
arrests and employment are highly seasonal. Females are employed at slightly
higher rates than males, but males dominate arrest counts for all age groups.
Generally, employment growth is strong in the late ’90s, flattens out from 2000
to late 2008, then decreases in 2008. These trends are not surprising as these data
capture the transition from the dot-com boom to the great recession. Arrests follow
a similar pattern, albeit with smaller magnitudes of growth and decline.
Methodology and Estimation
I create an estimate of predicted employment growth to determine how
changes in the number of arrests can be explained by predicted changes in the
employment level. Predicted employment growth is calculated by predicting the
level of employment in the next time period, then calculating the growth rate
from the actual level of employment in previous time periods. The next period’s
7
FIGURE 1.
Employment Trends
(a) (b)
(c) (d)
(e) (f)
8
FIGURE 2.
Arrest Trends
(a) (b)
(c) (d)
(e) (f)
9
employment for each state L̂st is calculated as follows:
∑[( ) ]US Emp in Ind i at time t
L̂st = × (State s Emp in Ind i at t− 1)
US Emp in Ind i at time t− 1
i
Where s indexes states and t indexes time by quarter. The predicted employment
level for the next quarter relies on national industry-specific growth rates and state-
industry composition. Predicted employment growth is then
L̂st − Ls,t−1
ĝst = ,
Ls,t−1
which can be written as
∑︷(
G︸︸it )︷  Lit − Li,t−1 Lsi,t− 1
i L − i,t 1 ∑
iGitLsi,t−1ĝst = = . (1)
Ls,t−1 Ls,t−1
This allows us to see how the national industry-specific growth Git interacts
with the state-level industry composition to create predicted employment growth.
Each state’s specific industry sector is predicted to grow at the national rate.
Blanchard et al. (1992) note that this predicted employment growth is a valid
instrument if industry national growth rates are uncorrelated with state-level
labor-supply shocks. This is true if there is no industry for which employment is
concentrated in any state and there is sufficient variation in state-level industry
composition. Figure 3 shows average industry shares for all 46 states for each
age-sex group in my sample. Each bar represents a state’s average industry
composition over the 14-year period. Each column has 46 horizontal bars; each
bar represents the share of total state employment in that particular industry. Each
10
color represents a state; the shares across all industries for each state add to one.
The retail sector and food-service sector dominate most states for youth and vary
more than 20% in share of employment across states. Additionally, the maximum
sector share is less than 50% for any particular state.
Figure 4 plots actual growth against instrumented growth for each state-
quarter in the sample for each age-sex group, weighted by population. Actual
growth plotted on the vertical axis is an equilibrium outcome, the change in
employment due to changes in supply and demand. Estimated growth on the
horizontal axis is growth due only to estimated changes on the demand side of
the labor market. The slope coefficient from the regression of estimated growth
on actual growth is reported near the bottom of each plot in Figure 4.
Generally, the clusters of large estimated growth in the right of the plots is
made up of observations from 1998-2000, when both employment and arrests were
increasing. Years before 2001 are excluded in Figure 5, and the slope coefficient
from the regression of actual growth on estimated growth is around one for all age
groups and sexes. From 2001 onward, estimated growth is an excellent predictor
of actual growth. This is less true from 1998-2000, which may be due to the
instrument’s variance in high-growth periods. Figure 6 plots actual growth and
estimated growth for every state over time side-by-side for each sex-age group.
Figure 6 illustrates how each state’s instrumented growth is similar to the national
growth trend but different due to state-specific industry composition.
Table 1 reports regression results from estimated growth regressed on actual
growth across various fixed-effect specifications. Columns 2-5 incrementally add
time and location fixed effects. The exogeneity of the instrument requires industry
national growth rates to be uncorrelated with state-level labor-supply shocks.
11
FIGURE 3.
Industry Composition by State
(a) (b)
(c) (d)
(e) (f)
Notes: This figure illustrates the variation of industry composition across states. Each bar represents a state’s industry-share of total
employment. Each column has 46 bars, one representing each state in the sample.
12
FIGURE 4.
Instrument Relevance
(a) (b)
(c) (d)
Notes: This figure plots estimated employment growth due to demand shocks against actual state employment growth from
1998-2012. Each observation is a state-quarter. Observations weighted by population.
13
FIGURE 5.
Instrument Relevance After Year 2000
(a) (b)
(c) (d)
(f)
(e)
Notes: This figure plots estimated employment growth due to demand shocks against actual state employment growth from
2001-2012. Each observation is a state-quarter. Observations weighted by population.
14
FIGURE 6.
Instrument Compared to Actual
(a)
(b) (c)
(d) (e)
Notes: This figure plots actual employment growth on the right and estimated employment growth on the left. Estimated growth is
driven by national industry specific growth but varies across state due state specific industry composition.
15
This may not be the case if a particular state is driving the national shock. To
address this concern, I calculate the instrument for each state, while leaving out
its own contribution to national employment growth. The formula to calculate
the leave-own-out predicted employment growth loˆogst is below in equation (2),
where gsit is state-specific industry employment growth. Column 6 reports the same
specification as column 5 using the leave-own-out predicted employment growth
specification for predicted employment growth.
∑
[Git − gsit]Lsi,t−1
loˆog = ist (2)Ls,t−1
The construction of a valid instrument for predicting employment growth
allows me to employ a simple empirical strategy. I use ordinary least squares
linear regression to analyze the effect of the instrument directly on my dependent
variable. I am estimating the reduced-form effect of estimated employment growth
on arrests, instead of a typical two-stage instrumental variables approach.
My estimating equation is a linear regression with time and location fixed
effects as follows:
%∆arrestssayq = α + βĝsayq + δPolicesy + φy + ωq + γs + sayq,
where %∆arrests is calculated as Arrestst−Arrestst−1 for each state and age-sex group
Arrestst−1
from quarter to quarter. Indices sayq index state, age-sex6, year, and quarter
for each observation. Estimated growth ĝsayq is constructed from employment
data according to equation (1). Policesy is the count of payroll officers in a given
6Age-sex categories include male, female, and all sexes for ages 14-18, 19-21, and 14-21.
16
TABLE 1.
Actual Employment Growth Predicted by
Estimated Employment Growth
(1) (2) (3) (4) (5)
Male 0.826*** 0.346*** 0.227*** 0.353*** 0.242***
(0.015) (0.033) (0.032) (0.036) (0.035)
Female 0.910*** 0.427*** 0.289*** 0.438*** 0.308***
14-18
(0.011) (0.034) (0.033) (0.037) (0.036)
All Sexes 0.875*** 0.383*** 0.261*** 0.392*** 0.278***
(0.013) (0.033) (0.031) (0.036) (0.034)
Male 0.278*** 0.137*** 0.086*** 0.142*** 0.090***
(0.016) (0.023) (0.021) (0.026) (0.024)
Female 0.534*** 0.122*** 0.076*** 0.130*** 0.083***
19-21
(0.013) (0.02) (0.019) (0.022) (0.021)
All Sexes 0.403*** 0.116*** 0.073*** 0.123*** 0.078***
(0.014) (0.02) (0.019) (0.023) (0.021)
Male 0.482*** 0.152*** 0.095*** 0.158*** 0.102***
(0.017) (0.025) (0.024) (0.028) (0.026)
Female 0.714*** 0.147*** 0.082*** 0.157*** 0.092***
14-21
(0.012) (0.024) (0.022) (0.026) (0.025)
All Sexes 0.612*** 0.139*** 0.082*** 0.148*** 0.091***
(0.014) (0.024) (0.022) (0.026) (0.024)
State FE n y y y y
Year FE n y y y y
Quarter FE n y y y y
State×year FE n n n y y
Leave-out-own Growth n n y n y
This table reports estimates for the percentage change in total arrests due to a one percent increase in youth employment
opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1. Standard Errors are reported in Parenthesis.
Errors are clustered at the state level. Regressions are weighted by annual state population for a particular age-sex group.
Columns (3) and (5) calculate predicted growth using national growth that was calculated for each leaving out own state
contribution to national growth.
state-year. Year fixed effects φy are included to capture broader economic trends
that may be simultaneously affecting employment levels and arrests across all
states. Seasonal variation is controlled for with quarter fixed effects ωq. Systematic
17
differences in states that are constant across time are controlled for with state fixed
effects γs. Finally, sayq is the error term.
Identifying variation comes from changes in arrest levels within a state,
quarter, and year for a particular sex-age group. Estimated standard errors are
clustered at the state level. Regressions are weighted by the age-sex population
in a given state-year. The coefficient of interest is β, which is interpreted as the
percentage change in arrests due a one percent increase in estimated employment
growth. My identifying assumption is that the predicted measure of employment
growth is conditionally uncorrelated with the unobservable component of change in
arrests.
Results
Table 2 reports regression results across various specifications. Column 1
reports estimates for estimated growth regressed on change in arrests. Column
2 adds state, year, and quarter fixed effects. Column 4 adds state-by-year fixed
effects. Columns 3 and 5 are similar specifications to 2 and 4, but are estimated
using leave-own-out growth as in equation (2). Robustness across these columns
rules out the concern that states are driving their own employment shocks via the
national growth rate. Table 3 reports the same specification as column 2, including
average arrest levels and average employment levels. These averages are combined
with the elasticities to calculate the estimated effect size. Effect size is interpreted
as the change in arrests caused by 100 new jobs for the age-sex group for a given
state-quarter.
I find increased employment opportunities lead to decreased arrests. 14-18
year old males are most responsive to increases in job opportunities. Young adults
18
TABLE 2.
Effects of Employment Opportunities on Crime
Specification Analysis
%∆arrestssayq = α + βĝsayq + δPolicesy + φy + ωq + γs + sayq
Age Sex (1) (2) (3) (4) (5)
Male -0.348* -1.056*** -0.992*** -1.063*** -0.980***
(0.206) (0.337) (0.31) (0.393) (0.348)
Female 0.323 -0.985*** -0.921** -0.980** -0.890**
14-18
(0.202) (0.382) (0.358) (0.439) (0.389)
All Sexes -0.064 -1.081*** -1.005*** -1.085*** -0.988***
(0.221) (0.36) (0.332) (0.416) (0.367)
Male -0.724*** -0.296** -0.286** -0.312* -0.282*
(0.196) (0.135) (0.13) (0.173) (0.147)
Female -1.103*** -0.260 -0.238 -0.276 -0.233
19-21
(0.176) (0.175) (0.168) (0.217) (0.192)
All Sexes -1.030*** -0.270* -0.253* -0.285 -0.249
(0.2) (0.149) (0.145) (0.189) (0.164)
Male -0.716*** -0.684*** -0.624*** -0.697** -0.615**
(0.245) (0.232) (0.214) (0.282) (0.242)
Female -0.187 -0.573** -0.509* -0.581* -0.491*
14-21
(0.219) (0.288) (0.27) (0.343) (0.298)
All Sexes -0.564** -0.663*** -0.593** -0.674** -0.580**
(0.242) (0.255) (0.237) (0.306) (0.265)
State FE n y y y y
Year FE n y y y y
Quarter FE n y y y y
State×year FE n n n y y
Leave-out-own Growth n n y n y
This table reports estimates for the percentage change in total arrests due to a one percent increase in youth employment
opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1. Standard Errors are reported in Parenthesis.
Errors are clustered at the state level. Regressions are weighted by annual state population for a particular age-sex group.
Columns (3) and (5) calculate predicted growth using national growth that was calculated for each leaving out own state
contribution to national growth.
19
TABLE 3.
Effect Size of 100 New Employment Opportunities on Arrests
Age Sex β R2 Crime Emp Effect Size
Male -1.055*** 0.089 9924 22646 -46.4
(0.336)
Female -0.985*** 0.163 3442 25857 -13.1
14-18
(0.382)
All Sexes -1.081*** 0.107 13366 48503 -29.8
(0.36)
Male -0.298** 0.201 8254 42817 -5.7
(0.136)
Female -0.261 0.192 2181 46755 -1.2
19-21
(0.139)
All Sexes -0.270* 0.204 10435 89572 -3.1
(0.15)
Male -0.685*** 0.106 18178 65463 -19
(0.233)
Female -0.574** 0.121 10435 72612 -4.4
14-21
(0.289)
All Sexes -0.664*** 0.107 23801 138075 -11.4
(0.256)
This table reports estimates for the percentage change in total arrests due to a one percent increase in
youth employment opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1. Standard Errors are reported in Parenthesis.
Errors are clustered at the state level. Regressions are weighted by annual state population for a particular
age-sex group.
Effect size is the change in arrests due to 100 new job opportunities at the state-quarter level.
are much less responsive. For male youth the coefficient of -1.055 is interpreted as
the percentage change in arrests at the state level for a given quarter due to a one
percent increase in employment opportunities. This translates to 46 fewer youth
arrests due to 100 new employment opportunities for 14-18 year old males in a
particular state-quarter. Young adults see 0.298 percent fewer arrests due to a one
percent increase in employment opportunities. Females are slightly less responsive,
20
but have a much smaller effect size. This is consistent with the fact that females
engage in much less criminal activity than males. These estimates are generated
using arrest data, which is a lower bound estimate of criminal activity since all
crime is not reported as an arrest. The reduction in criminal activity not resulting
in arrest could be much larger.
These results are similar in direction but larger in magnitude than those of
Heller and Gelber, who look at participation in different summer employment
opportunities. Heller finds a 43-percent reduction in violent crime arrests per
youth for disadvantaged youth who were randomly offered summer employment
opportunities through Chicago public schools. Gelber finds participation in New
York City’s Summer Youth Employment Program reduced the probability of
incarceration by 0.10 percentage points. Both of these studies examine only
disadvantaged populations and summer employment. Of the disadvantaged youth,
96 percent are black in Heller’s study, and 48 percent are black in Gelber’s. Neither
study uses a nationally representative sample.
I analyze the differential effect by race for juveniles in Table 4. I use arrest
counts by race as the dependent variable across 4 categories: White, Black, Asian,
and Native American. I report estimates only for males and females combined,
since arrests by race are not recorded by sex. The elasticities vary only slightly
across white and black. The difference in effect size, however, is quite large. The
effect size of 5.4 fewer arrests for blacks due to 100 new employment opportunities
at the state level is comparable to Heller’s findings, which translate to 4 fewer
arrests if 100 disadvantaged youth (96 percent of which are black) are given
summer employment opportunities. While blacks are responding proportionally
similarly to whites, whites make up a much larger fraction of the population; thus,
21
including whites explains the difference in magnitudes seen between my results
and those of previous studies. Asians and Native Americans have more than twice
the response of whites and black, but due to their relatively low level of criminal
activity, their effect sizes are small relative to other races. An important note is
that I am allowing only the dependent variable to differ by race; I do not have
employment data by race. These results, therefore, do not capture the fact that job
opportunities are likely not equally distributed across races. In fact, my results are
consistent with differential job opportunities across races. One possible explanation
that whites see a larger reduction in crime due to predicted job opportunities is
that whites are filling proportionally more of the potential job opportunities, which
means that more whites are removed from the criminal labor market.
TABLE 4.
Juvenile Crime by Race
Race β Emp Crime Effect Size
White -1.283*** 45,627 6531 -19.2
(0.404)
Black -0.926* 48,523 2852 -5.4
(0.419)
Asian -2.142*** 51,166 160 -0.7
(0.419)
Native American -2.433* 48,503 131 -0.7
(1.258)
All -1.081 48,503 13366 -29.8
(0.36)
This table reports estimates for the percentage change in arrests (by race) due to a one percent
increase in youth employment opportunities.
Only arrests are categorized by race, employment opportunities is not.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1. Standard Errors are reported in
Parenthesis.
Errors are clustered at the state level. Regressions are weighted by annual state population for
a particular age-sex group.
Effect size is the change in arrests due to 100 new job opportunities at the state-quarter level.
22
To further investigate the mechanisms driving the results in Tables 2 and
3, I categorize arrests by offense type. Arrests are recorded in 29 offense groups
and 14 subgroups, which makes 43 categories and subcategories. I group these
categories into non-mutually exclusive groups by offense type in Table 57. Group
1 is violent crimes; group 2 is financially motivated crimes; group 3 is mischief type
crimes; group 4 is personal offenses; group 5 is drug related crimes; and group 6
is substance abuse crimes. The incentives to commit offenses in different groups
vary substantially. Violent crimes are personal offenses often triggered by anger and
other emotional responses. Financially motivated crimes are categorized as crime
that could be an arguable substitute for income. Mischief crimes are crimes that
youth “up to no good” may commit. These crimes seem to be driven by boredom,
so the incapacitation of employment is expected to play a role in decreasing these
crimes. Personal offenses are sex crimes or family crimes. Drug-related crimes are
any arrests dealing with drug sale or drug possession. Finally, substance-abuse
crimes are alcohol-related crimes or drug-possession crimes.
The regression results for each of these groups by age-sex group are presented
in Table 6. I adjust significance levels for multiple hypothesis testing using the
Benjamini-Hochberg step-up method (Benjamini and Hochberg, 1995). Table 6
identifies which grouping of crimes are driving the aggregate results in Tables 2 and
3. All types of crimes for all sex-age groups still seem to be decreasing in predicted
employment opportunities. For male youth, all groups except drug-related crimes
are estimated to decrease as employment opportunities are expected to increase.
Female youth are much less responsive, as only three groups have coefficients
7The total number offenses listed in table 5 is less than 43 because some sub-categories are
omitted to prevent double-counting. For instance, drug sale and drug possession aggregate to
equal drug offenses.
23
TABLE 5.
Grouping of Offenses
Violent Crimes Financially Motivated Mischief Personal Offenses
Murder Larceny Vandalism Sex Offense
Manslaughter Motor Theft Arson Family Offense
Rape Forgery Disorderly
Aggravated Assault Fraud Vagrancy Drug-related
Weapon Embezzlement Suspicion
Other Assault Stolen Property Curfew Drug
Prostitution Runaway
Gambling Substance Abuse
Robbery
Burglary DUI
Drug Sale Liquor Laws
Drunkenness
Drug Possession
These groupings are not mutually exclusive. Drug includes several categories for sale and possession. Drug sale is included in
financially motivated offenses while drug possession is included in substance abuse. Both categories are included in drug-related
offenses.
significantly different from zero. The negative coefficient of financially motivated
crimes is suggestive that they are inferior goods, decreasing as income increases.
Consistent with the aggregate regressions, young adults are less responsive
than youth. For financially motivated crimes, young adult males are about a third
as responsive as youth to predicted increases in employment opportunities. The
result that youths respond more to predicted changes in employment opportunities
for financially motived crimes is suggestive that financially motivated crimes
are more of a substitute for youth than for young adults. Youth are constrained
in the types of jobs they are eligible to work at due to many over-18 policies.
This can been seen in Figure 6. Youths tend to be employed only in retail, and
food. The relatively lower availability of employment opportunities could be an
24
TABLE 6.
Effects of Employment Opportunities on Crime by
Offense Group and Age
Group: 14-18 Year Olds 19-21 Year Olds
Male Female All Sexes Male Female All Sexes
Violent Crimes -0.693** -0.659 -0.667* -0.422* -0.744 -0.494*
Financially Motivated -1.257*** -0.595* -1.073*** -0.405* -0.271 -0.343*
Mischief -1.241*** -1.404* -1.304** -0.466 -0.129 -0.494
Drug-related -0.073 0.199 -0.150 -0.249 -1.499 -0.402
Personal Offense -1.069** -0.931 -1.172** -0.258 -0.351 -0.374
Substance Abuse -0.902*** -1.08** -1.018*** -0.084 -0.343 -0.367
14-21 Year Olds
Male Female All Sexes
Violent Crimes -0.662** -0.825 -0.705**
Financially Motivated -0.847*** -0.341 -0.743***
Mischief -0.907** -0.922 -0.903*
Drug-related -0.247 -0.496 -0.325
Personal Offense -0.702** -0.691 -0.696*
Substance Abuse -0.408** -0.418 -0.381*
This table reports estimates for the percentage change in arrests (by grouping) due to a one-percent increase
in youth employment opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1.
Errors are clustered at the state level. Regressions are weighted by annual state population for a particular
age-sex group.
Significance levels are adjusted for multiple hypothesis testing using the Benjamini-Hochberg step-up method.
explanation for why youths seem to be substituting toward financially rewarding
crimes. Another possible explanation for young adult arrests being less responsive
to increases employment opportunities is that since the young adults are much less
likely to be dependents and much more likely to be employed, the observed arrests
are happening to employed individuals. Youth, on the other hand, are typically
dependents and much less likely to be employed, so increases in employment
opportunities have a larger incapacitating effect than for young adults. This is
an intuitive finding if incapacitation is concave in employment. Since youth have
a much lower level of employment than young adults, the marginal effect is much
larger.
25
I split arrests by offense type to analyze which individual offenses respond
to changes in employment opportunities. I adjust significance levels for multiple
hypothesis testing using the Benjamini-Hochberg step-up method. Regressions
by offense are included in Tables 7, 8, and 9. Table 7 is youth offenses, table 8 is
young adult offenses, and Table 9 is both age groups. For youth, most offenses have
a negative coefficient. This table illustrates which individual offenses are driving
the aggregate results seen in Tables 2 and 3. For youth males, robbery, aggravated
assault, burglary, larceny, motor theft, fraud, stolen property, vandalism, weapon,
drug, drug possession, non-narcotic drug sale, liquor laws, and suspicion, are all
decreasing as predicted employment opportunities increase. Young adult males
see a reduction only in robbery arrests as employment opportunities increase.
This result suggests that robbery is a substitute for income. For both age groups,
robbery, burglary, and larceny, other assault, vandalism, weapon, drug sale,
disorderly , and other offenses all decrease with employment opportunities. Many
of these significant results are driven by the youth results. A few offenses, like
disorderly conduct, are not significant for either age group but significant for the
combined age group. Overall, income substitutes seem to be moving the most for
young adult males, a result that is consistent with Gould et al. (2002) and Mocan
and Rees (2005).
None of the offenses are changing at a rate significantly different from zero
for females. This is likely due to the fact that females are committing significantly
fewer crimes than males, so slicing the data by offense strips away any identifying
power.
26
TABLE 7.
The Effect of Employment Opportunities on Arrests by Offense for 14-18 Year Olds
Offense Male Female All Sexes
Murder -2.508 -5.867 -2.249
Manslaughter -1.127 5.071 0.257
Rape -0.343 -4.281 -0.491
Robbery -1.164** 1.046 -0.855*
Aggrivated Assault -0.732** -0.670 -0.696*
Burglary -1.461*** -0.782 -1.424***
Larceny -1.409*** -0.734 -1.156**
Motor Theft -1.075** -0.528 -1.022*
Other Assault -0.593 -0.628 -0.604
Arson -0.868 -4.305 -0.995
Forgery -0.907 -0.461 -0.665
Fraud -1.744** 0.208 -1.050*
Embezzlement -1.021 -0.605 -0.763
Stolen Property -1.830** -2.439 -1.892**
Vandalism -1.856*** -1.821 -1.813***
Weapon -1.130** -0.505 -1.131**
Prostitution -1.470 -0.242 -1.581
Sex Offense -0.364 -0.934 -0.235
Drug -1.074** -0.958 -1.173*
Drug Sale -0.811 -0.662 -0.916
Drug Possession -0.958** -0.767 -1.081*
Opium Sale -0.187 0.413 0.314
Marijuana Sale -1.614 -0.752 -1.738
Synthetic Narcotic Sale -0.887 -13.701 -6.134
Non Narcotic Sale -0.230** 1.488 -0.370**
Opium Possession -0.906 -1.610 -0.774
Marijuana Possession -1.096 -1.495 -1.311
Synthetic Narcotic Possession -2.402 -0.242 -2.347
Non-narcotic Possession -0.801 0.572 -0.632
Gambling -7.222 -1.357 -7.615
Family Offense -0.607 2.548 4.009
DUI -0.264 -0.096 -0.168
Liquor Laws -0.445** -0.928 -0.694*
Drunkenness -1.914 -1.097 -2.953
Disorderly -1.957** -2.539 -2.217**
Vagrancy -3.781 -6.550 -2.238
Other Offenses -1.283 -1.711 -1.440
Suspicion -12.001* -5.072 -15.499*
Curfew -2.212 -0.945 -1.876
Runaways -0.794 -0.465 -0.647
This table reports estimates for the percentage change in arrests (by offense category)
due to a one-percent increase in youth employment opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1.
Errors are clustered at the state level. Regressions are weighted by annual state
population for a particular age-sex group.
Significance levels are adjusted for multiple hypothesis testing using the Benjamini-
Hochberg step-up method.
27
TABLE 8.
The Effect of Employment Opportunities on Arrests by Offense for 19-21 Year Olds
Offense Male Female All Sexes
Murder -1.759 -6.855 -0.448
Manslaughter -0.838 -1.969 -0.761
Rape -0.203 -0.248 -0.354
Robbery -1.321* -1.721 -1.371
Aggrivated Assault -0.584 -0.913 -0.693
Burglary -0.254 -0.934 -0.305
Larceny -0.36 -0.373 -0.422
Motor Theft -0.62 0.808 -0.603
Other Assault -0.391 -0.605 -0.456
Arson 1.108 -0.95 0.036
Forgery -0.724 0.575 -0.277
Fraud -0.371 -0.189 -0.257
Embezzlement -0.419 -0.791 -0.325
Stolen Property -0.725 1.201 -0.664
Vandalism -0.59 -0.494 -0.59
Weapon -0.659 -2.519 -0.675
Prostitution -2.076 -1.363 -1.008
Sex Offense 0.281 -2.097 0.192
Drug -0.258 -0.351 -0.195
Drug Sale -0.505 0.166 -0.442
Drug Possession -0.212 -0.278 -0.146
Opium Sale -0.097 -0.902 -0.141
Marijuana Sale -0.971 0.72 -0.783
Synthetic Narcotic Sale -2.113 2.038 -1.55
Non-narcotoc Sale -1.478 -0.802 -1.463
Opium Possession -0.511 -0.32 -0.426
Marijuana Possession -0.061 -0.135 -0.033
Synthic Narcotic Possession -2.073 -2.099 -1.802
Non-narcotic Possession -0.463 0.453 -0.373
Gambling -5.618 1.575 -4.538
Family Offense 2.07 -0.2 -0.68
DUI 0.171 -0.034 0.223
Liquor Laws -0.132 -0.54 -0.228
Drunkenness -0.545 -0.917 -0.563
Disorderly -0.837 0.213 -0.624
Vagrancy -1.661 5.535 -0.401
Other Offenses -0.481 -0.207 -0.383
Suspicion 0.769 -4.638 -1.641
This table reports estimates for the percentage change in arrests (by offense
category) due to a one-percent increase in youth employment opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1.
Errors are clustered at the state level. Regressions are weighted by annual state
population for a particular age-sex group.
Significance levels are adjusted for multiple hypothesis testing using the
Benjamini-Hochberg step-up method.
28
TABLE 9.
The Effect of Employment Opportunities on Arrests by Offense for 14-21 Year Olds
Offense Male Female All Sexes
Murder -1.816 -4.585 -1.202
Manslaughter 3.317 -5.082 4.309
Rape -0.406 -4.276 -0.51
Robbery -1.407*** -0.43 -1.304***
Aggravated Assault -0.53* -0.814 -0.6*
Burglary -0.857*** -1.101 -0.904***
Larceny -0.94*** -0.388 -0.785**
Motor Theft -0.553 0.052 -0.538
Other Assault -0.654* -0.779 -0.703
Arson -0.517 -2.157 -0.651
Forgery -0.577 0.236 -0.269
Fraud -0.588 0.028 -0.319
Embezzlement -0.364 -0.928 -0.569
Stolen Property -1.18 -0.96 -1.184
Vandalism -1.155** -1.381 -1.129*
Weapon -1.053*** -1.156 -1.106**
Prostitution -3.154 -0.956 -1.098
Sex Offense -0.371 -2.081 -0.378
Drug -0.702 -0.686 -0.696
Drug Sale -0.722* -1.169 -0.697
Drug Poss -0.527 -0.542 -0.559
Opium Sale 0.045 -0.331 0.267
Marijuana Sale -1.577 0.007 -1.673
Synthetic Narc Sale -2.244 -6.216 -2.513
Non-narcotic Sale -0.82 -4.486 -1.092
Opium Possession -0.713 -0.623 -0.633
Marijuana Possession -0.529 -0.802 -0.634
Synthetic Narcotic Possession -1.257 -2.7 -1.708
Non-narcotic Possession -0.765 0.303 -0.64
Gambling -6.007 1.468 -4.262
Family Offense -0.709 2.606 0.603
DUI 0.048 0.038 0.146
Liquor Laws -0.314 -0.445 -0.384
Drunkenness 0.105 0.134 0.862
Disorderly -1.633* -2.024 -1.785*
Vagrancy -3.371 -0.543 -1.772
Other Offenses -0.903* -0.931 -0.904
Suspicion -6.363 -3.296 -6.225
This table reports estimates for the percentage change in arrests (by offense category)
due to a one-percent increase in youth employment opportunities.
Significance is indicated by ***p<0.01, **p<0.05, *p<0.1.
Errors are clustered at the state level. Regressions are weighted by annual state
population for a particular age-sex group.
Significance levels are adjusted for multiple hypothesis testing using the Benjamini-
Hochberg step-up method.
29
Conclusion
Effectively decreasing the incidence of juvenile crime is a central interest of
public policy. While a large body of research shows that increasing the certainty of
apprehension reduces crime, doing so comes at a cost. A rational model of crime
posits alternative sources of income can also be an effective way to reduce crime.
I test this relationship for youths by predicting employment growth and analyzing
how youth arrests respond to predicted changes in employment levels.
This paper makes two major contributions to the economic literature on
employment conditions and crime. The first contribution is that it provides
external validity to the RCT findings of Heller (2014) and Gelber et al. (2014),
which document the reduction of criminal activity due to the random assignment
of youth employment opportunities in large cities. This paper looks at systematic
predictions for job growth across 46 states, encompassing a much larger population
over a much larger time period. The second is the distinction between labor market
conditions, which are equilibrium outcomes, and labor market opportunities, which
isolate predicted demand side shocks in the labor market.
To examine the effect of labor market opportunities on crime, I use a shift-
share analysis to create predicted employment growth only due to demand side
shocks. I then use changes in expected employment growth to explain changes
in arrest rates. I find youth arrests decrease 1.08% due to a 1% increase in
employment opportunities. This translates into 30 fewer youth arrests due to 100
new youth job opportunities in a given state for a given quarter. Arrests are a
lower-bound estimate of criminal activity, so actual youth crime could be decreasing
even more. For young adults, this response is considerably smaller. A 1% increase
in employment opportunities leads to a 0.29% decrease in arrests, which translates
30
to 6 fewer arrests for every 100 new job opportunities in a given state for a given
quarter.
Violent, financially motivated, mischief, personal offenses, and substance-
abuse-related arrests all decrease for male youths as employment opportunities
increase. Young adult male arrests respond about a third as much as youth arrests
for financially motivated crimes, which is an intuitive result if incapacitation is
concave in employment. Since young adults are employed at much higher levels
than youth, the marginal effect of increased employment is much larger for youth.
Slicing arrests by offense type, robbery, aggravated assault, burglary, larceny,
motor theft, fraud, stolen property, vandalism, weapon, drug, drug possession, non-
narcotic drug sale, liquor laws, and suspicion all decrease as a result of increased
employment opportunities for youth males. A possible limitation of these findings
is that they rely on voluntarily reported arrests. Only a fraction of criminal activity
results in an arrest since many crimes go undetected or unreported, so these results
likely understate the effect of employment opportunities on crime. Secondly, many
youth employment opportunities, such as babysitting or yard work for a neighbor,
will not be recorded in my data, since I see only employment for the duration of
a quarter recorded by firms for unemployment insurance obligations. Nonetheless,
these results are informative about youth and young adult responses to increased
employment opportunities in the formal sector.
A natural extension of the work is to shift time periods for youths to
capture summertime employment separately from school-year employment. Also,
obtaining employment data by race would allow for an analysis of the opportunity
of employment across races. Finally, in coming work, I plan to apply a similar
31
shift-share analysis at the state level and use counties as the local geographies
responding to changes statewide trends.
32
CHAPTER II
INFORMATION AND THE PERSISTENCE OF THE GENDER WAGE GAP;
EARLY EVIDENCE FROM CALIFORNIA’S SALARY HISTORY BAN
Introduction
Wage inequality across genders improved substantially during the twentieth
century but has since plateaued 1, despite the increase in female college enrollment
(Goldin, 2014; Goldin et al., 2006). Figure 7 illustrates the female to male earnings
ratio over the last 50 years.
FIGURE 7.
Female to Male Median Earnings Ratio of Full-Time Workers
0.80 Ratio
0.75
0.70
0.65
0.60
1960 1965 1970 1975 1980 1985 1990 1995 2000 2005 2010 2015 2020
Year
The literature lacks consensus on the underlying drivers of the gender
wage gap. O’Neill and Polachek (1993); Blau and Kahn (2006a); Mulligan and
Rubinstein (2008) all present different possible explanations in the narrowing of the
gender pay gap. Some explanations point to bargaining as a cause for the gender
1 Evidence of the narrowing of the gender pay gap can be seen in Blau and Kahn (2013, 2017,
2000, 2006a,b).
33
Earnings Ratio
pay gap, see Babcock et al. (2003). Others claim differences in competitiveness
drives the gender pay gap, see Gneezy et al. (2003); Niederle and Vesterlund
(2007). Alternatively, Manning and Saidi (2010) find little empirical evidence that
competitiveness drives the gender pay gap. It is unclear what, if anything, federal,
state, and municipal policy makers can do about the issue. A recent tool gaining
popularity is the salary history ban (SHB).
This paper is the first to offer evidence on the causal impact of SHBs.
Cities and states have recently been adopting variations of SHB laws, which
prohibit employers from asking about applicants’ previous compensation. These
laws address wage discrimination in multiple ways with the intent to reduce
salary disparity across genders. First, when current compensation is based on
previous salary, past wage discrimination could be perpetuated. Second, women
are more likely to work in female-dominated industries, which pay less than
male dominated industries. The salary history question could be perpetuating
the systemic undervaluation of women’s work. SHB laws could eliminate path
dependent compensation across multiple margins. Alternatively, SHB laws could
have unintended consequences that cause employers to engage in more statistical
discrimination. This has been seen before, notably due to the implementation of
ban the box policies (Henry and Jacobs, 2007; Agan and Starr, 2016; Doleac and
Hansen, 2016; Shoag and Veuger, 2016; Starr, 2014).
Specifically, this paper focuses on the SHB passed in California in January of
2018. The legislative commentary below demonstrates that pay equality was the
motivation behind California’s SHB.
“Gender wage discrimination is destructive not only for female workers
but for our entire economy. Closing the wage gap starts with barring
34
employers from asking questions about salary history so that previous
salary discrimination is not perpetuated.” - California legislature
In a competitive market, recent wages signal a worker’s marginal productivity,
which is of greatest interest to hiring firms (Kotlikoff and Gokhale, 1992; Altonji
and Pierret, 2001; Oyer et al., 2011; Lange, 2007). Labor markets may not be
perfectly competitive, but the assumption gives insight to why past wages matter
to firms. A previous wage can serve as a signal about the value of previous work.
And, firms do ask about prior earnings. Barach and Horton (2017) find over 80%
of respondents to a nationally representative Google Survey were asked by their
employer about past wages.
Some experimental work has been done on removing compensation history
from an online contracting labor market (Barach and Horton, 2017). They find
that banning wage history results in more call backs in general and more offers to
workers with lower past average wages. Their field experiment takes place in a very
unique online labor market. To my knowledge, no work has been done evaluating
the implementation of salary ban laws in the United States.
This research contributes to a broader literature which examines how changes
in employer screening affect labor outcomes for potential employees, specifically,
in the context of SHBs. This question about employer screening methods has
been addressed in the context of drug testing (Wozniak, 2015), credit screening
(Bartik and Nelson, 2016), test-based worker screening (Autor and Scarborough,
2008), criminal history checks (Finlay, 2009; Bushway, 2004; Holzer et al., 2006,
2007; Stoll, 2009), and ban the box policies (Henry and Jacobs, 2007; Agan and
Starr, 2016; Doleac and Hansen, 2016; Shoag and Veuger, 2016; Starr, 2014).
35
These papers suggest limiting information can often have unintended consequences,
increasing gaps, or shifting them disproportionately to other marginalized groups.
I use a synthetic control approach to estimate the causal impact of SHB
laws in the state of California on gender wage ratios and other labor outcomes
of interest calculated from the Basic Monthly Current Population Survey. I
find that California’s state wide weekly earnings ratio, which has been stagnant
around 0.77 for more than 12 years, increases from 0.77 to 0.81 after adoption of a
statewide SHB. These results are driven by women earning more in male dominated
industries.
The paper proceeds as follows: Section 2.2 provides background on SHB
policies. Section 3.3 describes the data. Section 2.4 presents my empirical
methodology. Section 3.4 describes my results. Section 2.6 discusses and concludes.
Background on SHBs
Salary history bans (SHBs) prohibit employers from inquiring about a
candidates former or current compensation. Currently, SHBs have been adopted
by a growing number of cities and states in varying degrees. Some affect the entire
population, some only state employees, and some only city employees. The rapid
uptake of SHBs suggest that many entities believe SHBs will improve gender pay
inequalities. Table 10 summarizes different cities and states that have adopted
SHB laws. Most of the SHBs only apply to a subset of the population. The states
with SHBs that affect the entire population and that have been implemented long
enough to exist in my data are Delaware and California. As of July 1st 2018,
36
Massachusetts, and Vermont have also implemented SHBs affecting the entire
population. 2
TABLE 10.
Salary History Ban Laws by Date and Region
Adoption Date Region Population
12/4/16 NYC City employees
1/9/17 New York State employees
1/25/17 New Orleans City employees
3/01/17 Pittsburgh City employees
10/31/17 NYC All
12/14/17 Delaware All
1/1/18 California All
4/10/18 Chicago City employees
2/1/18 New Jersey State employees
5/17/18 Louisville City employees
7/1/18 Massachusetts All
7/1/18 San Francisco (strong) All
7/1/18 Vermont All
7/26/18 Kansas City City employees
1/1/19 Oregon All
1/1/19 Hawaii All
California’s SHB became effective January 1 of 2018. Under California’s SHB
employers are prevented from seeking compensation history directly or through
an agent. Like Delaware, applicants may volunteer, without prompting, their own
salary history. Additionally, California restricts employers from basing salary solely
on the grounds of prior salary. The SHB also requires employers to provide a salary
range at the request of the applicant. After an offer has been extended, Californian
employers may seek the applicant’s compensation history.
2 The treatment of these states is too recent to show up in the data. I plan to include them in
future analysis.
37
States that have implemented SHBs affecting state employees only include
New York and New Jersey. Cities with SHBs affecting city employees only include
Pittsburgh, Chicago, and Louisville. New York City, which had adopted a SHB
effective for city employees, recently extended their SHB to the entire population of
New York City. Oregon and Hawaii will both adopt a SHB that affects the entire
population in January of 2019.
Each SHB adopting entity clearly states that they have adopted the SHB
to promote pay equality. The cities and states with a SHB law also tend to be
more progressive on the pay equality front. With the recent uptake of SHBs, some
states have implemented laws that prevent SHBs from being passed. These states
include Michigan, Wisconsin, Iowa, North Carolina, and Tennessee. Philadelphia
prevented the implementation of a SHB when a district judge found the SHB to
be in violation of the First Amendment’s free-speech clause. States preventing the
adoption of SHBs have done so with employer compliance in mind. They argue
that allowing employment law to change across regions is costly for small business
owners.
Data
I use data from the Basic Monthly Current Population Survey (CPS). The
CPS is a comprehensive survey containing monthly labor force statistics. Other
potential useful data sources for employment measures include the American
Community Survey, the Quarterly Workforce Indicators, and the Current
Employment Statistics, but each of these alternative data sources have a delayed
release schedule. The CPS is published roughly 10 days after each month’s end.
38
This makes it particularly useful given that the rollout of SHBs is so recent 3. It
samples roughly 60,000 households each month using a rotating panel design and
has a response rate averaging around 90 percent. I use the micro-level data, which
has responses by all household members as reported by the call recipient; then I
aggregate to the state level. My sample includes data from 2006 to the most recent
month of the CPS available. I continually update my estimates with each data
release.
The CPS is administer by the Census Bureau through personal and telephone
interviews. Individuals must be 15 years of age or over and not in the Armed
Forces. The person who responds to the phone call is the reference person. They
answer questions about all persons in the household. In the case that the reference
person is not knowledgeable, the Census Bureau attempts to contact those
individuals in the household directly.
I create statewide average weekly earnings ratios of female to male earnings
for each state. Additionally, I calculate earnings ratios by age, and by industry of
employment. I also calculate employment probabilities by sex. I use each of these
calculated values as a potential employment measure of interest.
Methodolgy
I use the synthetic control method introduced by Abadie et al. (2010).
This method uses pretreatment data to create a counterfactual group similar in
outcomes to entities experiencing a discrete change in policy. This method has
been used to study many different policy changes including decriminalization of
prostitution (Cunningham and Shah, 2017), highway police budget cuts (DeAngelo
3I obtained these data using the lowdown package for R. The data are available for download
almost immediately after the end of a month.
39
and Hansen, 2014), economic liberalization (Billmeier and Nannicini, 2013), and
increases in minimum wage (Jardim et al., 2017). I follow the work of Botosaru and
Ferman (2019) and create synthetic control groups matching outcomes only for each
treated entity.
Consider an outcome of interest Yit that is measured over T years, where
t indexes the time and the state is indexed by i if its treated and j if its not
treated, among I treated states and J untreated states. The synthetic control
approach aims to estimate the treatment effect, which is the difference between the
treated state, and the unobserved counterfac∑tual. The estimate for the unobserved
counterfactual for state i in time period t is j wjYjt, where wj is the weight
assigned to donor state j. The donor states chosen belong to the donor pool of
poten∑tial control states. The chosen weights w∗j minimize the distance between Yit
and j wjYjt for all pretreatment time periods. For treatment in period τ∑, the
treatment effect αi for state i in time period t is estimated as α
∗
it = Yit − j wjYjt
for t ∈ [τ, T ]. For each treated state, I create a synthetic control using lagged values
of the dependent variable from 2006 to 2018.
To conduct hypothesis tests, I run a set of placebo tests following the method
suggested by Abadie et al. (2010). I apply the same synthetic control method with
the donor state removed, and the treated states added to the donor pool to create
Synthjt for each donor state j and time period t. I compare the pre-treatment and
post-treatment mean squared prediction error (MSPE) for each state. I calculate
the MSPE ratio as follows:
∑T
(Yjt − Synthjt)2
MSPE ratio = t=τj .τ∑−1
(Yjt − Synth 2jt)
t=1
40
The MSPE measures a relative goodness of fit of the synthetic outcome generated
for each state. It provides a metric of pre-treatment fit relative to post treatment
fit for each state. A high MSPE ratio can be interpreted as poor post-treatment
fit relative to pre-treatment fit. The ranking of the treated states relative to the
placebo states provides a permutation based p-value.
I include a relatively long pretreatment window from 2006 to 2017. This
allows me to match on pretreatment outcomes only. Botosaru and Ferman (2019)
show that matching on covariates is not necessary if the match is made on a long
set of pretreatment outcomes. I define treatment in California as the adoption of
their state-wide SHB on January 1 of 2018. New York and Delaware are excluded
from the potential donor pool as they each adopt a SHB at the end of 2017. The
donor pool consists of 47 possible states and Washington D.C.
The synthetic control approach creates an estimate of the counterfactual
for California. Absent treatment, the synthetic California should match actual
California reasonably well. I test the ability of the synthetic control approach
to forecast the earnings ratio in California prior to treatment. I do this by
progressively rolling back a placebo treatment, matching on fewer and fewer
years. Within this exercise, I examine how well the synthetic control approach
does at predicting the earnings ratio within the pretreatment time period. The
cross validation exercise shows that the synthetic control approach succeeds
in forecasting one step ahead except for in 2018, the year actual treatment
begins. This can bee seen in Figure 8. As treatment rolls back in time, the
synthetic California matches the actual California in both levels and trends. This
cross validation exercise also shows that the synthetic control is a reasonable
counterfactual. Figure 8 shows the distribution of the MSPE ratios for the placebo
41
states and for California. As treatment is rolled back in time, California’s MSPE
ratio goes from being an outlier to well within the mean of the distribution. This
figure also illustrates the sensitivity of MSPE ratios. As there are fewer and fewer
pretreatment years, the post treatment MSPE can get very large driving up the
MSPE ratio.
The composition of the synthetic control can be seen in Figure 9. The
time-series of the female to male earnings ratio before California’s SHB is best
reproduced by a combination of 29% Nevada, 24% Arizona, 16% D.C., 12% North
Carolina, 6% Hawaii, 4% Florida, and, 1% Oregon. All other donor states are
assigned a weight of zero.
The weights chosen are consistent across the placebo treatments in the cross
validation exercise. Table 11 shows the composition of weights as the placebo
treatment is rolled back in time. Notably, the composition of the synthetic
California is stable across fewer and fewer pre treatment years. The weights chosen
are consistent for each of the cross validation years and they consistently predict
the actual California earnings ratio.
Using the detailed industry codes, I classify each industry in the CPS as male
or female dominated. I classify male dominated industries as industries with more
than 50 percent male workers and classify industries with more than 50% female
workers to be female dominated. I use the industry gender compositions reported
by the Equal Employment Opportunity Commission in Cartwright et al. (2011) to
classify each industry as male or female dominated. Female dominated industries
are in the service producing domain and male dominated industries tend to be in
the goods producing domain.
42
FIGURE 8.
California Cross Validation
(b) MSPE Ratio Distribution for
(a) Treatment in 2018
Treatment in 2018
SHB
0.82
30 ●TX●MD
●●
FL
AL
NM
0.80 California ●●MO●ID●KS●NH
20 ●●
DC
ND
0.78 ●COWA
Synthetic ●●OR●OK
California ●NV●HI
0.76 ●LA●KYWY
10 ●●WIINMI
●●AR●GA
0.74 ●●
NJ●●NCMTWV
●VA●AK●VT●SD●MA●CTNE●AZ●●IA●●MN●MEUTTNRI IL CA
2006 2008 2010 2012 2014 2016 2018 0 ●●●● ●
year 0 100 200 300 400
Post MSPE / Pre MSPE
(d) MSPE Ratio Distribution for
(c) Treatment in 2017
Treatment in 2018
SHB −S 1HB
0.82
30 ●CA●CO●NH●IDFL
0.80 California ●●LA●WA●MS●AZKS
20 ●●OR
0.78 ●DCMD
Synthetic ●●HI
California ●●
AL
WY
●WV
0.76 ●NC●KYGA
10 ●●AKVTMA
●●ND●●CT
0.74 ●IN●RI●UTNV●M●●INMNE●PA●OK●IL●MN●AR●●MT●SDMOIAWITN●ME●NJ●OH TX SC VA
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019 0 ●●●● ● ● ●
year 0 100 200 300 400
Post MSPE / Pre MSPE
(f) MSPE Ratio Distribution for
(e) Treatment in 2016
Treatment in 2016
SHB − 2 SHB
0.82
30
0.80 California
20 ●●
CA
CO
0.78 ●●
LA
ID
Synthetic ●DC●FL
California ●MS●WY●GA
0.76 ●WV●NM●KSNH●TN10 ●NC●
●RI
OK
●AZ●●MA●ALVT
0.74 ●WA●●NJ●MINEOH
●●
ND●ME●OR
AR●●AK●●TX●HIMTILSD●UT●●W●●INV●MNSCMDPAIN●CT●IAKY MOVA
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019 0 ●●●●●● ●●
year 0 100 200 300 400
Post MSPE / Pre MSPE
(h) MSPE Ratio Distribution for
(g) Treatment in 2015
Treatment in 2015
SHB − 3 SHB
0.82
30
0.80 California
20
0.78 ●CA●DCCO
Synthetic ●●MSWY
California ●
●●
ID
KS●VT0.76 ●ME●AL●UT●LA●NE10 ●HIMD●M●●IRI●AZ●MT
0.74 ●ND●NJOR●GA●W●●IMN●NMOHSC●NC●●AK●●FL●AR●WACT●MA●IL●●SD●KYNHNVINTNPA OKMO WV VA TX
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019 0 ●●●●● ●● ● ● ●
year 0 100 200 300 400
Post MSPE / Pre MSPE
Notes: This figure illustrates the ability the synthetic control approach to forecast out of sample. For each subfigure, matching only
occurs to the left of the treatment line.
43
Female to Male Earnings Female to Male Earnings Female to Male Earnings Female to Male Earnings Ratio
count count count count
FIGURE 9.
Composition of Synthetic California
Donor State Weight
Nevada 29%
Arizona 24%
District of Columbia 16%
North Carolina 12%
Mississippi 7%
Hawaii 6%
Florida 4%
Oregon 1%
Notes: This figure shows the composition of donor states used to make a synthetic California. States are shaded in proportion to
their weighted contribution towards synthetic California.
Results
The cross validation exercise from the previous section showed that the
synthetic California generated by the synthetic control approach does well at
predicting out of sample. I first consider the effect of the SHB on state-wide
earnings ratios. I then investigate weekly earnings, hours worked, and hourly wages
by sex. Then I turn to industry classifications reported in the CPS and analyze the
effect of SHB within predominately male and predominantly female industries, as
well as goods vs service industries. I split my sample by age, and investigate the
impact of the SHB among older and younger populations. Finally, I investigate the
impact of SHBs on the probability of employment for both males and females at
the state level and within industries.
Female to Male State-Wide Earnings Ratio
Figure 10a illustrates the female to male average weekly earnings ratio in
California and its synthetic counterpart from 2006 to 2018. Over the 11 year
window from 2006 to 2017 California’s synthetic counterpart closely matches, both
44
TABLE 11.
Cross Validation Weights
Weight by Placebo Treatment Year
Donor State 2018 2017 2016 2015 2014 2013 2012 2011
Alabama - - - - - - - -
Alaska - - - - - - - -
Arizona 24% 23% 23% 26% 28% 26% 25% 28%
Arkansas - - - - - - - -
Colorado - - - - - - - -
Connecticut - - - - - - - -
District of Columbia 16% 16% 16% 15% 17% 16% 16% 14%
Florida 4% 5% 4% - - 10% 12% -
Georgia - - - - - - - -
Hawaii 6% 6% 6% 6% 1% 1% 2% 25%
Idaho - - - - - - - -
Illinois - - - - - - - -
Indiana - - - - - - - -
Iowa - - - - - - - -
Kansas - - - - - - - -
Kentucky - - - - - - - -
Louisiana - - - - - - - -
Maine - - - - - - - -
Maryland - - - - - - - -
Massachusetts - - - - - - - -
Michigan - - - - - - - -
Minnesota - - - - - - - -
Mississippi 7% 6% 7% 7% 9% - - -
Missouri - - - - - - - -
Montana - - - - - - - -
Nebraska - - - - - - - -
Nevada 29% 28% 30% 32% 32% 18% 18% -
New Hampshire - - - - - - - -
New Jersey - - - - - - - -
New Mexico - - - - - - - -
North Carolina 12% 13% 13% 12% 12% 22% 23% 24%
North Dakota - - - - - - - -
Ohio - - - - - - - -
Oklahoma - - - - - - - -
Oregon 1% 1% - - - 1% - 7%
Pennsylvania - - - - - - - -
Rhode Island - - - - - - - -
South Carolina - - - - - - - -
South Dakota - - - - - - - -
Tennessee - - - - - - - -
Texas - - - - - - - -
Utah - - - - - - - -
Vermont - - 1% 1% - - - -
Virginia - - - - - - - -
Washington - - - - - - - -
West Virginia - - - - - - - -
Wisconsin - - - - - - - -
Wyoming - - - - - - - -
Table notes here
45
in trends and levels, the observed female to male earnings ratio. In the window
after California adopts the state-wide SHB, its average female to male earnings
ratio diverges from from 0.77 to 0.82. Not only does the California earnings
ratio diverge from its synthetic counterpart, it also diverges from the level it has
been close too for the past 11 years. Figure 10b visually illustrates the statistical
precision of my synthetic control estimate. The red line represents the difference
between California and its synthetic counterpart. The red line hovering around
zero before the SHB illustrates that synthetic California is a close match for actual
California. After the SHB, California’s earnings ratio diverges from its synthetic
counterpart. Only a few of the placebo states deviate close to as much as California
post SHB. In Figure 10c I calculate the pre MSPE to post MSPE ratio for each
placebo state and California. Notably, California has the highest MSPE ratio, over
3 times higher than the next highest MSPE ratio. There is probability 1/48=0.0208
that we would observe a MSPE ratio as large as California’s if we randomly
assigned a SHB to a state in the data4. Table 12 reports the point estimates and
the permutation based p-values.
My synthetic control estimates suggest that California adopting a salary
history ban increased average weekly female earnings relative to average weekly
male earnings. I estimate the change in the earnings ratio from its synthetic
counterpart to be .0239 which is a 10.4% decrease in the earnings gap. This finding
suggests that the earnings ratio improved as a result of the SHB. I next explore
potential mechanisms through which SHBs have caused the change in the earnings
ratio.
4The p-value of 0.0208 is the lowest possible p-value given the number of states in my sample.
46
FIGURE 10.
California Female to Male Earnings Ratio
(a) Synthetic Control
SHB
0.82
0.80 California
0.78
Synthetic
California
0.76
0.74
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019
year
Notes: This figure shows the annual time series of California’s earning (red) and the time series of the
synthetic California (blue)
(b) Actual California - Synthetic California vs. Placebo States
SHB
0.05 Control States CA
0.00
−0.05
−0.10
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
Notes: This figure shows the difference between the synthetic control and the actual earnings ratio for each
placebo state.
(c) MSPE Ratio Distribution
●OH●MS●PASC
30 ●●TXMD
●●FL●AL●NMMO
●●ID●KS●NHDC
20 ●●ND●CO●WA●OR●OK●NV●HI●LA●KY●WY10 ●WI●IN MI●AR ●GA●NJ ●NC
●●
MT ●WV
VA ●AK
●VT ●●SD●MA ●CT ●NE●AZ IA MN ME●UT ●●TN ●●RI ●IL CA0 ● ●
0 50 100 150 200
Post MSPE / Pre MSPE
Notes: This figure shows the distribution of MSPE ratios for each of the control states and California. The
ratio compares pre treatment versus post treatment fit for each state.
Weekly Earnings, Hours Worked, and Wages by Sex
The earnings ratio could change if there is a disproportional change in the
level of either male or female earnings. Changes in earnings could be a result
47
count Gap Female to Male Earnings Ratio
TABLE 12.
Change in Average Weekly Female to Male Earnings Ratio
State-Wide
SHB 0.0303**
P-Value [0.020]
Younger Older Than
Than 35 35
SHB 0.0115 0.0256**
P-Value [0.694] [0.020]
Female Male Service Good
Dominated Dominated Proving Producing
Industries Industries Industries Industries
SHB 0.0084 0.0419 0.0280** 0.0539**
P-Value [0.429] [0.102] [0.020] [0.020]
Table notes here
of changes in wages or changes in hours worked. For these reasons, I investigate
average weekly earnings, hours worked, and hourly wages by gender.
Figure 11a plots average weekly earnings data for California and its synthetic
counterpart by sex. For both males and females, the trends and levels of the
synthetic control group closely follow California’s for the years prior to the SHB.
After the SHB the male earnings slightly decrease and female earnings increase
relative to each of their synthetic counterparts. The point estimates corresponding
with Figure 11a are reported in Table 13 with permutation based p-values in
brackets. While the increase in female earnings and decrease in male earnings are
not significantly different from zero, we know they jointly significant. Figures 11b
and 11c illustrate the precision of the synthetic control estimates. The solid red
48
depicts California’s deviation from its synthetic counterpart for each sex. The red
line hovers around zero before the SHB, which illustrates that synthetic California
is a close match for actual California for each sex. The red line lying well within
the deviations observed in the post period for the placebo states illustrates that
these slight deviations are likely due to noise.
TABLE 13.
Change in Average Weekly Earnings and Hours Worked
Weekly Earnings Weekly Hours Worked
State-Wide
Female Male Female Male
SHB 3.1296 3.1627 0.3279** -0.299
P-Value [0.857] [0.837] [0.041] [0.388]
Male Dominated industries
Female Male Female Male
SHB 54.2317 26.2456 0.3314* 0.2654
P-Value [0.122] [0.122] [0.082] [0.653]
Female Dominated Industries
Female Male Female Male
SHB -7.9003 -24.4772 0.2556 -0.8066
P-Value [0.429] [0.327] [0.143] [0.102]
Younger Than 35
Female Male Female Male
SHB 25.9226 14.0185 0.6374** -1.2215**
P-Value [0.224] [0.551] [0.041] [0.020]
Older Than 35
Female Male Female Male
SHB -5.6522 -7.811 0.1354 -0.5514
P-Value [0.714] [0.714] [0.224] [0.286]
49
FIGURE 11.
Average Weekly Earnings by Gender
(a) Average Weekly Earnings by Gender
SHB
1200 Actual CA Synthetic CA
1100
Male
1000
900
Female
800
700
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Earnings
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
0
−100
−200
−300
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Earnings
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
0
−100
−200
−300
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
50
Gap Gap Average Weekly Earnings
The analogous analysis for average weekly hours worked by sex is shown in
Figure 12a. For both females and males, the synthetic control matches the levels
and trends of average weekly hours worked. After the SHB, average weekly hours
worked slightly decrease for males and slightly increase for females relative to
their synthetic counterpart. The point estimates can be found in Table 13 with
permutation based p-values in brackets. Females worked .37 hours more than
their synthetic counterpart, and males worked .69 hours less than their synthetic
counterpart. While the change in hours worked for males is larger than females,
it is not statistically different from zero and is likely due to noise. Figures 12b
and 12c illustrate the statistical precision of these point estimates. They show
deviations from average weekly hours worked in California and its synthetic
counterpart relative to the placebo states for each sex. For females, the synthetic
counterpart matches actual hours worked very well. The tight match pre SHB and
deviation post SHB results in a small p-value.
Figure 13a shows average weekly hourly wages for California and its synthetic
counterpart by sex. The synthetic control group does a good job of matching
in levels and trends for actual California’s hourly wage for both sexes. After
the SHB, average weekly hourly wage slightly decreases for males and slightly
increases for females relative to their synthetic counterparts. Table 14 reports the
point estimates and permutation based p-values in brackets. Figures 13b and 13c
illustrate the statistical precision of these point estimates. Similar to the figures
for earnings and wages, the solid red line represents the difference from California
and its synthetic counterpart. For males, the red line hovers around zero both
before and after the SHB. For females, the red line increases after the SHB, but the
51
FIGURE 12.
Average Weekly Hours Worked by Gender
(a) Average Weekly Hours Worked by Gender
Actual CA Synthetic CA SHB
38 Male
36
Female
34
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hours:
Actual - Synthetic California vs Placebo States
2 SHB
Control States CA
1
0
−1
−2
−3
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hours:
Actual California - Synthetic California vs Placebo States
2 SHB
Control States CA
1
0
−1
−2
−3
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
52
Gap Gap Average Hours Worked per Week 
deviation is well within the deviations observed in the post period for the placebo
states.
FIGURE 13.
Average Weekly Hourly Wage by Gender
(a) Average Weekly Hourly Wage by Gender
SHB
Actual CA Synthetic CA
20
Male
18
16
Female
14
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hourly Wage:
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hourly Wage:
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
0.5
0.0
−0.5
−1.0
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
53
Gap Gap Average Hourly Wage
TABLE 14.
Change in Hourly Wage by Sex and Industry
State-Wide
Female Male
SHB 0.213 0.0889
P-Value [0.224] [0.857]
Male Dominated industries
Female Male
SHB 0.9587** 0.3321
P-Value [0.020] [0.388]
Female Dominated Industries
Female Male
SHB 0.0314 -0.5352
P-Value [0.918] [0.367]
Younger Than 35
Female Male
SHB 0.4215 -0.1834
P-Value [0.204] [0.327]
Older Than 35
Female Male
SHB -0.0399 -0.3345
P-Value [0.939] [0.286]
Industry of Employment
The above results are state-wide averages, however, it is possible that the
effects of the SHB are not uniform across the state. For this reason, I investigate
differential effects within male dominated and female dominated industries. As
noted, I define an industry as female dominated if it has a composition of more
54
than 50 percent females within that industry. Male dominated industries are
defined analogously. I repeat the earnings ratio analysis within male and female
dominated industries. Similar to above, I then investigate earnings, hours, and,
wages within male and female dominated industries.
Figure 14 illustrates the California female to male average weekly earnings
ratio and their synthetic counterpart for each industry. The synthetic California
earnings ratio matches actual California in both levels and trends before the SHB
in both male and female dominated industries. The match is slightly better for
female dominated industries. After the SHB, the actual ratio does not deviate
from the synthetic ratio for female dominated industries. In male dominated
industries, however, the actual California earnings ratio increases relative to its
synthetic counterpart. Table 12 reports the point estimates and the permutation
based p-values. Figure 15 illustrates the statistical precision on these estimates by
plotting the difference in California and each placebo state relative to its synthetic
counterpart. Within female dominated industries, the difference between the
actual California earnings ratio and its synthetic counterpart is close to zero both
before and after the SHB. For male dominated industries, the difference between
the California earnings ratio and its synthetic counterpart hovers around zero
before the SHB. After the SHB, the ratio deviates from its synthetic counterpart
by a large amount relative to the placebo state deviations. This results in a
relatively small p-value for the changes in the earnings ratio within male dominated
industries. Within female dominated industries the difference between the
California earnings ratio and its synthetic counterpart hovers around zero before
and after the SHB.
55
FIGURE 14.
Average Weekly Earnings Ratio by Industry Type
(a) Female Dominated Industries
SHB
0.85
California
Synthetic
California
0.80
0.75
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019
year
This figure shows the average weekly earnings ratio in industries that are more than
50% female.
(b) Male Dominated Industries
0.88 SHB
California
0.84
Synthetic
California
0.80
0.76
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019
year
This figure shows the average weekly earnings ratio in industries that are more than
50% male.
These results suggest the change in the state-wide earnings ratio is composed
of larger changes in male dominated industries and relatively smaller changes
within female dominated industries. I estimate the increase in the female to male
earnings ratio to be .0579, which is a 32% decrease in the earnings gap (within
56
Average Weekly Earnings Ratio Average Weekly Earnings Ratio
FIGURE 15.
Actual California - Synthetic California vs Placebo States by
Industry Type
(a) Female Dominated Industries
0.15 SHB
Control States CA
0.10
0.05
0.00
−0.05
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Dominated Industries
SHB
Control States CA
0.1
0.0
−0.1
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
male dominated industries). Next I turn to mechanisms of these findings with in
male and female dominated industries.
Weekly Earnings, Hours Worked, and, Wages by Sex and Industry
The earnings ratio within industries could change if there is a disproportional
change in the level of either male or female earnings within industries. Changes in
57
Gap Gap
earnings could be a results of changes in wages or changes in hours worked. For
these reasons, I investigate average weekly earnings, hours worked, and hourly
wages by gender within male and female dominated industries.
Figure 16a illustrates male and female average weekly earnings in female
dominated industries compared to their synthetic counterpart. For both sexes, the
synthetic California matches actual California earnings in both levels and trends
before the SHB. After the SHB, female earnings in female dominated industries
continue to match their synthetic counterpart. Male earnings in female dominated
industries deviate slightly below their synthetic counterpart. Table 13 provides
the point estimates and the permutation based p-values in brackets. The p-values
for both male and female earnings within female dominated industries indicate
that I cannot reject the null hypothesis that the SHB caused no changes. Figures
16b and 16c illustrate the gap between California average weekly earnings and its
synthetic counterpart vs the placebo states. For both females and males, post SHB
deviations lie well within deviations of the placebo states.
Figure 17a illustrates male and female average weekly earnings in male
dominated industries compared to their synthetic counterpart. Again, for both
sexes, the synthetic California matches actual California earnings in both levels and
trends before the SHB. After the SHB, male earnings in male dominated industries
continue to match their synthetic counterpart. Female earnings in male dominated
industries increase relative to their synthetic counterpart. Figure 17b and 17c
illustrate the gap between California weekly earnings within male dominated
industries and their synthetic counterpart. Both the female and male earnings
gap hover around zero before the SHB, indicating that the synthetic control is a
good match. After the SHB, the female earnings’ deviation from their synthetic
58
FIGURE 16.
Average Weekly Earnings by Gender Within Female
Dominated Industries
(a) Average Weekly Earnings by Gender
SHB
Actual CA Synthetic CA
1200
1000 Male
800 Female
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
59
Gap Gap Average Weekly Earnings 
counterpart is among the highest of the placebo states. The point estimates and
the permutation based p-values in brackets can be seen in Table 13.
Figure 18a illustrates male and female average weekly hours worked in female
dominated industries compared to their synthetic counterpart. For both sexes, the
synthetic California matches actual California hours worked in both levels and
trends before the SHB. After the SHB, female hours worked in female dominated
industries increase 1 hour per week relative to their synthetic counterpart. Male
hours worked in female dominated industries continue to match their synthetic
counterpart. Table 13 provides the point estimates and the permutation based p-
values in brackets. The p-value for male hours worked within female dominated
industries indicate that I cannot reject the null hypothesis that the SHB caused no
changes. Figures 18b and 18c illustrate the gap between California average weekly
earnings and its synthetic counterpart vs the placebo states. For females, the post
SHB deviation is among the largest of deviations for the placebo states.
Figure 19a illustrates male and female average hours worked in male
dominated industries compared to their synthetic counterpart. For both sexes, the
synthetic California matches actual California worked in both levels and trends
before the SHB. After the SHB, female hours worked in male dominated industries
increase relative to their synthetic counterpart. Male weekly hours worked also
slightly increase in male dominated industries post SHB. Table 13 provides the
point estimates and the permutation based p-values in brackets. Figures 19b and
19c illustrate the gap between actual California’s average weekly hours worked and
its synthetic counterpart vs the placebo states. For females, the post SHB deviation
is among the largest deviations of the placebo states. This results in a relatively
60
FIGURE 17.
Average Weekly Earnings by Gender Within Male
Dominated Industries
(a) Average Weekly Earnings by Gender
SHB
Actual CA Synthetic CA
1200
1000 Male
800 Female
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
61
Gap Gap Average Weekly Earnings 
FIGURE 18.
Average Weekly Hours Worked by Gender Within Female
Dominated Industries
(a) Average Weekly Hours Worked by Gender
Actual CA Synthetic CA SHB
38
Male
36 Female
34
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hours Worked
Actual California - Synthetic California vs Placebo States
SHB
2 Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hours Worked
Actual California - Synthetic California vs Placebo States
SHB
2 Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
62
Gap Gap Average Weekly Hours Worked 
small p-value. For males, the p-value suggests the point estimate is not statistically
distinguishable from zero.
Figure 20a illustrates male and female average hourly wage in female
dominated industries compared to their synthetic counterpart. For both sexes,
the synthetic California matches the overall trend of actual California but with
less variation. After the SHB, female hourly wages in female dominated industries
slightly increase relative to their synthetic counterpart. On the other hand, male
hourly wages in male dominated industries slightly decrease relative to their
synthetic counterpart. Table 14 provides the point estimates and the permutation
based p-values in brackets. Figures 20b and 20c illustrate the gap between actual
California’s average hourly wage and its synthetic counterpart vs the placebo
states. The poor match pre SHB for both males and females makes their deviation
post SHB indistinguishable from zero.
Figure 21a illustrate male and female average hourly wages in male dominated
industries compared to their synthetic counterpart. For both sexes, the synthetic
California matches actual California in both levels and trends before the SHB.
After the SHB, female hourly wage in male dominated industries increase relative
to its synthetic counterpart. Male hourly wage in male dominated industries
decrease slightly relative to its synthetic counterpart. Table 14 provides the point
estimates and the permutation based p-values in brackets. Figures 21b and 21c
illustrate the gap between actual California’s average weekly earnings and its
synthetic counterpart vs the placebo states. For females, The deviation post SHB
is among the largest of the placebo states. This combined with a relatively good
pretreatment fit results in a small p-value. The male deviation post SHB is well
63
FIGURE 19.
Average Weekly Hours Worked by Gender Within Male
Dominated Industries
(a) Average Weekly Hours Worked by Gender
Actual CA Synthetic CA
SHB
41
40
Male
39
Female
38
37
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hours Worked
Actual California - Synthetic California vs Placebo States
SHB
2 Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hours Worked
Actual California - Synthetic California vs Placebo States
SHB
2 Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
64
Gap Gap Average Weekly Hours Worked 
FIGURE 20.
Average Hourly Wage by Gender Within Female
Dominated Industries
(a) Average Hourly Wage by Gender
SHB
Actual CA Synthetic CA
19
18
Male
17
16
Female
15
14
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hourly Wage
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hourly Wage
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
0.5
0.0
−0.5
−1.0
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
65
Gap Gap Average Hourly Wage
within the deviations of the placebo states and thus is not distinguishable from
zero.
The above analysis informs which industries are contributing to the
statewide increase in the earnings ratio. Within female dominated industries, the
improvement in the earnings ratio is smaller than at the state level. This result is
driven by a smaller decrease for females than males in the level of weekly earnings.
Wages slightly increase for females and decrease for males. This combined with
a larger decrease in hours worked by males than by females is consistent with
the changes in weekly earnings by sex in female dominated industries referenced
above. Within male dominated industries, the increase in the earnings ratio is much
larger than the state level. This is driven by a larger increase in weekly earnings
for females than for males. The changes in weekly earnings are driven by the joint
effect of increased wages and hours for females and an increase in hours that off-set
a slight decrease in wages for males.
By NAICS industries
The North American Industry Classification System (NAICS) is a slightly
more common way to define industry splits. For this reason I repeat the analysis
above for goods producing and service providing industries classified according to
the (NAICS) codes included in the CPS. Goods producing industries are a subset of
male dominated industries, while service producing industries include both female
and male dominated industries. Figure 22 illustrates the earnings ratio and its
synthetic counterpart for goods producing and service providing industries. In the
goods producing industries, the synthetic California matches the actual California
earnings in levels and trends almost perfectly. The service providing industries
66
FIGURE 21.
Average Hourly Wage by Gender Within Male
Dominated Industries
(a) Average Hourly Wage by Gender
SHB
Actual CA Synthetic CA
20
Male
18
16
Female
14
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hourly Wage
Actual California - Synthetic California vs Placebo States
2
SHB
Control States CA
1
0
−1
−2
−3
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hourly Wage
Actual California - Synthetic California vs Placebo States
2 SHB
Control States CA
1
0
−1
−2
−3
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
67
Gap Gap Average Hourly Wage
also provide a decent, but not as precise match in levels and trends of the female
to male earnings ratio. The point estimates and permutation based p-values are
reported in Table 12. Figure 23 illustrates the precision of these estimates. The
almost exact match pre SHB and slight deviation post SHB for goods producing
industries result in a large MSPE ratio and relatively small p-value. The service
providing industry has a slightly noisier match. It has a considerable deviation
relative to its synthetic counterpart amongst the placebo states which results in a
small p-value.
The effect of the SHB becomes increasingly larger as populations decrease in
size. The earnings ratio increases at the state level after the SHB. Within male
dominated industries, a subset of the statewide population, the earnings ratio
increases by a larger amount. Within goods producing industries, a subset of male
dominated industries, the increase in the earnings ratio is larger yet. These results
suggest the effects of the SHB are not uniform across subsets of the statewide
population. Rather, they are largest amongst goods producing industries, all of
which are composed by 50 % or more male workers.
By Age
One argument for SHBs is their potential to eliminate path dependence. The
length of compensation history will vary by an individual’s time spent in the labor
force. For this reason, I investigate the effect of the SHB on different age groups. I
split the population at age 35.
Figure 24 plots the average weekly earnings ratio by age. For individuals
younger than 35, the synthetic California matches the actual California earnings
ratio in levels, but not trends. The variation in the data causes the synthetic
68
FIGURE 22.
Average Weekly Earnings Ratio by Industry Type
(a) Goods Producing Industries
SHB
1.0
0.9
California
0.8 Synthetic
California
0.7
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019
year
Notes: This figure shows the average weekly earnings ratio in industries that are classified by NAICS as goods producing.
(b) Service Providing Industries
SHB
0.81
California
0.78
Synthetic
California
0.75
0.72
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018 2019
year
Notes: This figure shows the average weekly earnings ratio in industries that are classified by NAICS as service providing.
control approach to construct a poor match. After the SHB, the actual earnings
ratio increases by more than its synthetic counterpart. The permutation based p-
values suggest that this observed deviation is due to statistical noise, and there is
little evidence supporting an actual causal deviation.
69
Average Weekly Earnings Ratio Average Weekly Earnings Ratio
FIGURE 23.
Actual California - Synthetic California vs Placebo States by
Industry Type
(a) Goods Producing Industries
SHB
Control States CA
0.0
−0.2
−0.4
−0.6
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Service Providing Industries
SHB
Control States CA
0.1
0.0
−0.1
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
For individuals older than 35, the synthetic group closely mirrors actual
California in both trends and levels from 2006-2017. After treatment, the actual
California earnings ratio increases relative to its synthetic counterpart. The
point estimates and permutation based p-values are included in Table 12. Figure
25 illustrates the precision of the estimates. For individuals older than 35 the
70
Gap Gap
FIGURE 24.
Average Weekly Earnings Ratio by Age
(a) Younger Than 35
SHB
Actual CA Synthetic CA
0.90
0.86
0.82
0.78
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
Notes: This figure shows the average weekly earnings ratio in California among individuals younger than 35 relative to its synthetic
counterpart
(b) Older Than 35
0.800 SHB
Actual CA Synthetic CA
0.775
0.750
0.725
0.700
0.675
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
Notes: This figure shows the average weekly earnings ratio in California among individuals older than 35 relative to its synthetic
counterpart.
California earnings ratio is matched well by its synthetic counterpart prior to
the SHB. After the SHB the deviation is among the largest of the placebo states,
resulting in a large MSPE ratio and small p-value.
71
Average Weekly Earnings Ratio Average Weekly Earnings Ratio
FIGURE 25.
Actual California - Synthetic California vs Placebo States by Age
(a) Younger Than 35.
0.15 SHB
Control States CA
0.10
0.05
0.00
−0.05
−0.10
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Older Than 35
SHB
Control States CA
0.05
0.00
−0.05
−0.10
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
Weekly Earnings, Hours Worked, and Wages by Sex and Age
The earnings ratio within industries could change if there is a disproportional
change in the level of either male or female earnings within age groups. Changes in
earnings could be a result of changes in wages or changes in hours worked. For
72
Gap Gap
these reasons, I investigate average weekly earnings, hours worked, and hourly
wages by gender within old and young age groups.
Figure 26a illustrates male and female average weekly earnings for individuals
younger than 35 compared to their synthetic counterpart. For both sexes, the
synthetic California matches actual California earnings in both levels and trends
before the SHB. After the SHB, female earnings in female dominated industries
continue to match their synthetic counterpart. Male earnings in female dominated
industries deviate slightly below their synthetic counterpart. Table 13 provides
the point estimates and the permutation based p-values in brackets. The p-values
for both male and female earnings within female dominated industries indicate
that the point estimates are not statistically different from zero. Figures 26b and
26c illustrate the gap between actual California average weekly earnings and their
synthetic counterpart vs the placebo states. For both females and males, post SHB
deviations lie well within deviations of the placebo states.
Figure 27a illustrates male and female average weekly earnings for individuals
older than 35 compared to their synthetic counterpart. Again, for both sexes, the
synthetic California matches actual California earnings in both levels and trends
before the SHB. After the SHB, male earnings among individuals older than 35
deviate slightly below their synthetic counterpart while female earnings increase
slightly relative to their synthetic counterpart. Table 13 reports the point estimates
and permutation based p-values in brackets. Figures 27b and 27c illustrate the gap
between California weekly earnings among individuals above 35 and their synthetic
counterpart vs the placebo states.
Figure 28a illustrates male and female average weekly hours worked among
individuals below age 35 compared to their synthetic counterpart. For both sexes,
73
FIGURE 26.
Average Weekly Earnings by Gender Among Individuals Below Age 35
(a) Average Weekly Earnings by Gender
900 SHB
Actual CA Synthetic CA
800
Male
700
Female
600
500
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Weekly Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
−400
−500
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Weekly Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
−400
−500
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
74
Gap Gap Average Weekly Earnings Ratio
FIGURE 27.
Average Weekly Earnings by Gender Among Individuals Above Age 35
(a) Average Weekly Earnings by Gender
1400
SHB
Actual CA Synthetic CA
Male
1200
1000
Female
800
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Weekly Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
−400
−500
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Weekly Earnings
Actual California - Synthetic California vs Placebo States
100 SHB
Control States CA
0
−100
−200
−300
−400
−500
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
75
Gap Gap Average Weekly Earnings Ratio
the synthetic California matches actual California hours worked in both levels and
trends before the SHB. After the SHB, female hours worked continue to match
their synthetic counterpart. Male hours worked continue on the same trajectory,
but the synthetic counterpart increases after the SHB. Table 13 provides the
point estimates and the permutation based p-values in brackets. Figures 28b and
28c illustrate statistical precision of the point estimates. They show the the gap
between California average weekly hours worked and its synthetic counterpart vs
the placebo states.
Figure 29a illustrates male and female average weekly hours worked among
individuals above age 35 compared to their synthetic counterpart. For both sexes,
the synthetic California matches actual California hours worked in both levels
and trends before the SHB. After the SHB, female hours worked increase slightly
relative to their synthetic counterpart. Male hours decrease slightly relative to
their synthetic counterpart after the SHB. Table 13 provides the point estimates
and the permutation based p-values in brackets. Figures 29b and 29c illustrate
statistical precision of the point estimates. They show the gap between actual
California average weekly hours worked and its synthetic counterpart vs the
placebo states. Noticeably, for both males and females, the deviation from the
synthetic counterpart is well within the deviations among placebo states.
Figure 30a illustrates male and female average hourly wage among individuals
below age 35 compared to their synthetic counterpart. For both sexes, the synthetic
California matches actual California average hourly wages in both levels and trends
before the SHB. After the SHB, female average hourly wage among individuals
below age 35 increases relative to their synthetic counterpart. Male average hourly
wage among individuals below age 35 decreases slightly relative to their synthetic
76
FIGURE 28.
Average Weekly Hours Worked by Gender Among Individuals Below 35
(a) Average Weekly Hours Worked by Gender
38 SHB
Actual CA Synthetic CA
36
Male
34
Female
32
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hours Worked
Actual California - Synthetic California vs Placebo States
4 SHB
Control States CA
2
0
−2
−4
−6
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hours Worked
Actual California - Synthetic California vs Placebo States
4 SHB
Control States CA
2
0
−2
−4
−6
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
77
Gap Gap Average Weekly Hours 
FIGURE 29.
Average Weekly Hours Worked by Gender Among Individuals Above 35
(a) Average Weekly Hours Worked by Gender
SHB
Actual CA Synthetic CA
40
Male
38
36 Female
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hours Worked
Actual California - Synthetic California vs Placebo States
4 SHB
Control States CA
2
0
−2
−4
−6
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hours Worked
Actual California - Synthetic California vs Placebo States
4 SHB
Control States CA
2
0
−2
−4
−6
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
78
Gap Gap Average Weekly Hours 
counterpart. Table 14 provides the point estimates and the permutation based p-
values in brackets. Figures 30b and 30c illustrate the the statistical precision of
these point estimates. They show the gap between actual California average hourly
wages and their synthetic counterpart vs the placebo states. Deviations from their
synthetic counterpart for both sexes post SHB are well within the deviations of the
placebo states and thus is not distinguishable from zero.
Figure 31a illustrates male and female average hourly wage among individuals
above age 35 compared to their synthetic counterpart. For both sexes, the synthetic
California matches actual California average hourly wage in both levels and trends
before the SHB. After the SHB, female average hourly wage among individuals
above age 35 increases relative to their synthetic counterpart. Male average
hourly wage among individuals above age 35 decreases relative to their synthetic
counterpart. Table 14 provides the point estimates and the permutation based
p-values in brackets. Figures 30b and 30c illustrate the the statistical precision
of these point estimates. They show the gap between California average hourly
wages and their synthetic counterpart vs the placebo states. Deviations from their
synthetic counterpart for both sexes post SHB are well within the deviations of the
placebo states and thus are not distinguishable from zero.
The above analysis suggests the increase in the earnings ratio among
individuals above age 35 is driven by the joint increase in female earnings and
decrease in male earnings. The increase in female earnings is likely a result of
females increasing average hours worked per week.
79
FIGURE 30.
Average Hourly Wage by Gender Among Individuals Below 35
(a) Average Hourly Wage by Gender
17 SHB
Actual CA Synthetic CA
16
15
Male
14
13
Female
12
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hourly Wage
Actual California - Synthetic California vs Placebo States
SHB
Control States CA
1
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hourly Wage
Actual California - Synthetic California vs Placebo States
SHB
1 Control States CA
0
−1
−2
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
80
Gap Gap Average Hourly Wage
FIGURE 31.
Average Hourly Wage by Gender Among Individuals Above Age 35
(a) Average Hourly Wage by Gender
SHB
Actual CA Synthetic CA
22
Male
20
18
Female
16
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Hourly Wage
Actual California - Synthetic California vs Placebo States
2
SHB
Control States CA
0
−2
−4
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(c) Female Hourly Wage
Actual California - Synthetic California vs Placebo States
SHB
1.0 Control States CA
0.5
0.0
−0.5
−1.0
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
81
Gap Gap Average Hourly Wage
Employment Probabilities
The above effects in earnings and wages could be driven by systematic
entrance to or exit from the labor market as a result of the SHB. With this in
mind, I consider the effect of SHB policies on the probability that individuals are
employed. I calculate employment probabilities
Figure 32 plots the probability of employment in California against its
synthetic counterpart for both females and males. The synthetic control approach
matches actual California employment probabilities in both levels and trends
with almost no deviation. Female employment probability does not deviate
from its synthetic counterpart after the SHB. Male employment probability
increases slightly relative to its synthetic counterpart after the SHB. Neither of
these deviations are statistically different from zero. Table 15 contains the point
estimates and permutation based p-values in brackets. Figure 33 illustrates the
statistical precision of the point estimates reported in Table 15. Both male and
female employment probabilities fit their synthetic counterpart reasonably well
before and after the SHB. I also calculate the change in employment probability
within male and female dominated industries. Within both of these industries,
the change in employment probability after the SHB is small and statistically
indistinguishable from zero.
The implications of the employment probability findings are two fold. The
SHB does not appear to be causing systematic entrance to or exit from the
California labor market for either males or females; more specifically, within the
labor markets of male dominated and female dominated industries, there does not
appear to be systematic entrance or exit of either males or females. The observed
82
TABLE 15.
Change in Employment Probability by Sex and Industry
Level Data Demeaned Data
State-Wide
Female Male Female Male
SHB 0.0069 0.0004 -0.0462 0.0004
P-Value [0.163] [0.816] [0.571] [1.000]
Male Dominated industries
Female Male Female Male
SHB -0.0046 0.0086** 0.0023 0.0088**
P-Value [0.102] [0.041] [0.918] [0.020]
Female Dominated Industries
Female Male Female Male
SHB 0.0048 -0.0076 -0.0527 -0.0253
P-Value [0.796] [0.245] [0.653] [0.510]
FIGURE 32.
Employment Probabilities by Sex
SHB
0.70 Actual CA Synthetic CA
0.65
0.60
Male
0.55
Female
0.50
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
83
Employemnt Probability
FIGURE 33.
Actual California - Synthetic California vs Placebo States by Sex
(a) Female Employment Probability
SHB
Control States CA
0.04
0.00
−0.04
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
(b) Male Employment Probability
SHB
Control States CA
0.04
0.00
−0.04
2006 2007 2008 2009 2010 2011 2012 2013 2014 2015 2016 2017 2018
year
change in female to male earnings ratio after implementation of the SHB is likely
driven by the SHB’s impact on earnings, hours worked, and wages of individuals
participating in the labor market before the SHB. Turnover within the labor market
is likely driving the results observed at the state level.
84
Gap Gap
If a subset of the population is driving results via turnover, the results must
be larger for that subset of the population. According to the North America Mercer
Turnover Survey, US companies had an average 22 percent turnover rate. With a
turnover rate of 22 percent the change in the earnings ratio must be about 5 times
as large as the state wide estimates among those who are turning over. I am unable
to obtain a reliable measure of turnover from the CPS. The Quarterly Workforce
Indicators (QWI) are quarterly administrative data which include variables such as
total separation, total new hires, earnings of new hires by race age and sex. These
data are published with a lag of multiple quarters. The most recent publication of
the QWI suggests that statewide new hire rate for 2017 quarter 4 was roughly 10
percent. As QWI data are published, my results will be updated.
Robustness
I explore the sensitivity of my results to changes in the model specification. I
replicate Table 12 using multiple model specifications.
In my baseline specification, I use levels of the data reported in the CPS.
Synthetic control results can be sensitive to how the data are treated. For this
reason I replicate Table 12 using demeaned data. I demean the data for each
state by subtracting the pretreatment mean from the entire time series. The
synthetic control approach chooses donor states by matching on pretreatment
levels and trends. Demeaning the data allows the synthetic control approach to
choose donors by matching on variation only. Column 2 of Table 16 reports my
results using demeaned data. I include my baseline results in Column 1 of Table
16, previously reported in Table 12, for ease of comparison. The magnitude and
statistical precision moving from column one to column two remain relatively
85
stable. One exception is within good producing industries, where the demeaned
estimates are less than half the size of the level estimates. This is likely due to
synthetic California having a donor which matches levels well, but not trends. The
result is a synthetic California with a higher predicted earnings ratio than in Figure
22.
Another possible way to scale the data is to divide the whole time series by
the pretreatment mean for each state. Column 3 of Table 16 reports estimates
produced using scaled data. The scaled data produces estimates similar in
magnitude and statistical significance to Columns 1 and 2.
California is one of a few treated states that exist in the data. New York
and Delaware also adopted SHBs around a similar time. The synthetic control
approach is not able to create a synthetic counterpart that matches the actual
data reasonably well for either of these states. I offer an alternative where I pool
data across the three states and treat them as one state. I pool observations
from California, Delaware, and New York using the micro level data. I replicate
the analysis in Table 12 using pooled data from all three states. The sampling
frequency of each state is population adjusted; the pooled data are roughly 60%
California, 30% New York, and, 10% Delaware. The pooled estimates are reported
in Column 4 of Table 16. The magnitude and statistical precision of the pooled
point estimates are consistent with the baseline specification.
As a final test of model sensitivity, I replicate Table 16 in Table 17 using the
replication weights provided by the CPS. The replication weights can be used for
creating a representative sample. Across the two tables the point estimates are
consistent in magnitude and statistical precision.
86
TABLE 16.
Robustness
(2) (3) (4)
(1)
Demeaned Scaled Pooled
Baseline
Data Data Data
State-Wide
SHB 0.0303** 0.0232** 0.0301** 0.0218**
P-Value [0.020] [0.020] [0.020] [0.020]
Younger Than 35
SHB 0.0115 -0.0109 -0.0140 0.0138
P-Value [0.694] [0.367] [0.327] [0.449]
Older Than 35
SHB 0.0256** 0.0129** 0.0170** 0.021**
P-Value [0.020] [0.020] [0.020] [0.041]
Female Dominated Industries
SHB 0.0084 0.0078 0.0102 0.0084
P-Value [0.429] [0.245] [0.224] [0.490]
Male Dominated Industries
SHB 0.0419 0.0283 0.0329* 0.042
P-Value [0.102] [0.102] [0.061] [0.102]
Goods Producing Industries
SHB 0.0539** 0.0288** 0.0298** 0.0103
P-Value [0.020] [0.020] [0.020] [0.245]
Service Providing Industries
SHB 0.0280** 0.0211** 0.0215** 0.018**
P-Value [0.020] [0.041] [0.041] [0.020]
Table notes:
Column (1) reports my baseline estimates
Column (2) reports estimates using data that has been demeaned by its pretreatment mean for each state
Column (3) reports estimates using data that has been scaled by its pretreatment mean for each state
Column (4) reports estimates using pooled data from California, New York, and, Delaware.
87
TABLE 17.
Robustness Using CPS Replicate Weights
(2) (3) (4)
(1)
Demeaned Scaled Pooled
Baseline
Data Data Data
State-Wide
SHB 0.0218* 0.0169** 0.0228** 0.0136
P-Value [0.061] [0.020] [0.020] [0.102]
Younger Than 35
SHB -0.0039 -0.0195 -0.0270 0.014
P-Value [0.898] [0.265] [0.184] [0.388]
Older Than 35
SHB 0.0223** 0.0160** 0.0209** 0.0209**
P-Value [0.020] [0.020] [0.020] [0.041]
Female Dominated Industries
SHB 0.0030 0.0050 0.0066 -0.0003
P-Value [0.837] [0.571] [0.531] [1.000]
Male Dominated Industries
SHB 0.0370 0.0238 0.0274 0.0426*
P-Value [0.122] [0.102] [0.102] [0.082]
Goods Producing Industries
SHB 0.0757** 0.0457** 0.0342** 0.0391**
P-Value [0.020] [0.020] [0.020] [0.020]
Service Providing Industries
SHB 0.0220** 0.0205** 0.0269** 0.0126*
P-Value [0.020] [0.041] [0.041] [0.082]
Table notes:
Column (2) reports my baseline estimates
Column (2) reports estimates using data that has been demeaned by its pretreatment mean for each state
Column (3) reports estimates using data that has been scaled by its pretreatment mean for each state
Column (4) reports estimates using pooled data from California, New York, and, Delaware.
88
It’s possible that one of the donors or combination of donors to synthetic
California are driving the results I observe. Minard and Waddell (2018) provide a
sensitivity analysis of point estimates to the dispersion of the donor states selected.
Figure 34 illustrates that the point estimates are relatively stable for a wide range
of dispersion requirements for the potential donor states.
FIGURE 34.
Sensitivity Analysis
(a) Dispersion Paremeter ρ
(b) Dispersion Paremeter δ
89
Conculsion
Salary history bans (SHBs) are being implemented in cities and states as a
popular policy to help close the gender wage gap. The intent of these policies is to
remove path dependence in compensation. Removing information from the hiring
process has been shown to unintentionally incentivize statistical discrimination
in other settings. For example, ban the box policies have been shown to increase
statistical discrimination by employers (Henry and Jacobs, 2007; Agan and Starr,
2016; Doleac and Hansen, 2016; Shoag and Veuger, 2016; Starr, 2014).
In this paper, I provide the first evidence of the causal impact of statewide
salary history bans. I find that implementation of a SHB increases female earnings
relative to male earnings. I estimate SHBs cause the state level earnings ratio to
increases by .0298, a 10% decrease in the gender earnings gap. The effect of the
SHB is particularly robust across multiple model specifications, including pooling
three treated states into one state. Based on the trend that existed in the earnings
ratio before the SHB, a 0.0298 increase would have taken 5 or more years.
These results are driven by females earning more relative to males within
male dominated industries. The earnings ratio increases by .0579 in industries
with more than 50% males, a 30% decrease in the gender earnings gap within
male dominated industries. Within male dominated industries, systemic gender
discrimination is more likely to be present. SHBs create one more safeguard
against pay discrimination, and thus have the largest impact where the most pay
discrimination is taking place.
I find no evidence that males or females are systematically entering or exiting
the labor market as a result of the SHB. The observed increase in the earnings ratio
90
is likely driven by changes in earnings among individuals who participated in the
labor market before implementation of the SHB.
Given the recent implementation of SHBs, this paper is limited to identifying
the immediate impacts of SHBs. This paper also only examines one potential
margin (female to male earnings) for pay disparity. Eliminating path dependent
compensation could redress pay disparities across other margins as well. Future
research will shed light on the long run impact of SHBs, as well as the impact of
SHBs on other populations that have historically experienced disparities in pay.
SHB policies were designed with the goal of reducing gender-based pay disparities.
This research on the early effects of California’s SHB shows that this policy has the
intended result of reducing pay inequities experienced by female employees. The
immediate effects of the SHB do not appear to cause an increase in unintended
statistical discrimination toward the population for which the policy was designed
to help, as in similar labor policies such as ban the box. The effects of California’s
SHB on the female to male earnings ratio suggests that SHBs may be an effective
policy for reducing the gender pay gap.
91
CHAPTER III
MARIJUANA LEGALIZATION AND VIOLENT CRIME
This chapter is co-authored with Benjamin Hansen. He developed the initial
question, while I preformed the analysis and programming. Ben wrote up the
introduction, background, and conclusion. I wrote up the data, methods, and
results sections.
Introduction
Marijuana remains a polarized issue in the United States. While a super
majority of the population now supports legalization, much of the population
remains opposed to its legalization. Chief among the concerns are the relationship
between marijuana an crime. Will marijuana legalization encourage harder drug
use? Will marijuana access increase violence or reduce it?
There are many reasons that this question remains a largely unanswered.
Empirically, while marijuana has been legally available for 5 years in Colorado and
Washington, we only recently have observed enough post period data to potentially
have power to detect increases in crime. From a theoretical perspective, marijuana
legalization has ambiguous effects. Many clinical studies on marijuana highlights
that marijuana users are more likely to develop psychosis (Murray et al., 2016).
These effects could be exacerbated in recreational marijuana that has increased
THC potency and lower levels cannabinoils. However, many of these studies feature
small samples, questionable control groups, and self-selection into marijuana
consumption. Furthermore, marijuana consumption is often paired with alcohol
consumption, but often not accounted for in observational studies of psychosis and
92
marijuana. Two recent large scale studies failed find evidence linking marijuana
with psychosis. However, recently Berenson (2019) cited prior evidence on the
correlation between marijuana and psychosis and suggested recreational marijuana
legalization was a significant contributing cause to the uptick homicides observed in
the United States recently.
Even if marijuana does not directly affect violence at all, it could reduce
violence or increase it depending on marijuana’s substituability vs. complementary
with alcohol Pacula and Kilmer (2003); Crost and Guerrero (2012); Mark Anderson
et al. (2013); Wen et al. (2015). Previous research on alcohol suggests assaults and
other impulsive crimes increase notably with legal access to alcohol and the increase
in consumption, especially binge drinking Carpenter and Dobkin (2015); Carpenter
et al. (2016); Hansen and Waddell (2018). Likewise, it could depend on where
individuals get high vs. where they consume alcohol. Consumption in public spaces
could result in more conflict, or perhaps more calls to the police. Given we have
unclear pharmacological evidence on marijuana’s direct effect on violent behavior,
and alcohol and marijuana’s cross-price elasticity remains unsettled, the net effect
of marijuana legalization on violent behavior remains an empirical question.
Prior research has focused on variation in medical marijuana laws,
recreational marijuana laws, and unanticipated city wide dispensary closures.
Chu and Townsend (2019) investigate medical marijuana laws with a difference-
in-difference approach, finding little evidence they shift assaults or homicides.
Gavrilova et al. (2017) investigate the border counties of states that legal medical
marijuana, and find evidence that violent crime decrease. They suggest this could
93
be due to medical marijuana displacing violent drug trafficking organizations.1
Chang and Jacobson (2017) medical marijuana dispensary closures in Los Angeles
lead to moderate increases in localized property crime, likely due to fewer eyes on
the street. Dragone et al. (2019) investigate recreational marijuana legalization in
Washington and Oregon using a border county approach. They find evidence rapes
fell in Washington in the period 2012-2014 following the legalization of marijuana
possessions.
We test marijuana effects on violence using variation in early adopters. This
includes the following states: Colorado (2014), Washington (2014), Oregon (2015),
Alaska (2015), and Nevada (2017). We focus on two approaches. In this paper,
we focus murders and homicides, given those are crimes where reporting concerns
are minimized. First, we estimated a difference in difference approach using the
early adopters as treated states. Following that approach, we estimate a synthetic
control design approach of Abadie et al. (2010) for Colorado and Washington, given
they are the earliest adopters with the most years of follow up data. We focus on
the period of recreational legal access, as this is the time in which retailers sold
marijuana to anyone over the age of 21. We also explicitly avoid border county
comparisons for identification as prior research has suggested considerable cross
border shopping occurred in neighboring regions when recreational stores opened to
the pubic (Hao and Cowan, 2017; Hansen et al., 2017).
The remainder of the paper proceeds as follows. In section 3.2, we discuss
the background of marijuana legalization. In Section 3.3 we review our data and
1It could also be that the increased pressure from legal competition increases violence south of
the border. Lindo and Padilla-Romo (2018) find evidence the increased competition among drug
trafficking organizations lead to more violence in Mexico.
94
methods. In section 3.4, we discuss our results and investigate their robustness. In
Section 3.5, we review the policy implications and conclude.
Background
States had long varied in how they regulated marijuana in the United States.
This changed in 1937 with the Marijuana Tax act which effectively made marijuana
illegal at the federal level. This was re-enforced in 1970 with the Controlled
Substances Act. This law create the common scheduling of drugs in 4 categories
which remains today. Schedule I drugs are those with no known benefit and a
high potential for abuse, while schedule IV drugs are those with minimal risks and
known medical benefits. Marijuana remains scheduled as a class I today, along with
heroin, meth, and MDMA.
State individually began passing their own legislation, often first motivated
by state wide ballot initiatives in the 1990s. California was first with the medical
marijuana. Washington legalized medical marijuana soon thereafter in 1998,
while Colorado did so in 2000. The number of states with medical marijuana has
continued to increase over time.
In November 2012, Washington and Colorado became the first states to
legalize marijuana for recreational use for all adults over 21. Legal sales began on
January 1, 2014 in Colorado, and July 1, 2014 in Washington. Since those two first
states legalized, Alaska (2014), Oregon (2014), Nevada(2016), California (2016),
Vermont, and Maine and Massachusetts (2018). The states law passage and legal
sale dates are provided in Figure 35.
Colorado, Washington, Oregon, Alaska, and Nevada all have legalized
recreational marijuana laws prior to 2017, the end of our data. Because Oregon,
95
FIGURE 35.
Marijuana Laws by State
(a) Legalization Map
Law: Recreational Medical CBD Oil None
(b) Time-line of Legalization
State Rec Law Sales Start
Colorado 2012 Jan 1, 2014
Washington 2012 Jul 8, 2014
Oregon 2014 Oct 1, 2014
Alaska 2014 Oct 29, 2014
Washington DC 2014 No sales
California 2016 Jan 1, 2018
Main 2016 Est. 2020
Nevada 2016 Jul 1,2017
Vermont 2016 Est. 2021
Massachusetts 2016 Nov 20,2018
Alaska and Nevada have only a few years of post-legalization data, we focus on
Colorado, and Washington, both of which started recreational marijuana sales
in 2014. Figure 35 illustrates the medical marijuana, CBD oil, and recreational
marijuana laws in the USA currently.
96
Data and Methods
To study the impacts of Marijuana legalization on homicide, we utilize
data from the Federal Bureau of Investigations Uniform Criminal Reporting
(UCR) program. We use data from the offenses known yearly files, and from the
supplementary homicide report (SHR) files. We obtain these data from 2001 to
2017. The offenses known yearly files provide us with counts of reported murders at
the state level. Every cleared murder and non-negligent manslaughter is recorded at
the agency-month level, then aggregated up to the state-year level. Population data
is then used to create the murder rate per 100,000. Population data come from The
National Cancer Institutes Surveillance, Epidemiology, and End Results Program
(SEER) 2
We also utilize data from the supplementary homicide reports. These data
provide detailed information on criminal homicides reported to the police. From
these data, we are able to construct multiple subsets of homicide: homicides
involving a gun, homicides not involving a gun, homicides where the offender knows
the victim, homicides where the offender does not know the victim, homicides
related to drugs, and homicides related to gang use.
Figures 36a, and 36b plot the murder rate per 100,000 over the 16 year
sample period for both Colorado and Washington against all other states in the
data. Figures 37a, and 37b subtract the pre-treatment mean from each of the
treated states and the average of the non treated states. Figures 37a, and 37b
illustrate that prior to legalization, neither Colorado or Washington move closely
with the average of the rest of the United States. Parallel trends, needed for
2 The SEER data are a modification of the intercensal and vintage 2017 annual estimates
produced by the US Census Bureau’s Population Estimates Program. These data are aggregated
to provide yearly population estimates at the state level.
97
identification in a differences in differences model, do not hold. Figures 38,39,
and 40 illustrate each treated state compared to the average of the rest of the US
demeaned for homicides as reported in the SHR, gun related homicides, and gang
related homicides.
FIGURE 36.
Reported Murders per 100,000 by State
(a) Colorado (b) Washington
10.0 Rec 10.0 Rec
7.5 7.5
5.0 Average of 5.0 Average of
Other States Other States
Colorado
Washington
2.5 2.5
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
FIGURE 37.
Reported Murders per 100,000 by State, Demeaned
(a) Colorado
(b) Washington
1.0 Rec
1.0 Rec
0.5
Average of 0.5 Colorado
Other States Average of
Washington Other States
0.0 0.0
−0.5
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year 2001 2003 2005 2007 2009 2011 2013 2015 2017
year
With this concern in mind, we employ a synthetic control approach following
Abadie et al. (2010). This approach uses a data-driven process to make the
assumption of parallel trends more believable. This method has been used to
study many different policy changes including economics liberalization (Billmeier
and Nannicini, 2013), highway police budget cuts (DeAngelo and Hansen, 2014),
98
Reported Offenses per 100,000 Reported Offenses per 100,000
Reported Offenses per 100,000 Reported Offenses per 100,000
FIGURE 38.
Reported Homicides per 100,000 by State, Demeaned
(a) Colorado
(b) Washington
1.0 Rec
1.0 Rec
0.5 Average of Colorado0.5
Other States Average of
Washington Other States
0.0 0.0
−0.5
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year 2001 2003 2005 2007 2009 2011 2013 2015 2017
year
FIGURE 39.
Reported Gun Homicides per 100,000 by State, Demeaned
(a) Colorado
(b) Washington
0.6
Rec
0.6
Average of Rec Colorado
0.4 Other States Average of
Other States
0.3
0.2 Washington
0.0 0.0
−0.2
−0.3
−0.4
2001 2003 2005 2007 2009 2011 2013 2015 2017
year 2001 2003 2005 2007 2009 2011 2013 2015 2017
year
FIGURE 40.
Reported Gang Homicides per 100,000 by State, Demeaned
(a) Colorado
(b) Washington
Rec
0.10 Rec
0.10
0.05
Average of
Other States
0.05
0.00 Average of
Other States
−0.05
0.00
Colorado
Washington
−0.10
2001 2003 2005 2007 2009 2011 2013 2015 2017
year 2001 2003 2005 2007 2009 2011 2013 2015 2017
year
99
Reported Offenses per 100,000 Reported Offenses per 100,000 Reported Offenses per 100,000
Reported Offenses per 100,000 Reported Offenses per 100,000 Reported Offenses per 100,000
decriminalization of prostitution (Cunningham and Shah, 2017), and increases in
minimum wage (Jardim et al., 2017).
The synthetic control approach aims to construct a counter-factual such that
parallel trends absent treatment is a believable assumption. Consider a outcome of
interest Yit where i represents a state and t represents a year. For a tre∑ated state i,
the synthetic control approach estimates the treatment effect as Y Sit − i=6 j wjYjt
where wj is the weight assigned to unit j. All non treated states are considered
when choosing the weights wj. Weights are usually chosen to minimize the distance
between the treated unit and the synthetic control units for a set of variables
chosen by the researcher. Ferman et al. (2017) show that estimates can be quite
sensitive to the selection of variables chosen by the researcher. For this reason,
we follow the work of Botosaru and Ferman (2019) and match on pre-treatment
outcomes only. Our main specifications use data that has been demeaned by pre-
treatment mean to decrease bias as suggested by Ferman and Pinto (2016).
To conduct hypothesis testing, we follow the placebo based approach
suggested by Abadie et al. (2010). Using the same synthetic control approach, we
estimate a synthetic control for each non treated state. We then compare the ratio
of the mean square prediction error(MSPE), where MSPE is calculated using the
difference between the actual outcome and the synthetic counterpart, before and
after treatment (PostMSPE ) for each non treated state. The MSPE ratio provides a
PreMSPE
metric of post treatment fit relative to pre-treatment fit. A states ranking among
the distribution of MSPE ratios provides and empirical p-value as a permutation
based test.
100
Results
Murder as Reported in the UCR Offenses Known Files
Figure 41a illustrates the murder rate per 100,000 for Colorado and its
synthetic counterpart. The actual murder rate per 100,000 in Colorado is
represented by the green solid line and the synthetic counterpart is represented
by the grey dashed line. Figure 41b illustrates the composition of states chosen to
create synthetic Colorado. States are shaded by their relative contribution. Prior
to treatment, synthetic Colorado matches the direction of deviations from pre-
treatment mean but fails to match the magnitude of the deviations. Colorado is
much higher than its synthetic counterpart in 2004 and much lower in 2010. After
legalization, synthetic Colorado continues along a similar trajectory while actual
Colorado increases relative to synthetic. Figure 41c illustrates that Colorado’s
deviation from its synthetic counterpart is relatively small compared to the
deviations of each non treated state from their own synthetic counterpart. Figure
41d illustrates the distribution of pre MSPE to post MSPE ratio for each state.
Notably, many of the placebo states fall to the right of Colorado, meaning many
other states have larger post-treatment fit to pre-treatment fit ratios. The point
estimate and permutation based p-value corresponding with Figure 41 are in Table
18. Figures 41e, and 41f illustrate synthetic Colorado when moving treatment back
one and two years respectively. This exercise allows us to see how well synthetic
Colorado predicts actual Colorado absent treatment. Notably, with a shorter
window of data, the synthetic control approach does not predict the slight increase
in the murder rate in 2013.
101
TABLE 18.
Syntheic Control Results for Marijuana Legalization
Colorado Washington
(Demeaned) (Level) (Rate) (Demeaned) (Level) (Rate)
UCR Murder
Rec 0.2543 0.0342 3.3712 -0.0037 -0.0817 2.8356
P-Value [0.596] [0.638] [0.404] [0.553]
Homicide
Rec 0.2609 0.2537 3.3004 0.1068 -0.1813 2.7317
P-Value [0.773] [0.841] [0.341] [0.591]
Drug Related Homicide
Rec 0.0711 -0.0814 0.1792 -0.0199 -0.0253 0.2782
P-Value [0.409] [0.477] [0.250] [0.114]
Gang Related Homicide
Rec -0.0213 -0.0213 0.0594 -0.0573 -0.0113 0.1202
P-Value [0.955] [0.932] [0.341] [0.841]
Gun Related Homicide
Rec 0.4372 0.2861 1.924 0.1053 -0.0649 1.5299
P-Value [0.250] [0.273] [0.159] [0.568]
Non-Gun Related Homicide
Rec -0.209 -0.1092 1.3764 0.0815 0.134 1.2018
P-Value [0.841] [0.932] [0.886] [0.568]
Known Offender Homicide
Rec 0.417 0.2883 1.831 0.0564 -0.0288 1.7231
P-Value [0.682] [0.864] [0.455] [0.295]
Unknown Offender Homicide
Rec -0.2121 -0.306 1.4693 -0.1323 -0.1915 1.0086
P-Value [0.841] [0.659] [0.136] [0.205]
Permutation based p-vales are included in brackets. Demeaned data has been demeaned by the pre-treatment mean
for each state.
102
FIGURE 41.
Colorado Synthetic Control for Murder (UCR) Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
1.0 Rec
Actual
0.5 Colorado
0.0
Synthetic
Colorado
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
15 Rec ●LA
Control States Colorado ●WV
●IN
10 15 ●WY
●VT
DE
5 ●●KY
●DC ●CO
10 NM TN
0 ●●●ID ●KS
●MA ●RI
−5 ●SD ●ND
●MS ●AR
5 ●AL ●NJ
−10 ●VA ●OK ●NE ●TX
●UT ●MI ●MT ●GA ●MN ●ME
●HI ●WI ●MD ●AZ ●IA ●NY ●FL
−15 ●NH ●SC ●IL ●CT ●MO ●NC ●CA ●OH ●PA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
1.0 Rec −R 1ec 1.0 Rec − 2 Rec
Actual Actual
0.5 Colorado 0.5 Colorado
0.0 0.0
Synthetic Synthetic
Colorado Colorado
−0.5 −0.5
−1.0 −1.0
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Figure 42a illustrates the murder rate per 100,000 for Washington and its
synthetic counterpart. The actual murder rate per 100,000 in Washington is
represented by the green solid line and the synthetic counterpart is represented
by the grey dashed line. Figure 42b illustrates the composition of states chosen
to create synthetic Washington by shading states by their relative contribution
to synthetic Washington. Prior to treatment, synthetic Washington matches
103
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
both the direction and magnitude of deviations from pre-treatment mean of
actual Washington. After legalization, synthetic Washington continues along
a similar trajectory to actual Washington for 3 years. In the fourth year after
treatment, synthetic Washington deviates below its pre-treatment mean while
synthetic Washington deviates above its pre-treatment mean. Figure 42c illustrates
that Washington’s deviation from its synthetic counterpart is relatively small
compared to the deviations of each non treated state from their own synthetic
counterpart. Figure 42d illustrates the distribution of pre MSPE to post MSPE
ratio for each state illustrated in 42c. Notably, many of the placebo states fall to
the right of Washington, meaning many other states have larger post-treatment
fit to pre-treatment fit ratios. The point estimate and permutation based p-value
corresponding with Figure 42 are in Table 18. Figures 42e, and 42f illustrate
synthetic Washington when moving treatment back one and two years respectively.
This exercise allows us to see how well synthetic Washington predicts actual
Washington absent treatment. Notably, with a shorter window of data, the
synthetic control continues to match actual Washington quite well when using
one less year of pre-treatment data. When treatment is rolled back two years, the
synthetic control method fails to predict the spike in the actual Washington murder
rate in 2012.
Supplementary Homicide Report (SHR) Files
The UCR offenses known files provide only one count of total murders per
state for a given year. The supplementary homicide report (SHR) files provide rich
detail for every homicide in a state-year. Within the SHR, we are able to explore
the sensitivity of our results to different definitions of murder. To avoid bias in
104
FIGURE 42.
Washington Synthetic Control for Murder (UCR) Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
1.0 Rec
0.5
Actual
Washington
0.0
Synthetic
Washington
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
15 Rec ●LA
Control States Washington ●WV
●IN
10 15 ●WY
●VT
DE
5 ●●KY
●DC
10 ●NM ●TN0 ●ID ●KS
●MA ●RI
●SD ND−5 ●
●MS ●AR
5 ●AL ●NJ ●WA
−10 ●VA ●OK ●NE ●TX
●UT ●MI ●MT ●GA ●MN ●ME
●HI ●WI ●MD ●AZ ●IA ●NY ●FL
−15 ●NH ●SC ●IL ●CT ●MO ●NC ●CA ●OH ●PA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
1.0 Rec −R 1ec 1.0 Rec − 2 Rec
0.5 0.5
Actual Actual
Washington Washington
0.0 0.0
Synthetic
Washington Synthetic
Washington
−0.5 −0.5
−1.0 −1.0
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
our estimates, we strip out counts of homicide that were a result of mass shooting
or any incident with 4 or more victims. We consider multiple subsets of total
homicides: homicides involving a gun, homicides not involving a gun, homicides
where the offender knows the victim, homicides where the offender does not know
the victim, homicides related to drugs, and homicides related to gang use.
105
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
Total Homicide as Reported in the SHR
Figure 43a illustrates the homicide rate per 100,000 for Colorado and its
synthetic counterpart. The actual homicide rate per 100,000 in Colorado is
represented by the green solid line and the synthetic Colorado is represented by
the grey dashed line. Figure 43b illustrates the composition of states chosen to
create synthetic Colorado by shading states by their relative contribution. Prior
to treatment, synthetic Colorado matches the direction of deviations from pre-
treatment mean but fails to match the magnitude of the deviations. Colorado is
much higher than its synthetic counterpart in 2004 and much lower in 2010. After
legalization, synthetic Colorado continues along a similar trajectory while actual
Colorado increases relative to synthetic. Figure 43c illustrates that Colorado’s
deviation from its synthetic counterpart is relatively small compared to the
deviations of each non treated state from their own synthetic counterpart. Figure
43d illustrates the distribution of pre MSPE to post MSPE ratio for each state.
Notably, many of the placebo states fall to the right of Colorado, meaning many
other states have larger post-treatment fit to pre-treatment fit ratios. The point
estimate and permutation based p-value corresponding with Figure 43 are in Table
18. Figures 43e, and 43f illustrate synthetic Colorado when moving treatment back
one and two years respectively. This exercise allows us to see how well synthetic
Colorado predicts actual Colorado absent treatment. Notably, with a shorter
window of data, the synthetic control approach does not predict the slight increase
in the homicide rate in 2013.
Figure 44a illustrates the homicide rate per 100,000 for Washington and its
synthetic counterpart. The actual homicide rate per 100,000 in Washington is
represented by the green solid line and the synthetic Washington is represented
106
FIGURE 43.
Colorado Synthetic Control for Homicide Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
1.0 Rec
Actual
0.5 Colorado
0.0
Synthetic
Colorado
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●CO
Control States Colorado ●NE
●KY2 ●SC
12 ●WV ●AR
●KS ●HI
●WY ●LA
●MA ●ND
0 8 ●TN ●SD
●VA ●MT
●DE ●OK
●VT ●MD
−2 4 ●NH ●GA ●MI
●NM ●WI ●MS ●AZ ●IA
●IN ●ID ●CA ●CT ●MN ●OH
●UT ●NC ●RI ●MO ●NJ ●IL ●ME ●TX ●NY ●PA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
1.0 Rec −R 1ec 1.0 Rec − 2 Rec
Actual Actual
0.5 Colorado 0.5 Colorado
0.0 0.0
−0.5 −0.5
Synthetic Synthetic
−1.0 Colorado −1.0 Colorado
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
by the grey dashed line. Figure 44b illustrates the composition of states chosen
to create synthetic Washington by shading states by their relative contribution to
synthetic Washington. Prior to treatment, synthetic Washington matches both the
direction and magnitude of deviations from pre-treatment mean. After legalization,
synthetic Washington deviates from actual Washington. Figure 44c illustrates that
Washington’s deviation from its synthetic counterpart is relatively small compared
107
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
to the deviations of each non treated state from their own synthetic counterpart.
Figure 44d illustrates the distribution of pre MSPE to post MSPE for each state.
Notably, many of the placebo states fall to the right of Washington, meaning
Washington has one of the smallest post-treatment fit to pre-treatment fit ratios.
The point estimate and permutation based p-value corresponding with Figure 44
are in Table 18. Figures 44e, and 44f illustrate synthetic Washington when moving
treatment back one and two years respectively. This exercise allows us to see how
well synthetic Washington predicts actual Washington absent treatment. Notably,
with a shorter window of data, the synthetic control continues to match actual
Washington quite well when using one and two years less pre-treatment data. The
synthetic control approach does an arguably good job at predicting deviations from
pre-treatment mean of the actual homicide rate for Washington for 2012 and 2013.
After 2013, synthetic Washington begins to deviate from actual Washington.
Total Drug Related Homicide Reported in the SHR
Figure 45a illustrates the drug related homicide rate per 100,000 for Colorado
and its synthetic counterpart. The actual drug related homicide rate per 100,000
in Colorado is represented by the green solid line and the synthetic Colorado is
represented by the grey dashed line. Figure 45b illustrates the composition of
states chosen to create synthetic Colorado by shading states by their relative
contribution. Prior to treatment, synthetic Colorado matches the direction and
magnitude of deviations from pre-treatment. After legalization, synthetic Colorado
continues along a similar trajectory while actual Colorado increases relative to
synthetic. Figure 46c illustrates that Washington’s deviation from its synthetic
counterpart is relatively small compared to the deviations of each non treated
108
FIGURE 44.
Washington Synthetic Control for Homicide Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
1.0 Rec
0.5
Actual
Washington
0.0
Synthetic
Washington
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●NE
Control States Washington ●KY ●SC
●WV ●AR2
●KS ●HI
10 ●WY ●LA
●MA ●ND
0 ●TN ●SD
●VA ●MT
●DE ●OK
5 ●VT ●MD ●WA
−2 ●NH ●GA ●MI
●NM ●WI ●MS ●AZ ●IA
●IN ●ID ●CA ●CT ●MN ●OH
●UT ●NC ●RI ●MO ●NJ ●IL ●ME ●TX ●NY ●PA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
1.0 Rec −R 1ec 1.0 Rec − 2 Rec
0.5 0.5
Actual Actual
Washington Washington
0.0 0.0
Synthetic
Synthetic Washington
Washington
−0.5 −0.5
−1.0 −1.0
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
state from their own synthetic counterpart. Figure 45d illustrates the distribution
of pre MSPE to post MSPE ratio for each state. Notably, many of the placebo
states fall to the right of Colorado, meaning many other states have larger post-
treatment fit to pre-treatment fit ratios. The point estimate and permutation based
p-value corresponding with Figure 45 are reported in Table 18. Figures 45e, and
45f illustrate synthetic Colorado when moving treatment back one and two years
109
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
respectively. This exercise allows us to see how well synthetic Colorado predicts
actual Colorado absent treatment. Notably, with a shorter window of data, the
synthetic control approach creates a similar counter-factual as with the full window
of pre-treatment data.
FIGURE 45.
Colorado Synthetic Control for Drug Related Homicide Reported,
Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
Rec
0.2
Synthetic
Colorado
0.0 Actual
Colorado
−0.2
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
0.4 Rec 16 ●LA
Control States Colorado ●SC
0.2 ●NE
●NY
12 ●MS
0.0 ●MN
●WI ●MD
●GA ND−0.2 ●
8 ●IL ●SD
●AZ ●AR
−0.4 ●NM ●KY ●CO
●VT ●KS ●IN
−0.6 4 ●MI ●ID ●NC
●RI ●WY ●CA
●HI ●TN ●DE ●WV ●UT ●OH
−0.8 ●ME ●CT ●MO ●VA ●OK ●NJ ●PA ●MT ●IA ●TX ●NH ●MA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
0.3 0.3
0.2 0.2
0.1 Synthetic 0.1 Synthetic
Colorado Colorado
0.0 Actual 0.0 Actual
Colorado Colorado
−0.1 −0.1
−0.2 −0.2
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Figure 46a illustrates the drug related homicide rate per 100,000 for
Washington and its synthetic counterpart. The actual drug related homicide rate
110
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
per 100,000 in Washington is represented by the green solid line and the synthetic
Washington is represented by the grey dashed line. Figure 46b illustrates the
composition of states chosen to create synthetic Washington by shading states by
their relative contribution to synthetic Washington. Prior to treatment, synthetic
Washington matches both the direction and magnitude of deviations from pre-
treatment mean. After legalization, synthetic Washington increases relative to
actual Washington. Figure 46c illustrates that Washington’s deviation from
its synthetic counterpart is relatively small compared to the deviations from
their synthetic counterpart of each non treated state. Figure 46d illustrates the
distribution of pre MSPE to post MSPE for each state. Notably, many of the
placebo states fall to the right of Washington, meaning Washington has one of
the smallest post-treatment fit to pre-treatment fit ratios. The point estimate and
permutation based p-value corresponding with Figure 46 are reported in Table 18.
Figures 46e, and 46f illustrate synthetic Washington when moving treatment back
one and two years respectively. This exercise allows us to see how well synthetic
Washington predicts actual Washington absent treatment. Notably, with a shorter
window of data, the synthetic control continues to match actual Washington up to
2014 quite well when using one and two years less pre-treatment data. After 2014,
we see a similar increase in the synthetic control that is seen when using the full
treatment window.
Total Gang Related Homicide Reported in the SHR
Figure 47a illustrates the gang related homicide rate per 100,000 for Colorado
and its synthetic counterpart. The actual gang related homicide rate per 100,000
in Colorado is represented by the green solid line and the synthetic Colorado is
111
FIGURE 46.
Washington Synthetic Control for Drug Related Homicide Reported,
Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
Rec
0.2
Synthetic
0.0 Washington
Actual
−0.2 Washington
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
0.4 Rec 16 ●LA
Control States Washington ●SC
NE
0.2 ●
●NY
12 ●MS
0.0 ●MN
●WI ●MD
GA
−0.2 ●●ND
8 ●IL ●SD
●AZ ●AR
−0.4 ●NM ●KY
●VT ●KS ●IN
−0.6 4 ●MI ●ID ●NC
●RI ●WY ●CA
●HI ●TN ●DE ●WV ●WA ●UT ●OH
−0.8 ●ME ●CT ●MO ●VA ●OK ●NJ ●PA ●MT ●IA ●TX ●NH ●MA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
0.3 0.3
0.2 0.2
0.1 Synthetic 0.1 Synthetic
Washington Washington
0.0 0.0
−0.1 −0.1
Actual Actual
−0.2 Washington −0.2 Washington
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
represented by the grey dashed line. Figure 47b illustrates the composition of states
chosen to create synthetic Colorado by shading states by their relative contribution.
Prior to treatment, synthetic Colorado matches the direction and magnitude
of deviations from pre-treatment mean. After legalization, synthetic Colorado
continues to match the deviations of actual Colorado. Figure 47c illustrates that
Colorado’s deviation from its synthetic counterpart is relatively small compared
112
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
to the deviations of each non treated state from their own synthetic counterpart.
Figure 47d illustrates the distribution of pre MSPE to post MSPE ratio for each
state. Notably, many of the placebo states fall to the right of Colorado, meaning
many other states have larger post-treatment fit to pre-treatment fit ratios. The
point estimate and permutation based p-value corresponding with Figure 47 are
reported in Table 18. Figures 47e, and 47f illustrate synthetic Colorado when
moving treatment back one and two years respectively. This exercise allows us
to see how well synthetic Colorado predicts actual Colorado absent treatment.
Notably, with a shorter window of data, the synthetic control approach creates a
synthetic Colorado with an in crease in gang related homicides in 2016.
Figure 48a illustrates the gang related homicide rate per 100,000 for
Washington and its synthetic counterpart. The actual gang related homicide rate
per 100,000 in Washington is represented by the green solid line and the synthetic
Washington is represented by the grey dashed line. Figure 48b illustrates the
composition of states chosen to create synthetic Washington by shading states by
their relative contribution to synthetic Washington. Prior to treatment, synthetic
Washington matches both the direction and magnitude of deviations from pre-
treatment mean. After legalization, synthetic Washington increases relative to
actual Washington. Figure 48c illustrates that Washington’s deviation from
its synthetic counterpart is relatively large compared to the deviations from
their synthetic counterpart of each non treated state. Figure 48d illustrates the
distribution of pre MSPE to post MSPE for each state. Notably, many of the
placebo states fall to the left of Washington, meaning Washington has one of
the largest post-treatment fit to pre-treatment fit ratios. The point estimate and
permutation based p-value corresponding with Figure 48 are reported in Table 18.
113
FIGURE 47.
Colorado Synthetic Control for Gang Related Homicide Reported,
Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
0.8 Rec
0.6
0.4
0.2
Actual
Colorado
0.0 Synthetic
Colorado
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●CO
Control States Colorado ●AZ
0.0 ●AR
15 ●KS ●MN
●DE ●CT
−0.5 ●WI ●IL
●GA ●CA
●NM ●LA
−1.0 10 ●OK ●VA
●MD ●OH
●SC ●KY
−1.5 ●NY ●HI
●TX ●SD
5 ●WV ●MT
−2.0 ●UT ●NE ●MS ●VT
●NC ●MA ●NJ ●WY
●MO ●IN ●TN ●NH ●ME
−2.5 ●ID ●MI ●PA ●RI ●IA ●ND
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
1.0 1.0
0.5 0.5
Synthetic
Synthetic Colorado
Colorado
0.0 Actual 0.0 Actual
Colorado Colorado
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Figures 48e, and 48f illustrate synthetic Washington when moving treatment back
one and two years respectively. This exercise allows us to see how well synthetic
Washington predicts actual Washington absent treatment. Notably, with a shorter
window of data, the synthetic control continues to match actual Washington up
to 2015. After 2015, we see a similar increase in the synthetic control that is seen
when using the full treatment window.
114
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
FIGURE 48.
Washington Synthetic Control for Gang Related Homicide Reported,
Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
0.8 Rec
0.6
Synthetic
Washington
0.4
0.2
0.0
Actual
Washington
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●AZ
Control States Washington ●AR ●WA
0.0 15 ●KS ●MN
●DE ●CT
●WI ●IL
−0.5 ●GA ●CA
●NM ●LA
10
−1.0 ●OK ●VA●MD ●OH
●SC ●KY
−1.5 ●NY ●HI
●TX ●SD
5 ●WV ●MT
−2.0 ●UT ●NE ●MS ●VT
●NC ●MA ●NJ ●WY
●MO ●IN ●TN ●NH ●ME
−2.5 ●ID ●MI ●PA ●RI ●IA ●ND
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
1.0 1.0
Synthetic Synthetic
Washington Washington
0.5 0.5
0.0 0.0
Actual Actual
Washington Washington
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Total Gun Related Homicide Reported in the SHR
Figure 49a illustrates the gun related homicide rate per 100,000 for Colorado
and its synthetic counterpart. The actual gun related homicide rate per 100,000
in Colorado is represented by the green solid line and the synthetic Colorado is
represented by the grey dashed line. Figure 49b illustrates the composition of states
115
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
chosen to create synthetic Colorado by shading states by their relative contribution.
Prior to treatment, synthetic Colorado matches the direction and magnitude of
deviations from pre-treatment mean. After legalization, actual Colorado increases
relative to synthetic Colorado. Figure 49c illustrates that Colorado’s deviation
from its synthetic counterpart is relatively small compared to the deviations of each
non treated state from their own synthetic counterpart. Figure 49d illustrates the
distribution of pre MSPE to post MSPE ratio for each state. Notably, many of the
placebo states fall to the right of Colorado, meaning many other states have larger
post-treatment fit to pre-treatment fit ratios. The point estimate and permutation
based p-value corresponding with Figure 49 are reported in Table 18. Figures
49e, and 49f illustrate synthetic Colorado when moving treatment back one and
two years respectively. This exercise allows us to see how well synthetic Colorado
predicts actual Colorado absent treatment. Notably, with a shorter window of data,
the synthetic control approach creates a similar synthetic Colorado as with the full
pre-treatment window of data.
Figure 50a illustrates the gun related homicide rate per 100,000 for
Washington and its synthetic counterpart. The actual gun related homicide rate
per 100,000 in Washington is represented by the green solid line and the synthetic
Washington is represented by the grey dashed line. Figure 50b illustrates the
composition of states chosen to create synthetic Washington by shading states by
their relative contribution to synthetic Washington. Prior to treatment, synthetic
Washington matches both the direction and magnitude of deviations from pre-
treatment mean. After legalization, synthetic Washington tracks actual Washington
until 2015. In 2015 actual Washington levels off and synthetic Washington
continues to increase. Figure 50c illustrates that Washington’s deviation from
116
FIGURE 49.
Colorado Synthetic Control for Gun Homicide Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
0.8
Rec
Actual
Colorado
0.4
0.0
−0.4 Synthetic
Colorado
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●VT
2 Control States Colorado ●OK
●NE ●ID
1 10 ●WV ●DE
●KS ●MS
0 ●GA ●TN
●WI ●NM
●UT ●MD ●CT
−1 5 ●MT ●AR ●HI
●KY ●VA ●NH ●CO
−2 ●IN ●WY ●SC ●MI
●LA ●NJ ●AZ ●ND ●OH ●NY ●IA
−3 ●NC ●RI ●IL ●SD ●MN ●MO ●CA ●MA ●PA ●TX ●ME
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
1.0 1.0
Actual Actual
0.5 Colorado 0.5 Colorado
0.0 0.0
Synthetic Synthetic
Colorado Colorado
−0.5 −0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
its synthetic counterpart is relatively small compared to the deviations from
their synthetic counterpart of each non treated state. Figure 50d illustrates the
distribution of pre MSPE to post MSPE for each state. Notably, many of the
placebo states fall to the right of Washington, meaning Washington has one of
the smallest post-treatment fit to pre-treatment fit ratios. The point estimate and
permutation based p-value corresponding with figure 50 are reported in Table 18.
117
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
Figures 50e, and 50f illustrate synthetic Washington when moving treatment back
one and two years respectively. This exercise allows us to see how well synthetic
Washington predicts actual Washington absent treatment. Notably, with a shorter
window of data, the synthetic control continues to match actual Washington up
to 2015. After 2015, we see a similar increase in the synthetic control that is seen
when using the full pre-treatment window of data.
FIGURE 50.
Washington Synthetic control for Gun Homicide Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
0.8 Synthetic
Rec Washington
0.4
Actual
Washington
0.0
−0.4
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●VT
2 Control States Washington ●OK
●NE ●ID
1 10 ●WV ●DE
●KS ●MS
●GA ●TN0
●WI ●NM
●UT ●MD ●CT
−1 5 ●MT ●AR ●HI
●KY ●VA ●NH
−2 ●IN ●WY ●SC ●MI
●LA ●NJ ●AZ ●ND ●OH ●NY ●IA
−3 ●NC ●RI ●IL ●SD ●MN ●MO ●CA ●WA ●MA ●PA ●TX ●ME
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
1.0 1.0
Synthetic
Synthetic Washington
Washington
0.5 0.5
Actual Actual
Washington Washington
0.0 0.0
−0.5 −0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
118
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
Total Non-gun Related Homicide Reported in the SHR
Figure 51a illustrates the non-gun related homicide rate per 100,000 for
Colorado and its synthetic counterpart. The actual non-gun related homicide rate
per 100,000 in Colorado is represented by the green solid line and the synthetic
Colorado is represented by the grey dashed line. Figure 51b illustrates the
composition of states chosen to create synthetic Colorado by shading states by their
relative contribution. Prior to treatment, synthetic Colorado matches the direction
of deviations from pre-treatment mean as actual Colorado but fails to match the
magnitude of deviations from pre-treatment mean. After legalization, synthetic
Colorado continues on a similar trend and actual Colorado drops off relative
to synthetic. Figure 51c illustrates that Colorado’s deviation from its synthetic
counterpart is relatively small compared to the deviations of each non treated
state from their own synthetic counterpart. Figure 51d illustrates the distribution
of pre MSPE to post MSPE ratio for each state. Notably, many of the placebo
states fall to the right of Colorado, meaning many other states have larger post-
treatment fit to pre-treatment fit ratios. The point estimate and permutation based
p-value corresponding with Figure 51 are reported in Table 18. Figures 51e, and
51f illustrate synthetic Colorado when moving treatment back one and two years
respectively. This exercise allows us to see how well synthetic Colorado predicts
actual Colorado absent treatment.
Figure 52a illustrates the non-gun related homicide rate per 100,000 for
Washington and its synthetic counterpart. The actual non-gun related homicide
rate per 100,000 in Washington is represented by the green solid line and the
synthetic Washington is represented by the grey dashed line. Figure 52b illustrates
the composition of states chosen to create synthetic Washington by shading
119
FIGURE 51.
Colorado Synthetic Control for Non-gun Homicide Reported,
Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
0.4 Rec
0.2
Synthetic
Colorado
Actual
0.0 Colorado
−0.2
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●CO
Control States Colorado ●IL
1 ●VA
20 ●KY●ND
●●
NE
NH
●IN
0 15 ●PA●MS ●TN
●●
MD ●DE
SC TX
● ●RI ●OK
10 ●CT WY
−1 ● ●VT MA● ●LA ●MN
GA WV
●● ●NJ● ●
NC
5 ME ●AZ●UT ●HI
−2 ●AR OH● ●● ●●
CA
NM IA NY
● ● ● ● ●
SD
KS MO MT MI ●ID ●WI
0
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 30 60 90
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
0.4 Rec −R 1ec 0.4 Rec − 2 Rec
0.2 0.2
Synthetic Synthetic
Colorado Colorado
Actual Actual
0.0 Colorado 0.0 Colorado
−0.2 −0.2
−0.4 −0.4
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
states by their relative contribution to synthetic Washington. Prior to treatment,
synthetic Washington matches direction of deviations from pre-treatment mean
but fails to match the magnitude of deviations. After legalization, synthetic
Washington moves in the same direction as actual Washington but again, with
smaller magnitude. Figure 52c illustrates that Washington’s deviation from
its synthetic counterpart is relatively small compared to the deviations from
120
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
their synthetic counterpart of each non treated state. Figure 52d illustrates the
distribution of pre MSPE to post MSPE for each state. Notably, many of the
placebo states fall to the right of Washington, meaning Washington has one of
the smallest post-treatment fit to pre-treatment fit ratios. The point estimate and
permutation based p-value corresponding with figure 52 are reported in Table 18.
Figures 52e, and 52f illustrate synthetic Washington when moving treatment back
one and two years respectively. This exercise allows us to see how well synthetic
Washington predicts actual Washington absent treatment.
Total Offender Known to Victim Homicide Reported in the SHR
Figure 53a illustrates the offender known to victim homicide rate per 100,000
for Colorado and its synthetic counterpart. The actual offender known to victim
homicide rate per 100,000 in Colorado is represented by the green solid line and the
synthetic Colorado is represented by the grey dashed line. Figure 53b illustrates
the composition of states chosen to create synthetic Colorado by shading states
by their relative contribution. Prior to treatment, synthetic Colorado matches
the general direction of deviations from pre-treatment mean as actual Colorado
but fails to match the magnitude of deviations from pre-treatment mean. After
legalization, synthetic Colorado continues on a similar trend and actual Colorado
increases relative to synthetic. Figure 53c illustrates that Colorado’s deviation
from its synthetic counterpart is relatively small compared to the deviations of each
non treated state from their own synthetic counterpart. Figure 53d illustrates the
distribution of pre MSPE to post MSPE ratio for each state. Notably, many of the
placebo states fall to the right of Colorado, meaning many other states have larger
post-treatment fit to pre-treatment fit ratios. The point estimate and permutation
121
FIGURE 52.
Washington Synthetic Control for Non-gun Homicide Reported,
Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
0.4 Rec
0.2
Actual
0.0 Washington
Synthetic
Washington
−0.2
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
Rec ●WA
Control States Washington ●IL
1 ●VA
20
●●
KY
ND
●NE●NH
IN
0 15 ●●PA●MS● ●
TN
MD DE
● ●SC TX● ●RI ●OK
10 ●CT ●WY
−1 ●VT MA●LA● ●
●
MN
GA ●WV●NJ ●NC
5 ●ME ●AZ●UT ●HI
−2 ●AR ●OH● ●
CA
NM IA NY SD
●KS ●● ● ●MO ●MT ●MI ●ID ●WI
0
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 30 60 90
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
0.4 Rec −R 1ec 0.4 Rec − 2 Rec
0.2 0.2
Actual Actual
0.0 Washington 0.0 Washington
Synthetic
Washington Synthetic
−0.2 −0.2 Washington
−0.4 −0.4
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
based p-value corresponding with Figure 53 are reported in Table 18. Figures
53e, and 53f illustrate synthetic Colorado when moving treatment back one and
two years respectively. This exercise allows us to see how well synthetic Colorado
predicts actual Colorado absent treatment.
Figure 54a illustrates the offender known to victim homicide rate per
100,000 for Washington and its synthetic counterpart. The actual offender
122
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
FIGURE 53.
Colorado Synthetic Control for Homicide with
Known Offender Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
Rec
0.50
0.25
Actual
0.00 Colorado
−0.25
Synthetic
Colorado
−0.50
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
2 Rec ●CO
Control States Colorado ●WY
●VT
●DE
15 ●RI1 ●NC
●UT
●GA
●AR
10 ●WV ●MD
0 ●SC ●MT
●OK ●ND
●NE ●HI ●MI
●KY ●TN ●ME
5 ●IN ●NM ●MS
−1 ●WI ●IA ●MA
●NH ●NY ●MO ●TX
●LA ●SD ●ID ●CT
●VA ●CA ●KS ●NJ ●OH ●IL ●MN ●AZ ●PA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
0.6 0.6
0.4 0.4
0.2 0.2
Actual Actual
0.0 Colorado 0.0 Colorado
−0.2 −0.2
−0.4 −0.4
Synthetic Synthetic
−0.6 Colorado −0.6 Colorado
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
known to victim homicide rate per 100,000 in Washington is represented by
the green solid line and the synthetic Washington is represented by the grey
dashed line. Figure 54b illustrates the composition of states chosen to create
synthetic Washington by shading states by their relative contribution to synthetic
Washington. Prior to treatment, synthetic Washington matches direction of
deviations from pre-treatment mean but fails to match the magnitude of deviations
123
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
in 2012. After legalization, synthetic Washington moves in the same direction as
actual Washington for two years, then actual Washington decreases while synthetic
increases. Figure 54c illustrates that Washington’s deviation from its synthetic
counterpart is relatively small compared to the deviations from their synthetic
counterpart of each non treated state. Figure 54d illustrates the distribution of
pre MSPE to post MSPE for each state. Notably, many of the placebo states fall
to the right of Washington, meaning Washington has one of the smallest post-
treatment fit to pre-treatment fit ratios. The point estimate and permutation based
p-value corresponding with figure 54 are reported in Table 18. Figures 54e, and 54f
illustrate synthetic Washington when moving treatment back one and two years
respectively. This exercise allows us to see how well synthetic Washington predicts
actual Washington absent treatment.
Total Offender Unknown to Victim Homicide Reported in the SHR
Figure 55a illustrates the offender unknown to victim homicide rate per
100,000 for Colorado and its synthetic counterpart. The actual offender unknown
to victim homicide rate per 100,000 in Colorado is represented by the green solid
line and the synthetic Colorado is represented by the grey dashed line. Figure
55b illustrates the composition of states chosen to create synthetic Colorado
by shading states by their relative contribution. Prior to treatment, synthetic
Colorado matches the general direction and magnitude of deviations from pre-
treatment mean as actual Colorado. After legalization, synthetic Colorado increases
but actual Colorado increases by a larger amount. Figure 55c illustrates that
Colorado’s deviation from its synthetic counterpart is relatively small compared
to the deviations of each non treated state from their own synthetic counterpart.
124
FIGURE 54.
Washington Synthetic Control for Homicide with
Known Offender Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
Rec
0.50
0.25
Actual
Washington
0.00
Synthetic
Washington
−0.25
−0.50
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
2 Rec ●WY
Control States Washington ●VT
●DE
15 ●RI
●NC1
●UT
●GA
●AR ●WA
10 ●WV ●MD
0 ●SC ●MT
●OK ●ND
●NE ●HI ●MI
●KY ●TN ●ME
5 ●IN ●NM ●MS
−1 ●WI ●IA ●MA
●NH ●NY ●MO ●TX
●LA ●SD ●ID ●CT
●VA ●CA ●KS ●NJ ●OH ●IL ●MN ●AZ ●PA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
0.6 0.6
0.4 0.4
0.2 0.2
Actual Synthetic
Washington Washington
0.0 Synthetic 0.0 Actual
Washington Washington
−0.2 −0.2
−0.4 −0.4
−0.6 −0.6
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Figure 55d illustrates the distribution of pre MSPE to post MSPE ratio for each
state. Notably, many of the placebo states fall to the right of Colorado, meaning
many other states have larger post-treatment fit to pre-treatment fit ratios. The
point estimate and permutation based p-value corresponding with Figure 55 are
reported in Table 18. Figures 55e, and 55f illustrate synthetic Colorado when
moving treatment back one and two years respectively. This exercise allows us to
125
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
see how well synthetic Colorado predicts actual Colorado absent treatment. When
the pre-treatment window is two years smaller, synthetic Colorado matches actual
Colorado in deviations from mean up to 2017.
FIGURE 55.
Colorado Synthetic Control for Homicide with
Unknown Offender Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
Rec
1.0
Actual
0.5 Colorado
Synthetic
Colorado
0.0
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
2
Rec ●MD
Control States Colorado ●NC
●KY
1 ●WI
15 ●NJ
●OK
●CO ●MN
0 ●LA ●NM
●WY ●SD
10 ●UT ●IN
●AR ●TN
−1 ●VT ●WV
●NE ●VA
●KS ●DE
5 ●MS ●MO
−2 ●HI ●GA ●SC
●CT ●RI ●TX ●MI
●ND ●ME ●NY ●AZ ●MT
●PA ●MA ●IL ●ID ●OH ●CA ●NH ●IA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
Actual Actual
Colorado Colorado
Synthetic Synthetic
0.5 0.5
Colorado Colorado
0.0 0.0
−0.5 −0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Figure 56a illustrates the offender unknown to victim homicide rate per
100,000 for Washington and its synthetic counterpart. The actual offender unknown
to victim homicide rate per 100,000 in Washington is represented by the green solid
126
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
line and the synthetic Washington is represented by the grey dashed line. Figure
56b illustrates the composition of states chosen to create synthetic Washington
by shading states by their relative contribution to synthetic Washington. Prior to
treatment, synthetic Washington matches direction and magnitude of deviations
from pre-treatment mean of actual Washington. After legalization, synthetic
Washington moves in the same direction as actual Washington for two years, then
actual Washington increases while synthetic Washington levels off. Figure 56c
illustrates that Washington’s deviation from its synthetic counterpart is relatively
small compared to the deviations from their synthetic counterpart of each non
treated state. Figure 56d illustrates the distribution of pre MSPE to post MSPE
for each state. Notably, many of the placebo states fall to the right of Washington,
meaning Washington has the fifth largest post-treatment fit to pre-treatment
fit ratios. The point estimate and permutation based p-value corresponding
with figure 56 are reported in Table 18. Figures 56e, and 56f illustrate synthetic
Washington when moving treatment back one and two years respectively. This
exercise allows us to see how well synthetic Washington predicts actual Washington
absent treatment.
Differences in Differences
In addition to synthetic control, we analyze the effects of marijuana
legalization using a differences in differences model. We estimates the following
differences in in differences model.
Rateit = Dit + γt + δi + it
127
FIGURE 56.
Washington Synthetic Control for Homicide with
Unknown Offender Reported, Demeaned
(a) Synthetic versus Actual (b) Contributors to Synthetic Control
Synthetic
Rec
1.0 Washington
0.5
Actual
Washington
0.0
−0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017
year
(c) Placebo Synthetic Controls (d) MSPE Ratio Distribution
2
Rec ●MD
Control States Washington ●NC
●KY
1 ●WI
15 ●NJ
●OK
●MN
0 ●LA ●NM
●WY ●SD
10 ●UT ●IN
●AR ●TN
−1 ●VT ●WV
●NE ●VA
●KS ●DE
5 ●MS ●MO
−2 ●HI ●GA ●SC
●CT ●RI ●TX ●MI
●ND ●ME ●NY ●AZ ●WA ●MT
●PA ●MA ●IL ●ID ●OH ●CA ●NH ●IA
2001 2003 2005 2007 2009 2011 2013 2015 2017 0 50 100 150 200 250
year Post MSPE / Pre MSPE
(e) Cross Validation (f) Cross Validation
Rec −R 1ec Rec − 2 Rec
Synthetic Synthetic
0.5 Washington 0.5 Washington
Actual Actual
Washington Washington
0.0 0.0
−0.5 −0.5
2001 2003 2005 2007 2009 2011 2013 2015 2017 2001 2003 2005 2007 2009 2011 2013 2015 2017
year year
Rateit is the homicide rate per 100,000 people in a given state. Dit is a binary
treatment indicator turning on after a state legalizes marijuana. γt and δi are year
and state fixed effects respectively, and it in an error term. Treated states include
Washington-2014, Colorado-2014, Oregon-2015, Alaska-2015, and Nevada 2017.
Table 19 includes the point estimates for our 8 different definitions of homicide with
the standard errors in parenthesis below each point estimate. Standard errors are
128
Reported Offenses per 100,000 Gap Reported Offenses per 100,000
Reported Offenses per 100,000 count
clustered at the state level. Column 2 of Table 19 includes estimates using the log
of the homicide rate as the dependent variable ln(Rate).
Across all definitions of homicide in column one of Table 19, we fail to reject
the null hypothesis that our point estimates are significantly different from zero.
In column two we find evidence that gang related and non-gun related homicides
slightly decrease after marijuana legalization. For all other definitions of homicide,
we fail to reject the null hypothesis that our point estimates are significantly
different from zero.
Most states did not start legal marijuana sales January 1 of their legalizing
year. For this reason we include a specification that allows for partial treatment.
Legalization and sales start dates can be seen in Figure 35. Table 20 reports the
point estimates where we allow for partial treatment. We specify partial treatment
as follows: Washington-0.5-2014, Colorado-1-2014, Oregon-0.25-2015, Alaska-
0.25-2015, and Nevada-0.5-2017. The point estimates estimated when using a
differences in differences model allowing for partial treatment are consistent with
estimates from a differences in differences model with binary treatment. With the
exception of gang related homicides, we fail to reject the null hypothesis that our
point estimates are significantly different from zero. For gang related homicides, we
find evidence that there may be a slight decrease in homicide rates in marijuana
legalizing states.
Conclusions and Policy Implications
Marijuana policy continues to evolve quickly in the United States and
internationally where legal sales began nationwide in Canada in 2018. While
states have seen some benefits of legalization through increased tax revenue,
129
TABLE 19.
Differences in Differences Results for Marijuana Legalization
Legalizing States
(Level) (Logged) (Rate)
UCR Murder
Rec 0.475 0.001 4.1787
(0.423) (0.007)
Homicide
Rec 0.340 -0.002 4.0729
(0.372) (0.007)
Drug Related Homicide
Rec -0.086 0.011 0.341
(0.071) (0.012)
Gang Related Homicide
Rec -0.057 -0.012*** 0.0924
(0.037) (0.004)
Gun Related Homicide
Rec 0.329 0.003 2.3622
(0.359) (0.013)
Non-Gun Related Homicide
Rec 0.011 -0.010** 1.7107
(0.073) (0.005)
Known Offender Homicide
Rec 0.130 -0.004 2.3614
(0.238) (0.006)
Unknown Offender Homicide
Rec 0.210 0.007 1.7115
(0.150) (0.013)
Differences in differences regressions include the homicide rate
as the the dependent variable, a treatment indicator turning
on after a state legalizes, state fixed effects, and year fixed
effects. Treated states include Washington-2014, Colorado-2014,
Oregon-2015, Alaska-2015, Nevada-2107. Standard errors are
clustered at the state level
130
TABLE 20.
Differences in Differences Results for Marijuana Legalization
Partial Treatment
Legalizing States
(Level) (Logged) (Rate)
UCR Murder
Rec 0.338 -0.000 4.1787
(0.407) (0.007)
Homicide
Rec 0.286 -0.003 4.0729
(0.365) (0.006)
Drug Related Homicide
Rec -0.002 0.013 0.341
(0.072) (0.013)
Gang Related Homicide
Rec -0.066* -0.014*** 0.0924
(0.039) (0.003)
Gun Related Homicide
Rec 0.167 -0.002 2.3622
(0.266) (0.010)
Non-Gun Related Homicide
Rec 0.119 -0.002 1.7107
(0.138) (0.004)
Known Offender Homicide
Rec 0.123 -0.004 2.3614
(0.273) (0.007)
Unknown Offender Homicide
Rec 0.164 0.003 1.7115
(0.123) (0.009)
Differences in differences regressions include the homicide rate
as the the dependent variable, a treatment indicator turning
on after a state legalizes, state fixed effects, and year fixed
effects. Treated states include Washington(0.5)-2014, Colorado-
2014, Oregon(0.25)-2015, Alaska(0.25)-2015, Nevada(0.5)-2017.
Standard errors are clustered at the state level
131
the consequences of legalization remain unknown. Optimal taxes would serve to
potentially offset externalities. If legalization increases homicides, then the external
costs might exceed current revenues given the high social costs associated with
deaths, particularly those of young individuals.
Following marijuana’s legalization, homicides have increased in Colorado
and Washington. What would have happened in the counterfactual is the most
important question as many other factors including policing (Evans and Owens,
2007; Chalfin and McCrary, 2017) punishment , and illegal drug markets Evans
et al. (2018) could have influenced violence as well. To this end, we investigate
marijuana’s legalization and its potential role in the recent nationwide increase in
homicides. We use both difference-in-differences and synthetic control methods. We
fail to reject the null that homicide rates did not shift in Colorado and Washington
in ways that would not be predicted by counterfactual trends.
In our analyses, we investigate both murders (based on the UCR), homicides
(based on the SHR), and a wide variety of sub categories of homicides. While on
average many of our estimates are close to zero, there are some instances where
our point estimates would suggest treatment could have lead to a 10-20 percent
increase in homicides. However, even these cases, we fail to reject the null based on
randomization inference. This suggests homicides have shifted by a large amount
in many parts of the country. This is partly a result of a broader national trend (as
homicide rates have increased by roughly 20 percent since 2013), and because some
as the categories of homicides are split up, they naturally become more rare.
So what has caused in the increased homicides nationally? The question
remains open. Prior research suggests many plausible channels. It could be a result
of the improving economy Ruhm (2000), increases in gun ownership (Depetris-
132
Chauvin, 2015; Levine and McKnight, 2017), emerging illegal drug markets
(Grogger and Willis, 2000; Fryer Jr et al., 2013; Evans et al., 2018), or a “Ferguson
Effect” (Gross and Mann, 2017; Pyrooz et al., 2016). Each of these potential
channels merits attention in future research.
133
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