STATE COLLECTIVE BARGAINING LAWS
AND PUBLIC-SECTOR PAY
ERIC J. BRUNNER AND ANDREW JU*
Using the Public Use Microdata Sample from the 2005 to 2015
American Community Survey, the authors provide new evidence on
how state collective bargaining laws affect public-sector wages. To
isolate the causal effect of bargaining laws on public-sector pay, they
examine wage differentials between otherwise similar public- and
private-sector employees located in the same local labor market.
They estimate difference-in-differences (DD) models that exploit
two sources of plausibly exogenous variation: 1) policy discontinu-
ities along state borders and 2) variation within states in collective
bargaining laws in states where the majority of public workers are
without collective bargaining rights. Findings show that manda-
tory collective bargaining laws increase public-sector wages by
approximately 5 to 8 percentage points. Results therefore suggest
that mandatory collective bargaining laws provide a formal
mechanism through which public-sector workers are able to bar-
gain for increased compensation.
The Great Recession and the ensuing state and local budget deficits that
it prompted have reinvigorated the debate over the rights of public-
sector workers and their unions. Since 2011, state legislators across the
country have introduced bills designed to weaken or eliminate the collective
bargaining (CB) rights of public-sector workers. Most notably, the signing
of Wisconsin Act 10 in 2011, which significantly restricted the CB rights of
public-sector workers, sparked a national debate over public-sector worker
compensation.
Proponents of scaling back or eliminating bargaining rights have argued
that public-sector employees are overpaid, and furthermore, that public-
sector unions exploit their political power to elect pro-union government
officials to control both sides of the bargaining table (Wellington and
Winter 1972; Lewin, Keefe, and Kochan 2012). Opponents argue that
*ERIC J. BRUNNER is a Professor in the Department of Public Policy, University of Connecticut. ANDREW
JUis a PhD student in the Department of Economics, University of Connecticut. All of the data used in
this article and additional results and copies of the computer programs used to generate the results pre-
sented in the article are available from the lead author at eric.brunner@uconn.edu.
KEYWORDs: collective bargaining rights, public–private sector wage differentials, local labor market, com-
pensation, municipal unions
ILR Review, 72(2), March 2019, pp. 480–508
DOI: 10.1177/0019793918808727. ÓThe Author(s) 2018
Journal website: journals.sagepub.com/home/ilr
Article reuse guidelines: sagepub.com/journals-permissions
public-sector workers are underpaid and that collective bargaining is a fun-
damental right.
In this article, we present new evidence on how state CB laws affect
public-sector pay. Using data from the 2005 to 2015 Public Use Microdata
Sample (PUMS) of the American Community Survey (ACS), we estimate
standard log wage regressions that include state and local labor market
fixed effects. In these models, the key explanatory variable is an interaction
term between an indicator for whether an individual is a public-sector
employee and an indicator for whether a state has a mandatory CB law.
The coefficient on this interaction term measures how the public–private
wage differential differs in states that do and do not mandate collective
bargaining.
Isolating the effect of state CB laws on public-employee compensation is
challenging because those laws are likely correlated with other state unob-
servables that influence public-sector compensation. For example, state CB
laws may be correlated with unobserved worker and voter sentiment toward
public-sector unions, implying that voters in states with strong CB rights
might choose to provide higher compensation for public-sector workers
regardless of whether those workers were covered by a CB agreement
(Hirsch, Macpherson, and Winters 2012).
We attempt to address these challenges in several ways. First, rather than
focusing on how state CB laws affect public-employee compensation, as
most of the previous literature has done, we focus on how CB laws affect
the wage differential between otherwise similar public- and private-sector
employees. As noted by Diamond (2017), by comparing wage differentials
between otherwise similar public- and private-sector workers in the same
local labor market, we are able to control for unobserved differences in
labor market conditions as well as differences in the skill sets and compensa-
tion schemes of public- and private-sector workers that may be correlated
with both state CB laws and public-sector pay.
Second, our primary identification strategy exploits policy discontinuities
at state borders to identify the effect of mandatory CB laws on public-sector
wages. Specifically, we focus on workers located in commuting zones (CZs)
that cross state boundaries and estimate models that include CZ-by-public-
sector-employee fixed effects. In these models we are essentially comparing
public- and private-sector wage differentials along state borders within CZs,
where one state within a CZ mandates collective bargaining and the other
state does not. Our identification strategy therefore utilizes only within-CZ
variation in the strength of state CB laws and thus controls for a host of
unobservables that potentially might otherwise bias estimates of the impact
of state CB laws on public-sector wages.
Finally, we examine variation within states in CB laws. Specifically, we
focus on states that generally prohibit collective bargaining and exploit that
several of those states allow collective bargaining for firefighters or police
(or in some cases both). We then estimate models that compare the public-
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 481
and private-sector wage differential in states that authorize police and fire-
fighters to bargain to the public- and private-sector wage differential in
states that prohibit police and firefighters from bargaining.
We find that mandatory CB laws increase public-sector wages by approxi-
mately 5 to 8 percentage points. Drilling down to specific occupations, we
find that mandatory CB laws increase the wages of teachers, police, and fire-
fighters. A series of robustness checks suggests these results are highly
robust. For example, our results persist across specifications that include
occupation fixed effects and therefore compare wage differentials only
among workers in similar occupations. They also persist across specifications
that include additional state-specific local labor market controls for a variety
of factors that might be correlated with mandatory CB laws, such as the pro-
pensity to vote for the Democratic presidential candidate. Finally, based on
a series of falsification tests, we find no evidence that mandatory CB laws
affect the wages of either federal or nonprofit employees, thus providing
further evidence that our results have a causal interpretation.
Previous Research
Our work is most closely related to a relatively small strand of literature that
examines the effects of public-sector CB laws on public-sector earnings.
Freeman (1986) and Freeman and Valletta (1988) summarized the early lit-
erature on this topic. The majority of that literature found that a favorable
legal environment toward collective bargaining increases public-sector com-
pensation.
1
For example, Freeman and Valletta (1988) found that public-
sector employees in states with laws favorable to collective bargaining have
an approximate 6% wage advantage, and Ichniowski, Freeman, and Lauer
(1989) found that police compensation is higher in states with stronger CB
laws. Similarly, using an instrumental variable identification strategy, Hirsch
et al. (2012) found that state CB laws increased teacher wages by approxi-
mately 12 percentage points. Most recently, Frandsen (2016) exploited dif-
ferences in the timing of the enactment of state CB laws to isolate the effect
of those laws on public-sector compensation. Using historical data from the
Current Population Survey (CPS), he found that mandatory CB laws
increased the wages of firefighters and police but had little effect on the
wages of teachers.
2
Our article is also closely related to two recent studies on public-sector
rent extraction. Brueckner and Neumark (2014) developed a model that
posited the ability of public-sector workers to extract rents would depend in
1
Several papers focus solely on effects of unionization. Most of those papers, including Hoxby (1996)
and Baugh and Stone (1982), found substantial wage effects ranging from 5 to 22%. Important excep-
tions include Kleiner and Petree (1988) and Lovenheim (2009) who found the impact of unionization
to be close to zero for teacher pay.
2
Zax and Ichniowski (1990) and Frandsen (2016) also provided evidence that suggests mandatory CB
laws significantly increase unionization rates among public-sector workers.
482 ILR REVIEW
part on the level of desirable local amenities. Consistent with their theoreti-
cal predictions, they found that public-sector wages were higher in states
with desirable local amenities, with the effect of amenities being stronger in
states that mandated collective bargaining. Building on the work of
Brueckner and Neumark (2014), Diamond (2017) developed a model that
predicted that a less elastic housing supply would increase the ability of
public-sector workers to extract rents. Consistent with that prediction, she
found that public-sector wages were higher in metropolitan areas that have
a less elastic housing supply, with the effect of an inelastic housing supply
being stronger in states that mandated collective bargaining.
3
Our work builds on these studies and makes several important contribu-
tions to the literature. First, prior studies that examined the effect of state
CB laws on public-sector compensation tend to be based on either cross-
sectional or longitudinal data that exploits historical variation in the timing
of state adoption of CB laws. For example, the analysis of Frandsen (2016)
is based on changes in bargaining laws that occurred primarily during the
1960s and 1970s, and those laws have remained relatively unchanged for
the past 50 years. As a result, it is unclear whether his results (or the results
of other prior studies) would generalize to more recent time periods. By
contrast, we exploit variation across state borders within local labor markets
and use much more recent data on public-sector wages to isolate the causal
effect of CB laws on public-sector compensation. Second, although
Brueckner and Neumark (2014) and Diamond (2017) both found that
mandatory CB laws provide public-sector workers with a formal mechanism
to extract rents in the presence of desirable local amenities or an inelastic
housing supply, both studies refrain from attempting to isolate the direct
causal effect of mandatory CB laws on public-sector compensation.
Alternatively, isolating the causal effect of CB laws is the primary focus of
this article.
Data
Our primary source of data is the Public Use Microdata Sample (PUMS)
from the 2005 to 2015 American Community Survey (ACS). The ACS is a
nationally representative survey that contains detailed demographic and
labor force participation data on approximately two million households per
year. The obvious advantage of using the ACS, relative to other national
representative surveys, such as the Current Population Survey (CPS), is the
3
Our study is also indirectly related to a relatively large literature on public- and private-sector wage
differentials. Krueger (1988), Borjas (2002), Allegretto and Keefe (2010), Schmitt (2010), Munnell,
Aubry, Hurwitz, and Quinby (2011), and Lewin et al. (2012) all found that public-sector workers earn
approximately 4–10% less than their private-sector counterparts. By contrast, Biggs and Richwine (2011),
Gittleman and Pierce (2012), and Bewerunge and Rosen (2013) found that once public-sector benefits
are taken into account, public-sector workers are overcompensated relative to their private-sector
counterparts.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 483
large sample size and its detailed demographic and labor force information.
A second advantage is that the ACS includes information on the location of
workers’ primary employer (as well as residence), information that is essen-
tial to our border discontinuity analysis. Our sample consists of workers
aged 18 to 64 years who worked full-time in the past 12 months.
4
We define
full-time workers as individuals who reported working between 30 and 70
hours per week and who worked 50 to 52 weeks in the past 12 months.
Note that in all of our analyses, we identify workers in our sample based on
their place of work rather than their place of residence. Specifically, we
assign information on CB laws and the CZ attributes discussed below to
workers based on their place of work to ensure that we correctly match
workers to the CB environment that governs their workplace environment.
The dependent variable in our analysis is the log of hourly wages, which
is constructed using information on 1) reported total wage and salary
income in the past 12 months, 2) reported number of weeks worked last
year, and 3) usual hours worked per week. The hourly wage rate is then
computed as total wage and salary income divided by the product of weeks
worked and usual hours worked per week. We further restrict the sample to
individuals with an implied hourly wage rate greater than or equal to the
federal minimum wage in a given year. The full set of individual-level con-
trol variables include age, age squared, sex, years of educational attainment,
four categories of marital status, and race/ethnicity indicators for individu-
als who self-report themselves to be Asian, black, or Hispanic.
Following Diamond (2017), among others, we restrict our analysis to
workers with non-imputed earnings to guard against any bias resulting from
the ACS wage imputation methods (Hirsch and Schumacher 2004;
Bollinger and Hirsch 2006). Since omitting individuals with imputed earn-
ings potentially changes the characteristics of individuals included in the
sample, we follow Bollinger and Hirsch (2006) and Hirsch and Winters
(2014) and reweight the respondent sample using inverse probability of
response weights. Specifically, we first estimate a logit model in which the
dependent variable is an indicator that takes the value of 1 for individuals
with non-imputed earnings, and 0 otherwise; the regressors include the full
set of control variables discussed above. We then weight our regressions by
the inverse probability of response.
Nonprofit employees are included in the sample along with the private-
sector for-profit employees. We exclude from our analysis self-employed
workers and military personnel. We also exclude federal employees from
our main analysis but utilize them subsequently in falsification tests. Our
rationale for excluding federal workers relates to state and federal labor
laws. Specifically, the National Labor Relations Act (NLRA) covers private-
sector workers nationwide but explicitly excludes federal, state, and local
4
We focus on workers located in the contiguous United States and thus omit Alaska and Hawaii from
our analysis.
484 ILR REVIEW
workers. State and local workers are covered separately by state-specific
labor laws. Note that non-postal federal workers can be union members but
collective bargaining over wages and benefits is prohibited. Non-managerial
postal (USPS) workers have CB rights and can bargain over wages. As a
result, although federal workers are public-sector employees, we omit them
given that federal workers are not covered by state-specific CB laws.
A somewhat controversial issue is whether to control for occupational dif-
ferences when examining public- and private-sector wage differentials. On
the one hand, if occupation codes capture primarily unobserved differences
in human capital and working conditions, then controlling for occupation
would be appropriate (Gittleman and Pierce 2012). On the other hand, as
Schanzenbach (2015) noted, some occupational controls may be inap-
propriate since little common support occurs in those occupations across
the public and private sectors. For example, a significantly larger proportion
of public-sector workers (25.7%) than private-sector workers (2.3%) are
employed in education-related occupations. Given the controversy sur-
rounding occupation controls, we present results without any occupation
controls and results based on specifications for which we include broad,
two-digit census occupational controls (25 categories).
Another controversial issue is whether to control for union coverage,
which is not reported in the ACS. The consensus in the literature is to omit
union coverage controls. Specifically, as noted by Hirsch, Wachter, and
Gillula (2000), including a control for union coverage would be appropriate
if union status was a proxy for transferrable skills, making it similar to other
controls, such as educational attainment and age. Hirsch et al. (2000), how-
ever, summarized that the most credible empirical evidence on this topic
does not support the belief that union status is associated with higher pro-
ductivity, casting doubt on whether union status should be considered a
transferrable skill.
5
More recently, Gittleman and Pierce echoed this senti-
ment and noted that ‘‘controlling for union coverage seems inappropriate
because union wage premia probably do not reflect ability differences and
those in the public work force would not likely take their public sector
unionization rates with them if they were to move’’ (2012: 226).
The smallest identifiable geographical area in the ACS is the Public Use
Microdata Area (PUMA). We used the crosswalk between 1990 CZs and
2000 PUMAs created by Autor and Dorn (2013) to allocate PUMAs to CZs
for the 2005 to 2011 ACS, which includes 2000 PUMA codes.
6
For data from
the 2012 to 2015 ACS, which includes 2010 PUMA codes, we used data on
the division of 2010 county population across 2010 PUMAs from the
Missouri Census Data Center and the crosswalk between counties and 1990
5
See, for example, Clark (1984) for evidence on whether union status is associated with higher produc-
tivity, and Booth (1995) for a summary of the evidence on the union productivity differential.
6
Similar to core-based statistical areas (CBSAs), commuting zones are designed to be spatial measures
of local labor markets. Unlike CBSAs, commuting zones are defined for the entire United States, not just
for metropolitan areas.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 485
CZs to allocate 2010 PUMAs to CZs. (Since CZs are aggregations of coun-
ties, the crosswalk between counties and CZs provides a perfect overlap.) In
most cases, a PUMA can be matched to an exact county and therefore an
exact CZ. In some instances, however, PUMAs span multiple counties that
may belong to different CZs (but never different states). In that event we
cannot assign an individual to a unique CZ and instead follow Autor and
Dorn (2013), weighting individuals who are assigned to multiple CZs by the
fraction of the area of the individual’s PUMA in the given CZ.
We obtained detailed information on state CB laws from Sanes and
Schmitt (2014), who documented the CB rights of teachers, firefighters,
police, and all other public-sector workers in each state.
7
Classifying state
CB laws can be complicated, but states fall into three general categories: CB
required, CB prohibited, and CB permissible. CB-required states mandate
that state and local governments ‘‘bargain in good faith’’ with their employ-
ees if they present themselves with a union. As categorized by Sanes and
Schmitt (2014), we define CB-mandatory states as states where collective
bargaining is legal and wage negotiation is also legal. By contrast,
CB-prohibited states explicitly prohibit state and local employers from bar-
gaining with worker unions. Finally, in CB-permissible states, state and local
governments may choose whether to bargain if employees request to do so.
As described by Frandsen (2016), lack of a statute regarding collective bar-
gaining has typically been interpreted in the courts as an implicit prohibi-
tion. For simplicity, we therefore categorize states into two groups: those
with mandatory CB laws and those that explicitly or implicitly prohibit col-
lective bargaining.
A complication with this classification scheme relates to heterogeneity in
the right to bargain across occupations within some states. To overcome this
issue, in our primary analysis we drop the workers who do not match with
their corresponding state’s classification. For example, Texas strictly prohi-
bits collective bargaining for all public workers except police and firefigh-
ters. Since these two occupations do not match Texas’s classification, we
drop police and firefighters in Texas from our sample. We also estimate
models in which we focus directly on individual occupations and use the
specific bargaining laws for these groups. For example, we estimate separate
regressions for teachers, police, firefighters, and all other local government
employees. The top panel of Table 1 shows the states that fall into the three
classifications of CB laws, and the bottom panel presents the states that gen-
erally prohibit collective bargaining but allow either police or firefighters to
bargain.
In the empirical analysis that follows we include controls for several state-
and CZ-level variables that could potentially affect public- and private-sector
7
To minimize inaccuracies, we compared and validated the classifications developed by Sanes and
Schmitt (2014) with other sources of information on state CB laws, for example, Valletta and Freeman
(1985) and Brueckner and Neumark (2014).
486 ILR REVIEW
wage differentials. First, in all of our specifications we include an indicator
for whether a state had a Right-to-Work (RTW) law in place in year t.
8
In
states with RTW laws, employees cannot be compelled to join a union or to
pay union agency fees as a condition of employment. As a result, RTW laws
may potentially reduce the power of unions by reducing their membership
and resources. Second, we constructed the four amenity variables used by
Brueckner and Neumark (2014) in their analysis of the effects of amenities
on public-sector rent extraction. The variables include Mild and Dry repre-
senting local temperature and humidity, respectively; Proximity measuring
the average distance to the nearest coast or navigable water; and Density
measuring population density.
9
Third, as noted by Anzia and Moe (2014),
liberal states tend to grant more generous compensation packages to
public-sector employees. We therefore control for the presidential
Democratic vote share in the 2004 and 2008 presidential elections to proxy
for voter sentiment toward public-sector employees.
10
With the exception of
the RTW indicator, all of these variables were constructed by aggregating
county-level data up to either the CZ level or the state-by-CZ level.
Table 1. Collective Bargaining Environment for Public-Sector Workers
Collective Bargaining (CB) category States
CB required California, Connecticut, Delaware, Florida, Illinois, Indiana, Iowa,
Kansas, Maine, Maryland, Massachusetts, Michigan, Minnesota,
Montana, Nebraska, Nevada, New Hampshire, New Jersey, New
Mexico, New York, Ohio, Oregon, Pennsylvania, Rhode Island,
South Dakota, Vermont, Washington, Wisconsin
CB allowed Alabama, Arizona, Arkansas, Colorado, Idaho, Kentucky,
Louisiana, Mississippi, Missouri, North Dakota, Oklahoma,
Tennessee, Utah, West Virginia, Wyoming
CB prohibited Georgia, North Carolina, South Carolina, Texas, Virginia
State CB authorized occupations in states that generally prohibit
collective bargaining
Arizona Firefighters, Police
Georgia Firefighters
Texas Firefighters, Police
8
Data on the timing of enactment of state RTW laws come from National Conference of State
Legislatures.
9
Climate data are from the Area Resource File (ARF) maintained by the Health Resources & Services
Administration. Mild temperature is the negative of the sum of the absolute values of the differences
between monthly average temperature and 20 degrees Celsius, summed over January, April, July, and
October. Dry weather is the negative of the average monthly precipitation for those four months. Coastal
proximity data come from Rappaport and Sachs (2003), and proximity is the negative of the average dis-
tance from each county’s centroid to the nearest coast, Great Lake, or major river. Population density
data come from 2005–2009 ACS data.
10
County-level presidential vote tallies for the 2004 and 2008 presidential elections were obtained from
the Federal Election Commission. We use vote tallies from the 2004 presidential election for years 2005–
2008 and vote tallies from the 2008 presidential election for years 2009–2015.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 487
Furthermore, we standardize all of these variables to have a mean of 0 and
a standard deviation of 1.
Table 2 provides the mean and standard deviation of the variables used
in our analysis. We present separate summary statistics for public- and
private-sector employees in states with and without mandatory CB laws. As
Table 2 reveals, both public- and private-sector wages tend to be higher in
CB-mandatory states. Furthermore, in both sets of states, public-sector work-
ers tend to be older and have higher educational attainment than do
private-sector workers. This outcome is consistent with previous findings in
the literature. Finally, voters in CB-mandatory states appear to be much
more likely to vote for the Democratic presidential candidate.
Empirical Framework
To examine how state CB laws affect public-sector wages, we begin by esti-
mating models of the following form:
Table 2. Summary Statistics
Variables
CB mandatory CB non-mandatory
Public Private Public Private
Mean SD Mean SD Mean SD Mean SD
Salary 55,484 31,213 58,672 57,825 44,900 27,622 54,008 50,182
Individual controls
Age 45.634 10.839 42.979 11.588 44.947 11.088 42.542 11.612
Female 0.540 0.498 0.453 0.498 0.587 0.492 0.440 0.496
Less than high school 0.018 0.135 0.064 0.245 0.025 0.157 0.075 0.264
High school degree 0.458 0.498 0.580 0.494 0.440 0.496 0.603 0.489
Bachelor’s degree 0.255 0.436 0.238 0.426 0.276 0.447 0.223 0.416
Advanced degree 0.268 0.443 0.118 0.323 0.259 0.438 0.099 0.299
Black 0.087 0.282 0.054 0.226 0.140 0.347 0.100 0.300
Hispanic 0.094 0.292 0.118 0.322 0.085 0.279 0.111 0.314
Asian 0.043 0.202 0.062 0.241 0.017 0.129 0.028 0.166
Married 0.676 0.468 0.633 0.482 0.689 0.463 0.655 0.476
State and CZ controls
Right-to-Work 0.177 0.381 0.187 0.390 0.842 0.365 0.832 0.374
Mild –37.666 12.096 –38.362 12.090 –29.443 8.863 –29.644 8.784
Dry –7.606 2.501 –7.582 2.415 –8.252 2.800 –8.147 2.756
Density 0.792 0.798 0.696 0.699 0.205 0.089 0.207 0.088
Proximity –0.078 0.119 –0.076 0.096 –0.222 0.209 –0.222 0.209
Democratic vote share 2004 0.523 0.053 0.518 0.054 0.410 0.043 0.410 0.043
Democratic vote share 2008 0.574 0.053 0.570 0.052 0.449 0.050 0.449 0.050
Observations 631,399 3,674,311 368,432 1,959,983
Notes: Summary statistics for wages and individual-level control variables are from 2005–2015 American
Community Survey (ACS) Public Use Microdata Sample (PUMS) data. Climate data are from the Area
Resource File (ARF) maintained by Quality Resource Systems under Health Resources and Services
Administration. Data on population density are from the 2005–2009 ACS summary file, aggregated to
the CZ level. County-level presidential vote tallies for the 2004 and 2008 presidential elections come
from the Federal Election Commission and are aggregated to the CZ level. CB, collective bargaining;
CZ, commuting zone; SD, standard deviation.
488 ILR REVIEW
ln(wageimst )=b0+b1Pubimst +b2Pubimst*CBs
ðÞ
+Ximst a+dm+us+lt+eimst ,
ð1Þ
where wageimst is the hourly wage of worker iin CZ m, state s, in year t;
Pubimst is an indicator variable that takes the value of unity if individual i
works in the public sector; CBsis an indicator for whether state shas a man-
datory CB law for public-sector workers; Ximst is a vector of individual charac-
teristics; dm,us,andltare CZ, state, and year fixed effects, respectively; and
eimst is a random disturbance term. Because Equation (1) includes state
fixed effects, the level effect of CBsis omitted. In all of our specifications,
we also include an indicator for whether state shad a RTW law in place in
year t, and that variable interacted with the public-sector employee indicator
and the CB-mandatory indicator.
The coefficient of primary interest in Equation (1) is b2, the coefficient
on the interaction between the public-sector employee indicator and the
indicator for states with mandatory CB laws. Specifically, b2measures how
the wage differential between public- and private-sector workers changes
when public-sector workers are covered by a mandatory CB law. The inclu-
sion of both state and CZ fixed effects implies that we are controlling for
any state- or CZ-level, sector-invariant unobservables (i.e., unobservables
that affect public- and private-sector wages in the same way) that are poten-
tially correlated with our key variable of interest and thus might otherwise
bias our estimates.
11
The identifying assumption underlying Equation (1) is that the magni-
tude of the public–private wage gap in states without mandatory CB laws is
identical to what it would be in states with mandatory CB laws, had those
states not passed CB laws. This assumption will be violated if unobserved fac-
tors differentially affect the wages of otherwise similar public- and private-
sector workers and are correlated with CB laws. For example, Brueckner
and Neumark (2014) found that public- and private-sector wage differen-
tials are larger in states with more desirable local amenities. Thus, if manda-
tory CB laws are correlated with amenity levels, estimates of b2will be
biased unless one fully controls for differences in amenities across CB-man-
datory and CB-non-mandatory states. Similarly, if public- and private-sector
wage differentials are larger in more liberal states because those states grant
more generous compensation packages to public-sector employees, esti-
mates of b2will again be biased if CB laws are correlated with a state’s politi-
cal leanings.
To address these potential sources of bias, our preferred specification
builds on Equation (1) by exploiting policy discontinuities at state borders
to identify the effect of mandatory CB laws on public-sector wages.
11
Note that because we focus on how state CB laws affect public- and private-sector wage differentials,
we are essentially using a difference-in-differences (DD) identification strategy, in which the first differ-
ence is the average difference between otherwise similar public- and private-sector workers and the sec-
ond difference is how that difference changes if a worker is located in a mandatory CB state.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 489
Specifically, we focus on workers located in CZs that cross state boundaries
and estimate models that replace the CZ fixed effects in Equation (1) with
CZ-by-public-sector-worker fixed effects (dm*Pub):
ln(wageimst )=b0+b2Pubimst*CBs
ðÞ+Ximst a+dm*Pub +us+lt+mimst :ð2Þ
The inclusion of state and CZ-by-public-sector-worker fixed effects in
Equation (2) implies that we are now identifying the effect of mandatory
CB laws on public-sector wages using only within local labor market (CZ)
variation in the strength of state CB laws. That is, our model is now identi-
fied from CZs that cross state boundaries where one state in the CZ has a
mandatory CB law whereas the other state in the same CZ does not.
Furthermore, note that the inclusion of CZ-by-public-sector-worker fixed
effects provides nonparametric controls for any unmeasured CZ-level fac-
tors that might differentially affect the earnings of otherwise similar private-
and public-sector workers. Thus, the inclusion of these fixed effects controls
for the differential effect any sector-invariant CZ-level observable or unob-
servable factor may have on public- and private-sector wage differentials. As
a result, they fully control for all of the factors identified by Brueckner and
Neumark (2014) and Diamond (2017) that differentially shift public- and
private-sector wage differentials, namely desirable amenities and housing
supply elasticities.
Furthermore, to provide additional evidence that our results are not
being driven by unobservable factors that vary across states within the same
CZ, we also estimate specifications for which we interact the public-sector
employee indicator and the CB-mandatory indicator with several state-specific
CZ-level factors, namely population density; proximity to the nearest coast,
Great Lake, or major river; and the Democratic vote share in the 2004 and
2008 presidential elections.
12
We add these controls to further account for
the possibility that the returns to these attributes may differ across the pub-
lic and private sector or across CB-mandatory and non-mandatory states.
Finally, to control for the possibility that the returns to individual character-
istics (e.g., educational attainment and age) may also vary across the public
and private sector or across states with and without mandatory CB laws, we
estimate specifications in which we interact the individual characteristics in
Equation (1) and Equation (2) with both the public-sector worker indicator
and the indicator for states with a mandatory CB law.
We present estimates from Equations (1) and (2) based on two separate
samples of workers. The first sample includes all state and local government
workers and all private-sector workers; the second sample is limited to local
government workers and all private-sector workers. Our rationale for provid-
ing separate results that focus solely on local government employees relates
to our identification strategy. Recall that our primary identification strategy
12
We do not include the other two amenity controls used by Brueckner and Neumark (2014), namely
Mild and Dry, since these variables have almost no variation within CZs.
490 ILR REVIEW
exploits policy discontinuities at state borders and compares public- and
private-sector wage differentials in CZs that cross state borders where one
state has a mandatory CB law and the other state does not. We do this to
ensure we are comparing workers in the same labor market and workers
who are exposed to very similar amenities, general political leanings, and
other CZ attributes; characteristics that we show are balanced in Table 3.
Since most CB agreements for local government employees are negotiated
at the local level, the fact that characteristics of CZs that cross state bound-
aries are quite balanced provides increased confidence that our coefficient
of primary interest, b2, will not be biased by unobserved factors that are cor-
related with mandatory CB laws. By contrast, state employees have contracts
that are negotiated at the state level, and as we show in Table 3, overall
characteristics of states with and without mandatory CB laws differ greatly.
We therefore have less confidence that we can identify the causal impact of
CB laws on public- and private-sector wage differentials for state workers
since those differentials may still be influenced by unobserved state-specific
characteristics.
We also note that with freely mobile labor and the absence of differ-
ences in non-pecuniary working conditions or worker productivity, one
might expect that any pay differential between public-sector workers in states
with and without mandatory CB laws would be competed away, particularly
when such policy discontinuities occur along state borders. However, there
are several reasons why wages may not equalize. First, labor mobility between
the unionized (CB-mandatory) and non-unionized (CB-non-mandatory) sec-
tors is likely to be restricted because of the non-competitive features of union
agreements that govern employment conditions and pay scales. Second,
occupational licensing requirements that differ across states, non-portable
pension benefits, and residency requirements for public-sector workers are
likely to further impede labor mobility.
13
In addition to exploiting policy discontinuities at state borders in state
CB laws, we also examine variation within states in bargaining laws and con-
sider states where the majority of public workers are without bargaining
rights. Specifically, we exploit the fact that several of the CB-prohibited
states extend CB rights to firefighters or police, or in some cases both. For
example, Texas, which prohibits collective bargaining for most public-sector
workers, grants CB rights to police and firefighters. Similarly, Georgia
extends CB rights only to firefighters. Using this sample of states, we esti-
mate models of the following form:
13
See, for example, Kim, Koedel, Ni, and Podgursky (2016) and Goldhaber, Grout, Holden, and
Brown (2015) for evidence of significant barriers to cross-state teacher mobility, even along state borders.
Also see Black, Kolesnikova, and Taylor (2014) for evidence that the labor force participation of women
(a group overrepresented in the public sector) is highly sensitive to commute times, and Boyd,
Lankford, Loeb, and Wyckoff (2005) for evidence that teachers have strong preferences to teach nearby
to where they grew up.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 491
ln wageist
ðÞ=g0+g1Pub Occist +g2Pub Occist*CBs
ðÞ+Xist a+us+lt+vist ,ð3Þ
where Pub Occist is a set of indicator variables for police and firefighters,
respectively, and Pub Occist *CBsis a set of interaction terms between each of
Table 3. Balancing Tests
Variable
All CZ
comparison
Within straddling
CZ comparison
CB coefficient p value CB coefficient p value
(1) (2) (3) (4)
Voting, climate and 2005–2009 ACS Summary File variables
Democratic vote share 2004 0.041*** 0.000 0.022 0.188
Democratic vote share 2008 0.074*** 0.000 0.015 0.515
Population density 24.47*** 0.001 2.778 0.815
Mild climate –6.76*** 0.000 –0.005 0.981
Dry climate 1.529 0.150 1.194 0.136
Proximity to water 0.116 0.969 9.164 0.135
Mean household income 4,149*** 0.000 –139.7 0.938
Fraction college educated 0.028*** 0.000 –0.005 0.789
Log population 0.155 0.172 0.118 0.664
Observations 870 44
2005–2015 PUMS ACS variables
Age 0.657*** 0.000 0.340 0.130
Fraction female 0.002 0.668 0.001 0.841
Fraction less than high school –0.010 0.313 0.003 0.498
Fraction high school degree –0.019 0.234 0.034 0.498
Fraction college degree 0.012 0.174 –0.022 0.527
Fraction advanced degree 0.017** 0.017 –0.015 0.438
Fraction married –0.017** 0.017 –0.004 0.757
Fraction black –0.060*** 0.001 0.062 0.209
Fraction Asian 0.034*** 0.002 –0.015 0.341
Fraction Hispanic 0.009 0.804 –0.007 0.627
Management and financial operations occupations 0.005 0.377 –0.020 0.405
Professional and related occupations 0.005 0.398 –0.009 0.540
Service occupations 0.017*** 0.000 0.010 0.275
Sales and related occupations –0.004** 0.021 0.005 0.411
Office and administrative support occupations –0.002 0.487 –0.002 0.868
Farming, fishing, and forestry occupations 0.001 0.101 0.002 0.261
Construction and extraction occupations –0.011*** 0.000 0.007 0.240
Installation, maintenance, and repair occupations –0.005*** 0.000 0.003 0.590
Production occupations –0.004 0.461 0.002 0.806
Transportation and material moving occupations –0.002 0.249 0.003 0.756
Observations 6,634,125 388,394
Notes: Presents differences in means tests for various commuting zone attributes. Estimates are from a
regression of CZ attribute on indicator for a mandatory collective bargaining state. Columns (1) and
(2) provide comparisons based on all CZs. Columns (3) and (4) include CZ fixed effects and restrict
the sample to CZs that cross state boundaries and where the collective bargaining environment differs
on either side of the state border. The 10 occupation categories are defined by the Bureau of Labor
Statistics (http://www.bls.gov/cps/cenocc2010.pdf). Standard errors clustered at the commuting zone
level. ACS, American Community Survey; CB, collective bargaining; CZ, commuting zone; PUMS,
Public Use Microdata Sample.
***p\0.01; **p\0.05; *p\0.1.
492 ILR REVIEW
those indicators and an indicator for whether a state has a mandatory CB
law for the given occupation.
Results
Balancing Tests
To provide initial evidence that estimates from our preferred specification
given by Equation (2) have a causal interpretation, Table 3 presents
difference-in-means tests for observable state-specific CZ characteristics
among states that do and do not mandate collective bargaining. The top
panel of Table 3 reports balancing tests for Democratic presidential vote
shares, the four local amenities from Brueckner and Neumark (2014), and
several characteristics generated using the 2005 to 2009 ACS summary files.
The bottom panel reports balancing tests for observable characteristics
taken from the 2005 to 2015 ACS PUMS. Columns (1) and (2) present esti-
mated coefficients and pvalues from models in which we regress state-
specific CZ-level characteristics on an indicator for whether public-sector
employees in a CZ are covered by a mandatory CB law.
14
Note that the esti-
mates reported in columns (1) and (2) utilize all of the variation across CZs
in the listed characteristics. The results reveal significant differences in the
characteristics of CZs located in CB-mandatory and non-mandatory states.
For example, CZs located in CB-mandatory states have significantly higher
mean household incomes, higher population density, and contain voters
who are significantly more likely to support the Democratic presidential
candidate.
Columns (3) and (4) of Table 3 present results from balancing tests that
utilize only the identifying variation used in our preferred specification
given by Equation (2), namely within local labor market (CZ) variation in
the strength of state CB laws that originates from policy discontinuities at
state borders. Specifically, we restrict the sample to CZs that cross state bor-
ders and where the bargaining environment on either side of the border
differs. We then regress state-specific CZ-level characteristics on an indicator
for whether public-sector employees in a CZ are covered by a mandatory
CB law and also include CZ fixed effects. As a result, the estimates reported
in columns (3) and (4) are now identified from CZs that cross state bound-
aries where one state in the CZ has a mandatory CB law whereas the other
state in the same CZ does not. In columns (3) and (4), none of the esti-
mated coefficients are significantly different from zero, and they tend to be
smaller in magnitude than those reported in column (1). Thus, once we
include CZ fixed effects, we find that the observable state-specific character-
istics of CZs are quite balanced across states that do and do not mandate
collective bargaining: a finding that increases our confidence in the identify-
ing assumption underlying Equation (2).
14
The reported pvalues in Table 3 are based on standard errors that are clustered at the CZ level.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 493
Main Results
Our benchmark regression results based on the estimation of Equations (1)
and (2) are reported in Table 4.
15
All of the models are weighted using the
person weight provided by the ACS multiplied by the fraction of the area of
the individual’s PUMA in the given CZ and the inverse probability of
response. Furthermore, all standard errors are clustered at the state level to
allow for within-state autocorrelation of the disturbance term. Note that
although Table 4 reports only the estimated coefficient on the public-sector
employee indicator, and the interaction between that variable and the man-
datory CB indicator, all the specifications reported in Table 4 and subse-
quent tables include the full set of individual-level control variables, the
Table 4. Estimated Effects of Mandatory CB Laws on Public-Sector Pay
Variable (1) (2) (3) (4) (5) (6)
State and local government workers vs. Private-sector workers
Public –0.117*** –0.113*** –0.0974***
(0.00784) (0.00899) (0.0107)
Public 3CB 0.110*** 0.103*** 0.107*** 0.0610*** 0.0589*** 0.0599***
(0.0111) (0.0141) (0.0137) (0.0135) (0.0132) (0.0129)
Observations 6,634,125 6,634,125 6,634,125 388,394 388,394 388,394
Local government workers vs. Private-sector workers
Public –0.120*** –0.109*** –0.0910***
(0.00875) (0.00964) (0.0118)
Public 3CB 0.117*** 0.0975*** 0.103*** 0.0616*** 0.0628*** 0.0605***
(0.0123) (0.0125) (0.0134) (0.0117) (0.0135) (0.0141)
Observations 6,235,000 6,235,000 6,235,000 370,079 370,079 370,079
CZ FE Yes Yes Yes Yes Yes Yes
State FE Yes Yes Yes Yes Yes Yes
State-specific CZ controls No Yes Yes No Yes Yes
Individual interactions No No Yes No No Yes
CZ-by-Public FE No No No Yes Yes Yes
Notes: Data from the American Community Survey (ACS) 2005–2015. All specifications include the full set
of individual-level controls, right-to-work (RTW) status, and year fixed effects. Top panel reports results for
the combined sample of state and local government workers and all private-sector workers. Bottom panel
limits the sample to local government workers and all private-sector workers. Columns (1)–(3) utilize all
CZs, and columns (4)–(6) restrict the sample to CZs that cross state boundaries and where the collective
bargaining environment differs on either side of the state border. Robust standard errors clustered at the
state level in parentheses. CB, collective bargaining; CZ, commuting zone; FE, fixed effects.
***p\0.01; **p\0.05; *p\0.1.
15
Blackburn (2007) demonstrated that if the distribution of the error term is not independent of the
regressors, standard OLS estimates from semi-log wage equations can lead to estimates of percentage
wage gaps that are biased. To address that possibility, we also estimated models based on a generalized
linear model (GLM) with a log-link. Results from this alternative estimation procedure were similar to
those reported in Table 4 and are available upon request.
494 ILR REVIEW
RTW indicator, and the RTW indicator interacted with the public-sector
employee indicator and the CB-mandatory indicator.
16
The top panel of Table 4 reports results for the full sample of state and
local government workers and all private-sector workers whereas the bottom
panel limits the sample to local government workers and all private-sector
workers. Column (1) reports results based on a specification that includes
state and CZ fixed effects. In both the top and bottom panel, the estimated
coefficient on the Public 3CB interaction is positive and statistically signifi-
cant. In terms of magnitude, our results suggest mandatory CB laws increase
public-sector wages by approximately 0.11 log points.
17
We next present results based on specifications for which we interact the
public employee indicator and the mandatory CB indicator with a number
of state-specific CZ-level control variables, namely the four amenity variables
used by Brueckner and Neumark (2014) and the fraction of voters within a
CZ who supported the Democratic candidate for president.
18
As shown in
column (2), the inclusion of these additional controls slightly attenuates the
estimated coefficient on the Public 3CB interaction, but it remains statisti-
cally significant at the 1% level. Column (3) includes additional controls
that take the form of interactions between the individual-level controls
(e.g., educational attainment and age) and the public-sector employee and
CB-mandatory indicators. Again, the inclusion of these controls has only a
modest impact on the results.
Results based on our preferred specification given by Equation (2) are
presented in columns (4)–(6) of Table 4. There we report results based on
specifications identical to those reported in columns (1)–(3) except we
replace the CZ fixed effects with CZ-by-public-employee fixed effects and
restrict the sample to workers located in CZs that cross state boundaries and
where the bargaining environment on either side of the border differs.
Restricting the sample to CZs that cross state boundaries and controlling for
CZ-by-public-employee fixed effects reduces the magnitude of the estimated
coefficients on the Public 3CB interaction by approximately 40 to 50%, but
they remain statistically significant in both the top and bottom panels. In our
preferred specification that includes the full set of amenity and individual
interactions (column (6)), our results now suggest that mandatory CB laws
increase public-sector wages by approximately 0.06 log points.
Table 5 replicates the results reported in Table 4 but adds occupation
fixed effects, based on the Standard Occupational Classification system
16
As noted previously, the full set of individual-level control variables include age, age squared, sex,
years of educational attainment, four categories of marital status, and controls for Asian, black, and
Hispanic.
17
Because of concerns over the comparability of public- and private-sector workers, we refrain from
interpreting the estimated coefficient on the public-sector worker indicator as showing whether public-
sector workers are ‘‘overpaid’’ or ‘‘underpaid’’ relative to their private-sector counterparts.
18
As noted previously, the four amenity variables include local temperature and weather controls
(Mild and Dry), the average distance to the nearest coast (Proximity), and population density (Density).
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 495
two-digit occupation codes, to all specifications.
19
In our preferred specifica-
tions that restrict the sample to workers located in CZs that cross state
boundaries and include CB-by-public employee fixed effects (columns (4)–
(6)), the estimated coefficients on the Public 3CB interaction are slightly
smaller than the corresponding estimates reported in Table 4, but all esti-
mates remain statistically significant.
One potential concern with the results based on specifications that
include CZ-by-public-sector-employee fixed effects (our preferred specifica-
tion), is that we are identifying the effect CB laws have on wages based on
the relatively small number of CZs that cross state boundaries, where one
state in the CZ has a mandatory CB law and the other does not. Specifically,
as shown in Table A.1 of the Appendix, our results are based on 21 CZs that
Table 5. Estimated Effects of Mandatory CB Laws on Public-Sector Pay with
Occupational Controls
Variable (1) (2) (3) (4) (5) (6)
State and local government workers vs. Private-sector workers
Public –0.0428*** –0.0364*** –0.0386***
(0.00694) (0.00845) (0.00871)
Public 3CB 0.100*** 0.0897*** 0.0966*** 0.0543*** 0.0486*** 0.0517***
(0.0108) (0.0137) (0.0131) (0.0116) (0.0117) (0.0115)
Observations 6,634,125 6,634,125 6,634,125 388,394 388,394 388,394
Local government workers vs. Private-sector workers
Public –0.0225*** –0.0113 –0.00924
(0.00655) (0.00730) (0.00862)
Public 3CB 0.107*** 0.0858*** 0.0921*** 0.0569*** 0.0562*** 0.0576***
(0.00978) (0.0108) (0.0115) (0.00842) (0.00980) (0.0110)
Observations 6,235,000 6,235,000 6,235,000 370,079 370,079 370,079
CZ FE Yes Yes Yes Yes Yes Yes
State FE Yes Yes Yes Yes Yes Yes
State-specific CZ controls No Yes Yes No Yes Yes
Individual interactions No No Yes No No Yes
CZ-by-Public FE No No No Yes Yes Yes
Notes: Data from the American Community Survey (ACS) 2005–2015. All specifications include the full
set of individual-level controls, 23 occupational controls defined by Current Population Survey (CPS),
right-to-work (RTW) status, and year fixed effects. Top panel reports results for the combined sample
of state and local government workers versus all private-sector workers. Bottom panel limits the sample
to local government workers versus all private-sector workers. Columns (1)–(3) utilize all CZs, and
columns (4)–(6) restrict the sample to CZs that cross state boundaries and where the collective
bargaining environment differs on either side of the state border. Robust standard errors clustered at
the state level in parentheses. CB, collective bargaining; CZ, commuting zone; FE, fixed effects.
***p\0.01; **p\0.05; *p\0.1.
19
We also estimated models that, in addition to the occupational controls, included a separate indica-
tor for teachers to account for the fact teachers tend to earn substantially less than other college gradu-
ates. Adding a dummy variable for teachers yielded results that were similar to those reported in Table 5.
Results are available upon request.
496 ILR REVIEW
cross state boundaries and have bargaining environments that vary.
Although this apparent limitation has no impact on the validity of our analy-
sis, it may affect generalizability.
We therefore present further evidence on the generalizability of our
results by conducting similar analyses to those reported in Table 5 (models
with occupation fixed effects) except we now utilize all the PUMAs that are
located within 20 miles of a state border and where the states along the bor-
der have CB environments that differ. Results are reported in Table 6.
20
Column (1) reports results based on specifications that include PUMA fixed
effects, column (2) adds the same amenity interactions used in column (2)
of Table 4 except the amenities are now measured at the PUMA level, and
column (3) adds the full set of interactions between the individual
Table 6. Estimated Effects of Mandatory CB Laws on Public-Sector Pay: PUMAs
Located within 20 Miles of State Borders
Variable (1) (2) (3) (4) (5) (6)
State and local government workers vs. Private-sector workers
Public –0.0221*–0.0197*–0.0210**
(0.0112) (0.0101) (0.00980)
Public 3CB 0.0909*** 0.0728*** 0.0807*** 0.0611*** 0.0560*** 0.0644***
(0.0212) (0.0192) (0.0182) (0.0150) (0.0149) (0.0157)
Observations 1,908,487 1,908,487 1,908,487 360,728 360,728 360,728
R-squared 0.478 0.478 0.479 0.468 0.469 0.470
Local government workers vs. Private-sector workers
Public –0.00344 –0.00172 0.00166
(0.0101) (0.00830) (0.00763)
Public 3CB 0.0886*** 0.0665*** 0.0727*** 0.0603*** 0.0521*** 0.0602***
(0.0191) (0.0170) (0.0154) (0.00726) (0.0127) (0.0141)
Observations 1,808,689 1,808,689 1,808,689 341,596 341,596 341,596
R-squared 0.480 0.480 0.481 0.471 0.472 0.472
PUMA FE Yes Yes Yes Yes Yes Yes
PUMA amenities No Yes Yes No Yes Yes
Individual interactions No No Yes No No Yes
Border-by-Public FE No No No Yes Yes Yes
Notes: Data from the American Community Survey (ACS) 2005–2015. All specifications include the full
set of individual-level controls, 23 occupational controls defined by Current Population Survey (CPS),
right-to-work (RTW) status, and year fixed effects. Top panel reports results for the combined sample
of state and local government workers and all private-sector workers. Bottom panel limits the sample to
local government workers and all private-sector workers. Columns (1)–(3) utilize all PUMAs located
within 20 miles of a state border, and columns (4)–(6) restrict the sample to PUMAs located within 20
miles of a state border and where the collective bargaining environment differs on either side of the
state border. Robust standard errors clustered at the state level in parentheses. CB, collective
bargaining; FE, fixed effects; PUMA, Public Use Microdata Area.
***p\0.01; **p\0.05; *p\0.1.
20
We also conducted balancing tests, like those reported in Table 3, for the PUMA sample. The results
are quite similar to those reported in Table 3 and are available upon request.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 497
characteristics and the public-sector worker indicator and the CB-manda-
tory indicator. Finally, columns (4)–(6) replicate the specifications in col-
umns (1)–(3) but restrict the sample to state borders where the bargaining
environment differs on either side of the border and add border-by-public
fixed effects so that our estimates are identified based on PUMAs in which
the bargaining environment differs on either side of a state border. The
standard errors reported in Table 6 are once again clustered at the state
level.
The results reported in Table 6 are generally quite similar to those
reported in Table 5, which speaks to the generalizability of our results.
Specifically, in our preferred specifications reported in columns (4)–(6), all
of the point estimates on the Public3CB interaction are statistically signifi-
cant and similar in magnitude to those reported in Table 5.
Teachers, Police, and Firefighters
In this section, we examine whether the results shown in Tables 4 and 5
hold for workers in specific occupations, namely teachers, police, and fire-
fighters. Specifically, in Table 7 we estimate specifications identical to those
in Table 4 except we use detailed occupation-specific bargaining laws and
include only government workers employed in the given occupation, com-
paring their wages to the overall sample of private-sector workers.
21
Results based on our preferred specification that includes CZ-by-public-
sector-employee fixed effects and the full set of individual and CZ interac-
tion terms are reported in columns (2), (5), (8), and (11) for teachers,
police, firefighters, and all other local public-sector employees, respectively.
In every case we find that the estimated coefficient on the Public 3CB inter-
action is positive and statistically significant, with the exception of firefight-
ers. We note, however, that even for firefighters the point estimate on the
Public 3CB interaction is relatively large in magnitude and similar to the
estimates for other public-sector occupations but is noisily estimated. That
the estimate for firefighters is noisy is not surprising given the significantly
smaller sample sizes for firefighters. In terms of magnitude, our results sug-
gest that mandatory CB laws increase the wages of teachers by approxi-
mately 0.10 log points and police, firefighters, and all other local workers by
0.12, 0.08, and 0.04 log points, respectively. Using a DD identification strat-
egy that exploits the plausibly exogenous timing of when states adopted
mandatory CB laws, Frandsen (2016) found that mandatory CB laws
increase the wages of police and firefighters by 0.075 and 0.129 log points,
respectively. Our estimates for police and firefighters are generally compa-
rable to his estimates.
22
Frandsen (2016) also found, however, that
21
In Table 7 and all other tables in which we focus on specific occupations, we do not include occupa-
tion fixed effects.
22
Based on a t-test, we cannot reject the null hypothesis that the estimates obtained by Frandsen
(2016) are the same as the estimates reported in Table 7 for police and firefighters.
498 ILR REVIEW
Table 7. K-12 Teachers, Police, Firefighters, Other Local Public Employees
Variable
(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11)
K-12 teachers Police Firefighters Other local public employees
Public –0.199*** 0.0374 –0.0353 –0.101***
(0.0215) (0.0275) (0.0272) (0.0109)
Public 3CB 0.0771*** 0.0900*** 0.110*** 0.164*** 0.121*** 0.117*** 0.137*** 0.0664 0.0793 0.102*** 0.0388***
(0.0258) (0.0290) (0.0203) (0.0351) (0.0198) (0.0328) (0.0444) (0.0393) (0.0478) (0.0159) (0.0109)
Observations 5,827,910 348,019 348,019 5,678,687 339,113 339,113 5,650,218 337,715 337,715 6,050,505 359,114
CZ FE Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes
State FE Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes
Individual interactions and CZ controls No Yes Yes No Yes Yes No Yes Yes No Yes
CZ-by-Public FE No Yes Yes No Yes Yes No Yes Yes No Yes
Quality of work environment No No Yes No No Yes No No Yes No No
Notes: Data from the American Community Survey (ACS) 2005–2015. All specifications include the full set of individual-level controls, right-to-work (RTW) status, and year fixed
effects. Columns (1)–(3) restrict the sample of government workers to K-12 teachers, and columns (4)–(6), (7)–(9), and (10)–(11) restrict the sample of government workers to
police, firefighters, and all other local government workers, respectively. Robust standard errors clustered at the state level in parentheses. CB, collective bargaining; CZ,
commuting zone; FE, fixed effects.
***p\0.01; **p\0.05; *p\0.1.
mandatory CB laws have little effect on the wages of teachers, a result that
stands in contrast to our finding that such laws increase the wages of teach-
ers by approximately 0.10 log points.
23
The results reported in Tables 4 to 7 consistently suggest that manda-
tory CB laws increase public-sector wages. Several possible explanations
for this finding exist. First, observed wage differentials could arise because
of unobserved productivity or skill differences between public- and
private-sector workers in CB-mandatory and non-mandatory states.
Specifically, one possible explanation for our results is that compared to
CB-non-mandatory states, CB-mandatory states employ public-sector work-
ers who are relatively more skilled than their private-sector counterparts.
Second, our results may reflect compensating differentials in pay for non-
pecuniary job attributes that vary across CB environments. For example,
pupil–teacher ratios (class size) may vary across CB environments and
teachers in states with higher pupil–teacher ratios may earn higher wages
to compensate them for having larger classes.
24
The final explanation is
rent extraction: public-sector employees in CB-mandatory states may be
better situated to extract rents than are public-sector employees in CB-
non-mandatory states.
In terms of the first explanation (productivity or skill differences), we
note that in our preferred specifications we include interactions between
individual-level observable measures of skill, such as educational attainment
and age (a proxy for experience), and both the public-sector worker indica-
tor and the CB-mandatory indicator. Thus, our fully interacted specifica-
tions control for observable measures of skill that vary across the public and
private sector and across CB-mandatory and non-mandatory states.
Although we cannot completely rule out the presence of other unobserva-
ble skill differences between public-sector workers in CB-mandatory and
CB-non-mandatory states, the fact that our results are highly robust to the
inclusion of these additional interactions casts doubt on whether skill differ-
entials fully explain our findings.
As an initial test of the second explanation (compensating differentials),
in columns (3), (6), and (9) of Table 7 we add additional covariates
designed to capture the quality of the public-sector work environment.
Specifically, in column (3), we add the state-specific pupil–teacher ratio in a
CZ and that variable interacted with both the indicator for public-sector
teachers and the indicator for CB-mandatory states to the specification
23
Our results are also at odds with those obtained by Lovenheim (2009). Using historical data on the
timing of teachers’ union election certification for school districts in three Midwestern states, he found
that unionization had little effect on teacher salaries. By contrast, our results are consistent with the
results of Winters (2011), who found that collective bargaining significantly increases the salaries of expe-
rienced teachers.
24
This variance could arise, for example, if there is a trade-off between wages and employment and
teachers in CB-mandatory states bargain for higher wages in exchange for lower employment leading to
higher pupil–teacher ratios.
500 ILR REVIEW
reported in column (2).
25
The inclusion of these additional covariates has
little impact on our results: The estimates reported in column (3) are
quite similar to those reported in column (2). In columns (6) and (9),
respectively, we add state-specific measures of the number of police offi-
cers per capita and the number of firefighters per capita in a CZ and those
variables interacted with both the indicators for police officers and firefigh-
ters and the indicator for CB-mandatory states. Once again, we find that our
results are largely unaffected by the inclusion of these additional covariates.
We interpret these results as suggesting that compensating differentials are
likely not the primary explanation of our core findings. Given we find little
evidence that our results are being driven by skill differences or compensat-
ing differentials, we conclude that the most plausible explanation for our
results is that public-sector employees with strong bargaining rights receive
rents.
Table 8. Estimated Effects of Mandatory CB Laws on Public-Sector Pay: States
without Public-Sector CB Rights
Variable
(1) (2) (3) (4)
Comparison vs. Public-sector workers Comparison vs. Private-sector workers
Firefighter 0.0155 0.0165 –0.1407*** –0.139***
Robust SE (0.0279) (0.0280) (0.0262) (0.0256)
Confidence interval [–0.277, 0.063] [–0.026, 0.062] [–0.181, –0.100] [–0.177, –0.101]
Firefighter 3CB 0.139*** 0.137*** 0.1117*** 0.110***
Robust SE (0.0284) (0.0291) (0.0263) (0.0263)
Confidence interval [0.094, 0.184] [0.091, 0.183] [0.071, 0.152] [0.070, 0.150]
Police 0.0925** 0.0927*** –0.0802*** –0.0798***
Robust SE (0.0212) (0.0212) (0.0178) (0.0177)
Confidence interval [0.057, 0.133] [0.0593, 0.129] [–0.112, –0.050] [–0.112, –0.048]
Police 3CB 0.157*** 0.156*** 0.145*** 0.144***
Robust SE (0.0315) (0.0315) (0.0369) (0.0371)
Confidence interval [0.093, 0.214] [0.095, 0.214] [0.077, 0.207] [0.083, 0.212]
Observations 285,464 285,464 1,628,585 1,628,585
State year FE Yes Yes Yes Yes
State-by-Year FE No Yes No Yes
Notes: Sample restricted to states without collective bargaining rights for most government workers. All
specifications include the full set of individual-level controls and year fixed effects. Columns (1) and (2)
compare firefighters and police to all other local government workers. Columns (3) and (4) compare
firefighters and police to all private-sector workers. Robust standard errors clustered at the state level in
parentheses. Wild-clustered bootstrap confidence intervals in brackets. CB, collective bargaining; FE,
fixed effects; SE, standard error.
***p\0.01; **p\0.05; *p\0.1.
25
Brueckner and Neumark (2014) conducted a similar test in their analysis of the relationship between
local amenities and public- and private-sector wage differentials. To construct CZ-level estimates of the
pupil–teacher ratio we used data from the National Center for Education Statistics (NCES) from 2005–
2010 on the number of teachers and number of pupils in each school district within a CZ. We then
aggregated those to the CZ (or CZ-by-state) level to construct the CZ measure of the pupil–teacher ratio.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 501
Estimates Based on States that Restrict CB Rights
In Table 8 we turn to results based on Equation (3), which exploits variation
within states in CB laws. Specifically, we focus on states that generally pro-
hibit collective bargaining and exploit the fact that several of those states
allow collective bargaining for firefighters or police, or in some cases both.
26
We then estimate two sets of models. In the first set, we restrict the sample
to public-sector workers and estimate models that compare the wages of
police and firefighters to those of all other public-sector workers in states
that do and do not authorize police and firefighters to bargain. In the sec-
ond set, we restrict the sample to police, firefighters, and all private-sector
workers and estimate models that now compare the wages of police and
firefighters to those of private-sector workers in states that do and do not
authorize police and firefighters to bargain.
Columns (1) and (2) of Table 8 report results for a comparison group
comprising all government workers other than police and firefighters, and
columns (3) and (4) report results for a comparison group comprising
private-sector workers. We report only the estimated coefficients on the
police and firefighter indicators and those indicators interacted with the
CB-authorized indicator but note that all specifications include the full set
of individual-level control variables. Because the number of states in our
sample is small (eight states), conventional clustering methods are likely to
produce standard errors that are too small (Cameron and Miller 2015). As
demonstrated by Cameron, Gelbach, and Miller (2008), however, the wild
clustered bootstrap performs quite well even with as few as six clusters. We
therefore report both traditional standard errors clustered at the state level
and wild clustered bootstrap confidence intervals.
Turning first to the results reported in column (1), we find that the
ability to collectively bargain increasesthewagesoffirefightersbyapprox-
imately 0.14 log points, an estimate that is statistically significant at the
1% level. As shown in the bottom rows of Table 8, we find similar results
for police. In column (2) we replace state and year fixed effects with
state-by-year fixed effects to control for intertemporal differences across
states in wage gaps. The inclusion of these state-by-year fixed effects has
little effect on our results. As shown in columns (3) and (4), we find qua-
litatively similar results when we switch the comparison group to private-
sector workers rather than all other public-sector workers. Specifically,
the ability to collectively bargain increases the wages of firefighters by
approximately 0.11 log points and the wages of police by approximately
0.14 log points.
26
The states are Alabama, Arizona, Georgia, Mississippi, North Carolina, South Carolina, Texas, and
Virginia. In addition to being states that typically prohibit collective bargaining, all of these states are also
right-to-work states. Among these states, Georgia extends CB rights to firefighters but no other public-
sector workers; Arizona and Texas extend CB rights to both firefighters and police but no other public-
sector workers.
502 ILR REVIEW
Falsification Test
In this section, we report results based on a series of falsification tests in
which we examine whether mandatory state CB laws also affect the wages of
federal or nonprofit workers. Non-postal federal employees are on a federal
government defined pay schedule called General Schedule (GS).
27
The
schedule is based solely on the level of experience, education, and the posi-
tion applied for, which do not reflect state or local laws that govern the bar-
gaining environment. Similarly, nonprofit workers are in many ways quite
similar to public-sector workers, with the exception that they are not cov-
ered by mandatory state CB laws.
28
Therefore, if our previous results have a
causal interpretation we should find that state CB laws have little impact on
the wages of either federal or nonprofit workers.
29
Table 9. Falsification Tests
Variable (1) (2) (3) (4) (5) (6)
Federal government workers vs. Private-sector workers
Public 0.191*** 0.188*** 0.190***
(0.0106) (0.0106) (0.00963)
Federal worker 3CB –0.0121 –0.00641 –0.00515 0.00510 –0.00584 0.00478
(0.0168) (0.0154) (0.0136) (0.0151) (0.0169) (0.0182)
Observations 5,845,456 5,845,456 5,845,456 363,515 363,515 363,515
Nonprofit workers vs. All other private-sector workers
Public –0.0601*** –0.0595*** –0.0699***
(0.00474) (0.00555) (0.00668)
Nonprofit worker 3CB 0.0183*** 0.0184*** 0.0145*–0.00338 0.000492 0.00127
(0.00629) (0.00667) (0.00736) (0.00407) (0.00375) (0.00743)
Observations 5,634,294 5,634,294 5,634,294 336,810 336,810 336,810
CZ FE Yes Yes Yes Yes Yes Yes
State FE Yes Yes Yes Yes Yes Yes
State-specific CZ controls No Yes Yes No Yes Yes
Individual interactions No No Yes No No Yes
CZ-by-Public FE No No No Yes Yes Yes
Notes: Top panel presents falsification tests that compare federal workers to all private-sector workers;
bottom panel compares nonprofit workers to all other private-sector workers. All specifications include
the full set of individual-level controls, 23 occupational controls defined by Current Population Survey
(CPS), right-to-work (RTW) status, and year fixed effects. Columns (1)–(3) utilize all CZs, and columns
(4)–(6) restrict the sample to CZs that cross state boundaries and where the collective bargaining
environment differs on either side of the state border. Robust standard errors clustered at the state
level in parentheses. CB, collective bargaining; CZ, commuting zone; FE, fixed effects.
***p\0.01; **p\0.05; *p\0.1.
27
Non-managerial postal (USPS) workers utilize a different pay scale and can bargain over wages. We
therefore drop federal postal workers from the sample in the falsification tests.
28
See Hirsch, Macpherson, and Preston (2017) for evidence on the similarities between nonprofit and
public-sector workers.
29
Brueckner and Neumark (2014) and Diamond (2017) also used federal workers as a falsification test
in their studies.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 503
Table 9 reports results from our falsification tests. The specifications
reported in Table 9 are identical to those reported in Table 5 except that in
the top panel of Table 9 the sample is now restricted to federal employees
and all private-sector workers, and in the bottom panel the sample is
restricted to nonprofit employees and all other private-sector workers. In all
six columns the point estimate on the Federal worker 3CB interaction is
small in magnitude and statistically insignificant. In the bottom panel, the
point estimate on the Nonprofit worker 3CB interaction is positive and sta-
tistically significant in the first three columns but small in magnitude rela-
tive to the results reported in Table 5. More important, in our preferred
specifications that include CZ-by-nonprofit worker fixed effects (columns
(4)–(6)), the estimated coefficient on the Nonprofit worker3CB interac-
tion is quite small in magnitude and statistically insignificant. Thus, our falsi-
fication tests reveal little evidence that mandatory CB laws increase the
wages of either federal or nonprofit workers, providing further evidence
that our core results have a causal interpretation.
Conclusion
In recent years, a number of states have attempted to pass legislation (some-
times successfully) that would substantially curtail or eliminate the CB rights
of public-sector workers. In the midst of the worst economic crisis since the
Great Depression, proponents of limiting public-sector employee bargain-
ing rights have argued that public-sector workers are overpaid and that
mandatory CB laws grant public-sector unions additional negotiation power
through political influence that could potentially distort the labor market
and have detrimental impacts on government finances. In this article, we
provide new evidence on whether and how mandatory CB laws affect
public-sector wages.
Using a variety of identification strategies, we find that mandatory CB
laws raise public-sector wages by approximately 0.05 to 0.08 log points.
Drilling down to specific occupations, we find that mandatory CB laws
increase the wages of teachers, firefighters, police, and all other local
public workers. Furthermore, we exploit variation within states in CB laws
and consider states where the majority of public-sector workers are with-
out bargaining rights. Within these states, we estimate DD models that
compare the public- and private-sector wage differential in states that
authorize police and firefighters to bargain to the public- and private-
sector wage differential in states that prohibit police and firefighters from
bargaining. Once again we find that, even in states that generally prohibit
collective bargaining, the extension of bargaining rights to certain occu-
pations, namely police and firefighters, tends to increase the wages of
workers in those occupations.
Our finding that mandatory CB laws increase public employee wages is
consistent with the majority of the existing literature. Indeed, our estimates
504 ILR REVIEW
of the effect of collective bargaining on the wages of firefighters and police
are quite comparable to Frandsen’s (2016) DD estimates that exploit the
historical timing of when states adopted mandatory CB laws. We note, how-
ever, that our finding that mandatory CB laws increase the wages of teach-
ers stands at odds with the results of Frandsen (2016) and Lovenheim
(2009), who found that collective bargaining and teacher unionization have
little effect on teacher salaries. Among the many potential explanations for
why our results differ from these prior studies, one could be related to the
time period being studied. Specifically, both Frandsen (2016) and
Lovenheim (2009) focused on the historical timing of when states adopted
mandatory CB laws or when teachers within districts first became unionized
to identify the effects of CB laws and unions on teacher salaries. Thus, their
analyses are based primarily on changes in CB laws and unionization that
occurred during the 1960s and 1970s. By contrast, we exploit contempora-
neous variation across state borders within local labor markets to isolate the
causal effect of CB laws on teacher salaries and utilize very recent (2005–
2015) data on teacher salaries. Nevertheless, given the mixed evidence in
the literature on the effect of mandatory CB laws on teacher compensation,
more research on this topic is clearly needed.
As noted previously, recent articles by Brueckner and Neumark (2014)
and Diamond (2017) provided evidence that mandatory CB laws provide a
formal mechanism through which public-sector workers can extract rents in
areas with low housing supply elasticities or high levels of desirable ame-
nities. In this article, we show that even after controlling for the effects of
housing supply elasticities and amenities, mandatory CB laws appear to have
a direct effect on public-sector wages.
An important caveat to our work is that we focus solely on the impact of
mandatory CB laws on wages and not total compensation. To the extent
that such laws also lead to higher total compensation in the form of
increased retirement and health benefits, our results may be a lower
bound on the overall effect of mandatory collective bargaining on public-
sector compensation. In fact, recent evidence suggests this may indeed be
the case. Diamond (2017) found that a decrease in the housing supply
elasticity increased the probability that local public-sector workers receive
some employer contribution toward health insurance premiums, but only
in states that mandate collective bargaining. Similarly, using an identifica-
tion strategy that exploited the timing of state adoption of CB laws,
Frandsen and Webb (forthcoming) found that mandatory CB laws signifi-
cantly increase government contributions to pensions while simultane-
ously reducing employee contributions. Finally, using data from the
1999–2000 Schools and Staffing Survey (SASS), Hirsch et al. (2012) found
that state CB laws increase average benefits by approximately 0.2 log
points,aneffectthatisroughlytwiceaslargeastheeffectofmandatory
CB laws on average salaries.
STATE COLLECTIVE BARGAINING LAWS AND PUBLIC-SECTOR PAY 505
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23600 Burlington, IA 3,557 1,330 4,887 548 256 804
24701 St. Louis, MO 5,283 48,249 53,532 754 4,431 5,185
26404 Lemmon, SD 911 1,546 2,457 133 269 402
26704 Grand Forks, ND 2,643 1,005 3,648 461 100 561
26801 Fargo, ND 1,934 3,453 5,387 311 373 684
29502 Kansas City, MO 22,083 27,627 49,710 2,783 3,243 6,026
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