Are State Workers Overpaid? Survey Evidence from Liquor Privatization in Washington State

Abstract

Industry privatizations that result in exogenous job displacement of public employees can be exploited to estimate public sector wage rents. I report the findings of an original survey I administered to examine how wages of displaced government workers were affected by a 2012 privatization of liquor retailing in Washington State. Based on a panel difference-in-differences estimator I find that privatization reduced wages by $2.51 per hour or 17 percent compared to a counterfactual group of nearly identical non-displaced workers, with larger effects for women. I decompose wage losses into three rents identified in the literature: public sector rents, union premiums, and industry-specific human capital. Public sector wage premiums separately account for 85 to 90 percent of overall wage losses, while union premiums and industry-specific human capital account for just 10 to 15 percent. The results are consistent with a roughly 16 percent public sector wage premium.

Introduction

Are state government workers overpaid? The question has received renewed attention in recent years as state budget shortfalls and deteriorating public employee pension systems have prompted increased scrutiny of public sector pay. Labor economists have long recognized the potential for “rent extraction” by public employees in the form of wages and benefits in excess of workers’ outside alternatives. Government wages are not set in competitive markets (Brueckner and Neumark 2014), workers are more likely to be union represented (at least in those states that allow public-sector collective bargaining, see Visser 2006), and public employees are politically active (O’Brien 1992). Public-sector rent extraction has taken a variety of non-wage forms as well, including increased health and pension benefits (Clemens and Cutler 2014) and deflection of budget cuts away from programs associated with strong public sector unions (Clemens 2012). For these reasons, the stylized fact of public employee wage premiums has been incorporated into a variety of formal models of public sector labor markets (Brueckner and Neumark 2014; Glaeser and Ponzetto 2013; Holmlund 1993; Borjas 1980; Reder 1975; Fogel and Lewin 1974).

While economic theory makes clear predictions about public employee wage premiums, the large empirical literature on the subject is mixed.¹ Most studies find evidence of wage premiums among federal government employees on the order of 10 to 20 percent relative to private sector counterparts. However, premiums are typically found only at the highest levels of government: the federal government in the U.S., and comparable central governments internationally. Wage premiums for state and local employees are zero or slightly negative in most estimates. This suggests the rent seeking central to most theoretical models of public sector labor markets may be a poor description of local public employee labor markets.

In recent years, a vigorous political debate surrounding state budget crises has prompted a reexamination of public compensation. At one extreme Keefe (2012) finds no evidence of public sector wage premiums, reporting a 7.6 percent earnings penalty among state workers based on cross-sectional microdata from IPUMS-CPS and the Employer Costs for Employee Compensation survey. At the other extreme Gittleman and Pierce (2012) find a significant 3 to 10 percent earnings premium for state employees relative to comparable private sector workers through the use of an alternative treatment of controls for occupation, employer size, and union status (reflecting earlier methodological points about the appropriateness of these controls as a proxy for worker skills made by Linneman et al. 1990 and Hirsch et al. 1999). Both studies were covered extensively in the media, fueling the longstanding political controversy over the degree to which state employees are over (or under) compensated and thus a contributing (or non-contributing) factor to state budget woes.²

This study presents evidence on public sector wage premiums from a different source of identification. Rather than comparing private and public sector wages in the cross section, I make use of a panel of exogenously displaced government workers laid off by a 2012 privatization of liquor retailing in Washington State. Enacted by voter ballot initiative, the privatization closed 167 state-run retail liquor stores and laid off an entire occupational category of public employees. As a comparison group, I use government workers in similar retail occupations who were unaffected by the policy. The decision by displaced workers to accept employment following layoffs serves as a revelation mechanism for the second-best wage offer facing displaced public sector workers. Due to the exogenous timing and non-selective nature of the displacements, these quasi-experimental “treatments” can be used to identify public sector wage premiums.³

The treatment group consists of exogenously displaced government workers for whom wages are observed before and after privatization. I collected information on post-policy wages and other demographic characteristics of the displaced workers via an original mail and online survey questionnaire. These responses were then matched to pre-policy wage information from administrative records, resulting in an individual-level panel of wages and other demographic details over the nine year period from 2005 to 2013. The control group consists of a panel of remarkably similar employees working in comparable retail occupations in state government: customer service specialists in the state’s motor vehicle licensing offices. These individuals were employed by the same state government, worked in retail occupations with similar job skills, were similarly unionized, and worked in comparable urban and suburban retail outlets. Average wages for both groups of workers followed nearly identical trends throughout the pre-policy period. I use these data to identify the causal effect of privatization-related job displacements on public sector wages using a panel difference-in-differences estimator with individual and time fixed effects.

Based on a panel of 262 workers from 2010 to 2013, I find that privatization reduced wages of displaced government workers by −$2.51 per hour, or roughly 17.2 percent compared to the control group of unaffected workers. Consistent with past literature I find somewhat larger effects among female workers, with wages falling by −$2.87 per hour or 19.7 percent for females compared with −$2.20 per hour or 15.1 percent for males, although the two estimates are not statistically different. Quantile regression results reveal considerable heterogeneity of treatment effects throughout the conditional wage distribution, ranging from −$4.62 per hour at the 5th percentile of wages to a statistical zero effect at the 95th percentile. These basic findings are unaffected by (1) the inclusion of individual-level controls for gender and length of job tenure; by (2) excluding from the sample individuals who reported more valuable non-wage fringe benefits in their post-policy employment; and by (3) estimation via a kernel matching difference-in-differences estimator in which treated and control workers are propensity-score matched based on observables.⁴

By examining treatment effects in various subsamples, it is possible to provide a rough decomposition of overall wage losses into three types of wage rents identified by previous literature: public sector wage premiums; union wage premiums; and wage premiums from industry-specific human capital lost following job displacement. I decompose overall wage losses into lost union, public-sector and industry-specific wage rents by examining linear combinations of treatment effects from various subsamples of workers who sorted into (1) private-sector retail liquor jobs, (2) government jobs, (3) union jobs, and (4) non-union jobs following privatization.⁵ I find that public sector wage rents separately account for roughly 86 to 90 percent of the overall decline in wages following privatization. By contrast, lost industry-specific human capital accounts for 11 to 13 percent of wage declines, while lost union wage premiums account for roughly 1 percent or less. These results suggest that displaced state government workers earned a roughly 16 percent public sector wage premium prior to displacement. This estimate lies somewhat above the 3 to 10 percent earnings premium reported by Gittleman and Pierce (2012), and is substantially larger than estimates from comparable panel studies such as Krueger (1988) and Lee (2004) which are not based on exogenous job separations. However, the effects are considerably smaller than those found in Galiani and Sturzenegger (2008), and are consistent with those found in similar international studies of the effect of privatizations on displaced workers such as Firpo and Gonzaga (2010).

This study is not the first to use the privatization of state-owned firms as an exogenous shock to identify public sector wage rents. Studies in Brazil (Firpo and Gonzaga 2010), Portugal (Monteiro 2008), Argentina (Galiani and Sturzenegger 2008), and the U.K. (Disney and Gosling 2003) have used a similar approach in recent years, yielding a wide variety of estimates from zero to roughly 40 percent wage premia. This study contributes to this growing literature by applying the approach to public employees in the United States for the first time. This extension is relevant as U.S. labor markets are generally more flexible and labor unions weaker than in previous countries examined, and thus conclusions from overseas studies may not apply to public sector workers in the U.S. While the source of identification is novel, it is not without limitations. I examine a small sample of government workers in an unusual occupational category,thus, the results may not easily generalize to broader classes of public employees. However, by making use of a clean source of identifying variation the approach overcomes many of the sorting, selection and endogenous job separation problems that have plagued past research. With several states considering similar liquor privatization initiatives, this study provides the first estimates of the likely effect of those policies on displaced public employees.⁶

The remainder of the paper is organized as follows. Section “Related Literature” reviews the related literature. Section “Policy Background” gives background on the privatization of liquor retailing in Washington State. Section “Data” describes the data and survey design. Section “Identification Strategy” explains the difference-in-differences identification strategy. Section “Results” presents my results, and Section “Conclusion” concludes. The Appendix presents tables of alternative results and a copy of the original survey questionnaire.

Related Literature

Public Sector Wage Premiums

The empirical literature on public sector wage premiums is large, both in the U.S. and internationally. Gregory and Borland (1999) and Ehrenberg and Schwartz (1986) review the early literature. Most research has focused on federal employees, with a smaller number of studies examining state and local workers. Among those examining state employees, most research has been cross sectional based on large, publicly available data sets. Following Smith (1976), early studies employed Oaxaca (1973)-style decompositions or simple OLS with controls to identify public sector wage premiums. Nearly all studies report a positive wage premium for federal workers on the order of 10 to 20 percent, with higher premiums for women and those in high-amenity urban locations, but zero or slightly negative wage premiums for state and local government workers (Gregory and Borland 1999).⁷

The basic identification problem faced by early literature is the inability to address non-random assignment of workers into sector of employment in the cross section. Workers choose jobs partly on the basis of unobserved characteristics, including risk aversion and attitudes toward public service, which are likely correlated with productivity. Recognizing this problem, a second wave of studies beginning with Robinson and Tomes (1984) and Gyourko and Tracy (1988) employed Heckman-style correction methods to cross-sectional data, resulting in somewhat smaller estimates of federal wage premiums but still zero or slightly negative premiums for state and local workers. The modern literature has made little progress beyond these methods. For example, the two recent studies of Keefe (2012) and Gittleman and Pierce (2012) both estimate wage premiums for state government workers using OLS with controls in large, cross-sectional data sets.⁸

Three studies have used longitudinal data to address the problem of unobserved worker heterogeneity: Krueger (1988), Hirsch et al. (1999) and Lee (2004). All three identify government wage premiums via fixed effects estimators identified off workers who voluntarily shift between private and government jobs. Krueger (1988) uses matched files from the Current Population Survey and the supplemental Displaced Worker Survey to identify “switchers” who moved between sectors in subsequent years in the two panels. He finds somewhat smaller federal wage premiums of 5 to 10 percent for federal workers, but again a statistically zero wage premium for state workers. Subsequently, Krueger (1988) has been criticized for the small number of “switchers” used for identification in the two panels—for example, the Displaced Worker Survey used in the study contains information on just 91 workers who switched between sectors—and thus the representativeness of the results (Moulton 1990; Lee 2004). By contrast, Hirsch et al. (1999) restrict attention to U.S. Postal Service employees, analyzing earnings for workers switching between private sector and federal postal jobs based on longitudinal data from the Postal New Hire Survey, matched Current Population Survey panels, and the Displaced Worker Survey. They find large public sector wage premiums on the order of 30-40 percent among new postal employees.

Lee (2004) presents longitudinal estimates of public sector wage premiums using the National Longitudinal Survey of Youth (NLSY) for the first time. For state government employes, the survey contains information on 214 male and 309 female “switchers,” roughly five times the number used in Krueger (1988). He finds a 5 percent wage premium for federal workers that is well below most cross sectional estimates. For state government employees he reports a 4 percent wage premium for women and a -1 percent penalty for men, both of which are substantially larger (i.e., more positive) than typical cross-sectional estimates. An important criticism of both of Krueger (1988) and Lee (2004) is that neither makes use of exogenous job separations to identify wage premiums. Workers’ decisions to become “switchers” between sectors are likely endogenous with respect to productivity and wages. For example, if workers of low (or high) ability are disproportionately observed shifting from private sector jobs into the public sector over time, panel estimates of wage premiums will be biased and inconsistent. Without exogenous job separations the causal effect of sectoral shifts on wages is not identified, even in panel data.

In recent years, a smaller literature has emerged using quasi-experimental job displacements among government workers to identify public sector wage premiums. The transition of state-owned firms in banking, petroleum, and liquor retailing into private ownership typically results in layoffs for large numbers of government employees. To the extent that the policy decision to privatize is exogenous with respect to wages of the affected employees, and if layoffs are non-selective among workers, these job displacements can be used as “treatments” to investigate the loss of wage rents among the affected workers. Recent examples of this approach include Firpo and Gonzaga (2010) in Brazil, Monteiro (2008) in Portugal, Galiani and Sturzenegger (2008) in Argentina, and Disney and Gosling (2003) in the U.K. Estimates of public sector wage premiums from this newer literature range from 40 percent among former petroleum workers in Argentina (Galiani and Sturzenegger 2008) to 11 percent among a variety of workers in Brazilian state-run firms (Firpo and Gonzaga 2010). Only Disney and Gosling (2003) find no evidence of wage premiums based on privatization from the 1990s in the U.K. This study contributes to the growing literature by applying this quasi-experimental approach to displaced public sector workers in the U.S. for the first time.

Displaced Worker Studies

Because this study examines public employees displaced by a mass layoff event, it is also related to the large empirical literature on “displaced workers.” Extensive reviews are provided by Kletzer (1998), Fallick (1996), and Hamermesh (1989). Among workers displaced by plant closings and other mass layoffs, studies typically find significant wage declines that persists for years after displacement. Summarizing the literature, Kletzer (1998) offers five broad explanations for these observed wage losses: (1) Loss of industry specific human capital; (2) loss of firm-specific human capital; (3) loss of high-quality matches with employers; (4) loss of industry specific rents (including public sector wage rents); and (5) loss of union premiums. A key challenge faced in this study is separately identifying which of these effects played a role in the observed changes in wages among displaced state workers.

A common finding throughout the displaced worker literature is that wage losses are highly concentrated among workers who change industries following layoff (Kletzer 1998). Workers who remain in the same industry typically suffer small or zero permanent wage losses. This suggests industry-specific capital plays a central role in explaining observed wage losses among displaced workers. Several high-quality studies have confirmed this pattern, finding most worker skills appear to be transferrable within the same industry following layoffs, and that workers who find post-displacement jobs in the same industry experience few wage effects (Neal 1995; Carrington 1993; Ong and Mar 1992; Addison and Portugal 1989).⁹

Among the displaced WSLCB workers I examine, the effect of any lost industry-specific human capital should be concentrated among those who shift out of the liquor retailing industry following privatization. By contrast, those who remain in the industry following privatization should not experience this effect, as industry-specific skills have been retained. Similarly, the effect of lost union premiums and public sector rents should be concentrated among those who shift into non-union and private sector jobs, respectively, while those remaining in union and government jobs should not experience these effects.¹⁰ It is possible that this decomposition based on post-policy employment decisions by workers introduces biases due to endogenous sorting across occupations; however, I show below that there is no evidence of this on observable worker dimensions. For simplicity, I group the effects of job displacement on wages into three categories: (1) lost public sector wage rents; (2) lost union premiums; and (3) wage losses due to lost industry specific capital. Using this approach, in Section “Results” I decompose overall wage losses suffered by displaced public workers into three distinct wage rents identified in past literature.

Policy Background

In November 2011, Washington State voters approved ballot initiative I-1183, privatizing the state’s liquor retailing and distribution system.¹¹ Previously the state was one of 19 “control” states that maintain some form of public monopoly over liquor retailing.¹² For seven decades, liquor retailing was state owned and operated under the supervision of the Washington State Liquor Control Board (WSLCB). The passage of I-1183 abruptly ended the system, closing 167 state-owned liquor retailers and liquidating the assets at auction.¹³ As a consequence, approximately 900 public sector workers employed in liquor retail establishments were laid off on June 1, 2012.

A key feature of the policy is that the resulting layoffs were strongly exogenous with respect to any wage premiums enjoyed by the affected workers. The primary impetus for the ballot initiative was business lobbying by local retailers, and was not explicitly designed to reduce public sector employment or wages.¹⁴ This is a unique feature of the policy relative to most existing literature on mass layoffs, as job displacements are typically accompanied by confounding shifts in industry demand conditions or endogenous state budget pressures, neither of which were present in this setting.

The displaced public employees were union represented by the United Food and Commercial Workers Local 21 (UFCW 21). Wages were set by a collective bargaining agreement with the state. Nearly all of the affected workers held the job title “Liquor Store Clerk” or “Retail Manager.” Job responsibilities were typical of retail occupations: ringing up purchases at cash registers, maintaining merchandise displays, restocking shelves, and answering customer questions. The formal requirement for these positions was for a high school diploma, and the jobs required little specialized technical skills or knowledge. The displaced workers were employed in liquor retailers located primarily in urban and suburban areas throughout the state. Stores averaged 5,200 square feet, maintained staffs of 3 to 12 employees, and had average annual retail sales of $4 million per store. Overall, the industry was likely characterized by a similar production function to small, urban grocery and convenience stores that operate in the private sector.

Following privatization, the displaced workers were eligible for ordinary unemployment insurance benefits, but no special benefit provisions were made. Some media outlets reported local firms offering open-door job interviews to displaced workers,¹⁵ but there was no formal process to retrain or place workers into alternative employment. Fearing wage losses and reduced employment, WSLCB employees and their union representatives were among the most vocal opponents of the privatization initiative.¹⁶ Both before and after the policy change there was widespread speculation about the fate of the roughly 900 displaced public sector workers. This study is the first to examine how earnings and employment of the displaced retail liquor workers were affected by the 2012 privatization.

Data

Survey Design

I implemented an original survey of the roughly 900 state workers whose occupations were eliminated by the 2012 liquor privatization, based on individual contact information provided by Local 21 of the United Food and Commercial Workers union (UFCW 21). The survey collected detailed information on earnings, employment and other demographic characteristics from respondents.¹⁷ Names and home addresses were obtained for 911 displaced workers, 284 of whom listed email addresses. The survey followed a multi-mode approach consisting of (1) a recruitment letter; (2) an online survey; (3) a traditional mail survey; and (4) a follow-up reminder letter. The initial wave consisted of 284 emails to individuals for whom addresses were available inviting them to complete an online survey between July 12 and August 4, 2013, roughly one year after displacement. This was followed by a mail survey to the remaining individuals between August 5 and September 10, 2013. Mail surveys also included an option for completing an online survey using a unique 4-digit code, preventing duplicate responses. In total, the survey collected in N = 404 responses for a response rate of 44.3 percent. 199 online questionnaires were submitted and 205 were received via mail.

For the full population of 900 affected workers, I obtained information on pre-policy wages, hours, and gender from administrative data from the Washington State Office of Financial Management (WA OFM). These data are drawn directly from state accounting records and contain the name, gender, job title, hourly wage, and average weekly hours for 2010, 2011 and 2012 for all workers affected by the policy. These population characteristics enable me below to examine whether there is any evidence of systematic differences between this subset of survey respondents and the overall population. For the N = 404 survey respondents, the WA OFM data were matched to individual survey responses on the basis of employee names, providing a longitudinal file of earnings and other demographic information for both pre- and post-policy periods.

Tables 1 and 2 present basic descriptive statistics for the full sample of 404 respondents collected by the survey. The gender balance among survey respondents closely matches the overall population, with 42.1 percent male and 57.9 female compared to 43.8 and 56.2 percent in the overall population of displaced workers, respectively. The average age is 45 to 49 years. 84 percent report their ethnicity as white or Caucasian, with 4.2 percent African American, 3.7 percent Asian or Pacific Islander, and 3.5 percent Hispanic. Nearly half live in married households. The overwhelming majority of workers (84 percent) have less than a 4-year college degree.

Table 1 Descriptive statistics for all survey respondents (1 of 2)

Table 2 Descriptive statistics for survey respondents (2 of 2)

In terms of employment, 56.2 percent of respondents reported being employed one year after displacement, with 25.2 percent full time, 29 percent part time, and 2 percent self-employed. 30 percent of respondents were unemployed by the usual definition. The remaining 13.8 percent exited the labor force for a variety of reasons, including retirement (8.4 percent), to become a student or homemaker (4 percent), or because they simply stopped looking for work (1.5 percent). The implied unemployment rate among displaced workers was 34.5 percent one year after the policy. By comparison, the state’s overall unemployment rate was roughly 7 percent during the same period.

Because we do not observe post-policy wages for the subset of displaced workers who remain unemployed, our estimates of the effect of displacement on wages may suffer bias from this exclusion. To the extent that unemployed workers would have accepted wages that are above (or below) those observed among employed workers, the estimated treatment effects will over- (or under-) state the impact of the policy. To assess the importance of this concern, I examine whether employed and unemployed workers significantly differ on observable individual characteristics. Letting U _{i t} be a binary indicator equal to 1 if survey respondent i was unemployed during the post-policy period and 0 otherwise, I estimate the following linear probability model,

$$\begin{array}{@{}rcl@{}} \text{Prob}(U_{i} = 1 \mid X) = \beta_{o} + \beta_{1}\text{Wage}_{i} +\beta_{2}\text{Hours}_{i} + \beta_{3}\text{Tenure}_{i}+ \beta_{4}\text{Female}_{i} + \\ \beta_{5}\text{Age} + \beta_{6}\text{Moved} + \beta_{7}\text{Race} + \beta_{8}\text{Education} + \beta_{9}\mathrm{HH Size} + \epsilon_{i} \end{array} $$

(1)

Pre-policy wages and hours are from administrative data from WA OFM. Mover status is determined by a comparison of individuals’ pre-policy addresses with post-policy address from roughly one year after the policy based on a USPS-validated mailing list. Data for all other characteristics are from the administered survey. The estimation uses the full sample of N = 404 survey respondents. Table 3 presents the results. Pre-policy wages, hours, and all other individual characteristics have zero predictive power on post-policy employment status. Put differently, unemployed and employed workers do not differ significantly in terms of pre-policy observables. None of the coefficients on worker characteristics are significant, and together they explain less than 4 percent of the variation in employment status. It is possible that unemployed workers may differ on unobservable characteristics from employed workers, but there is no evidence of systematic selection into unemployment on observables.

Table 3 Assessing selection into unemployment: regression of probability of post-policy unemployment on observed worker characteristics

Average pre-policy wages among respondents were $14.35 per hour, with a standard deviation of $2.57. This amounts to annual earnings of roughly $29,850 for full-time workers, well below the average annual $55,000 earnings for Washington state employees overall in 2012.¹⁸ Post-policy wages were a significantly lower $13.33 per hour, with a larger standard deviation of $4.93.¹⁹ Most respondents who were employed found jobs in the same or similar fields, the most common being liquor retail (26.9 percent), with 13.7 percent finding jobs in the same store they previously worked in. The second most common was general non-liquor-related retail jobs (22 percent), followed by government jobs (8.8 percent), administrative jobs (8.4 percent), education (5.7 percent), and restaurant or hotel services (4.8 percent).

Among the employed, just under half reported receiving zero non-cash “fringe” benefits post-policy, with 44 percent reporting health insurance, 40.5 percent dental insurance, 44 percent paid vacation, 34.4 percent retirement benefits, and less than 10 percent childcare or transportation benefits. To assess whether wage declines were partly (or completely) offset by increases in non-wage benefits, respondents were asked to compare the dollar value of their current benefits to those provided by their previous government employer. 91.2 percent reported post-policy fringe benefits were less valuable or of roughly the same value as pre-policy benefits.²⁰ In terms of union membership, 18.9 percent of the employed reported working in a union job. 13 percent of respondents moved to a new home address during the year after job displacement, while 87 percent remained in the same location.

Construction of Treated Group

For the treatment group, I restrict the sample to a balanced panel of state workers who were involuntarily laid off by the 2012 privatization and for whom wages are observed in all pre- and post-policy years. From the sample of N = 404 survey respondents, I omit 37 individuals who self-selected out of treatment by voluntarily quitting before the policy went into effect in June 2012. This is done to isolate only those individuals for whom job displacement was involuntary and strongly exogenous with respect to wages.²¹ To avoid confounding effects of attrition from individuals moving in and out of public sector employment over time, I further restrict the sample to individuals for whom I observe public-sector wages in all years, creating a balanced panel of treated workers.²² In choosing panel size, I face a trade-off between panel length T and total observations NT as the number of individuals observed in all years falls sharply as the panel length is extended backward into the pre-policy period. I select the four-year panel from 2010 to 2013 that maximizes NT, consisting of three pre-policy periods and one post-policy period. This results in a balanced panel of N = 143 workers over T = 4 periods (N T = 572).²³ This panel serves as the “treated” group in the difference-in-differences estimates below. Table 4 presents summary statistics for this treated group.

Table 4 Summary statistics for the treated group (N = 143; T = 4)

Non-Response Bias in Treated Group

Because survey participation was voluntary, it is possible that the sample of treated workers differs systematically from the population due to survey non-response. To examine the representativeness of the treated group I regress an indicator of survey response on various pre-policy characteristics of workers for whom wages are observed in all years. For a random sample, pre-policy observables should have little explanatory power when regressed on the probability of response. Letting Y _{i t} be a binary indicator equal to 1 for survey respondents and 0 for non-respondents, I estimate the following linear probability model,

$$ \text{Prob}(Y_{i} = 1 \mid X) = \beta_{o} + \beta_{1}\text{Wage}_{i} +\beta_{2}\text{Hours}_{i} + \beta_{3}\text{Female}_{i}+ \beta_{4}\text{Moved}_{i}+\epsilon_{i} $$

(2)

As noted above, pre-policy wages, hours and gender are drawn from administrative data from WA OFM, and mover status is determined by a comparison of individuals’ pre- and post-policy addresses. The sample consists of 557 individuals for whom wages were observed on all pre-policy years, of whom 286 are survey respondents and 271 are non-respondents. Table 5 presents the estimation results. Taken together, worker characteristics explain roughly 1 percent of the variation in response probabilities. In Column (1), the univariate regression of 2011 wages on response probability is statistically significant but small, suggesting each $1 higher wages corresponds to a 1.5 percent increased likelihood of survey response. However, this effect disappears when additional controls are included.²⁴ In Columns (2) - (5) all of the estimated coefficients on wages, hours and gender are insignificant, suggesting an absence of systematic selection into survey participation on observables. The only factor that significantly predicts survey nonresponse when all controls are included in Column (5) is having moved to a new address during the post-policy period. Movers were roughly 17 percent less likely to have responded to the survey. To the extent that movers and non-movers experienced different post-policy outcomes, this will not be fully reflected in the sample. However, for those whom I have data on post-policy outcomes, movers and non-movers report post-policy wages that are not statistically different from one another, limiting the practical importance of this potential underrepresentation of migrating households.

Table 5 Assessing bias from survey non-response: regression of probability of survey response on observed population characteristics

Figure 1 shows the unconditional distributions of pre-policy wages among survey respondents and non-respondents. The left panel shows the distribution of 2011 wages among the 286 survey respondents for whom wages are observed in all years, while the right panel shows the distribution of pre-policy wages for the 271 non-respondents. The two distributions are nearly identical, with a modal wage just below $15 per hour and a range of roughly $11 to $19 per hour. Overall, systematic survey non-response does not appear to pose an important threat to identification.²⁵

Fig. 1

Distributions of Pre-Policy Wages for Survey Respondents (left panel) and Non-Respondents (right panel)

Construction of Control Group

As a control group, I identified a collection of similar public employees who were unaffected by the privatization, but whose path of earnings provides a reasonable counterfactual for what the treated workers would have experienced in the absence of displacement. Ideally these individuals would be employed within the same state government, work in similar occupations with comparable skills, and in similar geographic areas as the displaced workers. A category of public employees who closely fit this description are “Customer Service Specialists” in the Washington State Department of Licensing (WA DOL). These employees provide over-the-counter driver’s licensing application and renewal services to the public. As one of the few other retail occupations in state government, these employees have similar job requirements, skill profiles, and urban and suburban locations as the displaced workers. The workers are similarly unionized, and are represented by the American Federation of State, County, and Municipal Employees union (AFSCME 28) Council 28. Wages are established by collective bargaining agreement with the state in a similar way. The path of earnings for these employees would almost certainly have mirrored the path of wages among the displaced WSLCB workers had they been unaffected by the policy, making them an ideal counterfactual group.²⁶

Data on wages, hours, and gender for the control group of workers was provided from WA OFM for the years 2010 to 2013. Unlike treated individuals who responded to the survey, little demographic information is available for the control workers. The information provided by WA OFM was matched at the individual level to public wage data for 2005, 2007 and 2009. Doing so allowed me to construct one additional covariate for the control group: estimated job tenure at WA DOL. The resulting individual-level panel consists of N = 281 workers between 2005 and 2013. As with the treated group, the sample was restricted to workers for whom wages were observed in all years from 2010 to 2013. This resulted in a balanced panel of N = 119 individuals over T = 4 years, for a panel of size N T = 476. Table 6 presents summary statistics for this control group. Combining treated and control groups, the overall panel used for my estimation contains N = 262 individuals over T = 4 years, for a panel of size N T = 1,048.

Table 6 Summary statistics for the control group (N = 119; T = 4)

Identification Strategy

Method for Estimating Wage Losses

I identify the causal effect of liquor privatization on wages via a standard difference-in-differences (DD) estimation strategy. Conceptually, I estimate a pooled DD estimator in which panel observations of individuals from the treated and control groups are pooled into two groups in two pre- and post-policy time periods:

$$ w_{i} = \beta_{0} + \beta_{1}\text{Post}_{i} + \beta_{2}\text{Treated}_{i} + \beta_{3}\text{Post}_{i}\text{Treated}_{i} + X_{i}^{\prime} {\Gamma} + \epsilon_{i}, \qquad i = 1,...,N, $$

(3)

where w _i is the hourly wage of observation i, Post _i and Treated _i are binary indicators equal to one during the post-policy period and for members of the treated group, respectively. X _i is a matrix of individual-level controls consisting of gender and length of job tenure, and 𝜖 _i is a mean-zero error term. The coefficient of interest is β ₃, the usual DD estimator of the treatment effect of the policy on wages. Because my estimation makes use of a balanced panel of individual-level data, estimating treatment effects via (3) is equivalent to a fixed-effects panel model of the form,

$$ w_{it} = \alpha_{i} + \gamma_{t} + \beta_{3}P_{it} + X_{it}^{\prime} {\Gamma} + \epsilon_{it}, \qquad i = 1,...,N \ \ \ \ t=1,...,T $$

(4)

where α _i and γ _t are fixed effects for individual i and time period t, and P _{i t} is a dummy equal to 1 if individual i is treated in period t, and zero otherwise. In both (3) and (4) the estimated $\hat {\beta _{3}}$ has the same expectation and standard error, and provides a consistent estimate of the causal effect of the policy on wages. Equation (4) is my basic estimating equation.²⁷

To examine whether treatment effects vary throughout the conditional distribution of wages, I also present quantile regression estimates of the effect of job displacement on earnings.²⁸ Finally, as a robustness check I present estimates of propensity-score kernel matching difference-in-difference estimates in the Appendix. For these estimates, I use individual characteristics on gender and length of job tenure to estimate likelihoods of receiving treatment conditional on observables. Individuals in the treated group are then kernel-matched to a composite group of individuals from the control group with similar propensity scores.²⁹

Assessing Pre-Policy Wage Trends

The key identifying assumption for my difference-in-differences estimator is that pre-policy wages for treatment and control workers followed parallel trends. Figure 2 shows hourly wages for the balanced panel of workers for whom wages are observed in all years from 2010 to 2013. The panel consists of 143 treated individuals and 119 control individuals observed over T = 4 periods. During the decade before privatization, average wages followed nearly identical trends for the two groups. This is practically by construction as both groups were union represented, had wages established by similar collective bargaining agreements, and were employed by the same state government in similar retail occupations. Average wages grew steadily for both groups from 2005 to 2010, dipping slightly during the post-recession state budget crisis in 2011,³⁰ and stabilizing near pre-recession levels in 2012. Liquor privatization went into effect in June 2012, resulting in job displacement for the treated group. In the post-policy period of 2013, average wages diverge sharply for the two groups, with wages for the control individuals continuing their upward trend while wages fell sharply for treated workers. This parallel evolution in pre-policy wages provides an ideal setting for the identification of the causal effect of privatization on earnings via a standard difference-in-differences estimator.³¹

Fig. 2

Evolution of pre-policy wages for the treatment and control groups, 2010-2013

Method for Decomposition of Wage Rents

Treatment effects for displaced WSLCB workers should reflect the loss of three distinct wage rents: union premiums; public sector wage premiums; and lost industry-specific human capital rents. If workers are choosing jobs to maximize earnings, the pre-policy wage is the maximum attainable wage $w^{*}_{pre}$ for public employees. Following displacement, workers engage in job search, selecting the next highest alternative wage, $w^{*}_{post}$. The gap between pre- and post-policy wages $w^{*}_{pre}-w^{*}_{post}$ provides an estimate of the extent to which public employee wages exceeded workers’ opportunity cost of employment in WSLCB jobs. The decision by workers to accept employment following job displacement serves as a mechanism for revealing second-best wage offers facing public employees.

By examining linear combinations of treatment effects from various subsamples of workers who sorted into (1) private-sector retail liquor jobs, (2) government jobs, (3) union jobs, and (4) non-union jobs following privatization, overall wage losses can be decomposed into separately identifiable wage rents. Let D be a binary indicator of treatment, T be a binary indicator equal to one in the post-policy period, and I be the set of m post-policy industries into which displaced workers select for employment. Conceptually, estimated treatment effects can be expressed as a linear combination of the three lost wage rents,

$$ \mathrm{E}(\beta_{3} \mid D, T, I) = \left [ \begin{array}{ccc} \mathbb{1}_{1}(\text{union}) & \mathbb{1}_{1}(\text{govert.}) & \mathbb{1}_{1}(\text{retail} \ \text{liquor}) \\ {\vdots} & {\ddots} & {\vdots} \\ \mathbb{1}_{m}(\text{union}) & \mathbb{1}_{m}(\text{govert.}) & \mathbb{1}_{m}(\text{retail} \ \text{liquor}) \end{array} \right ] \left [ \begin{array}{c} w_{U} \\ w_{G} \\ w_{F} \end{array} \right ] = \left [ \begin{array}{c} \hat{{\beta_{3}^{1}}} \\ {\vdots} \\ \hat{{\beta_{3}^{m}}} \end{array} \right ] $$

(5)

where w _U is lost union wage rents, w _G is lost public sector wage rents, w _F is lost rents from industry-specific human capital, and the lefthand matrix is an m×3 array of zeros and ones reflecting which rents are present among wages in each of the m post-policy industries. By conditioning on the post-policy industry into which workers sort, I can use the m conditional estimates of $\hat {\beta _{3}}$ to separately identify wage rents. For example, the subsample of workers who remained employed in retail liquor following displacement retained industry-specific human capital rents w _F , but lost union and public sector wage rents w _U and w _G . Similarly, workers who moved into union-represented government jobs elsewhere retained union and public sector rents w _U and w _G , but lost rents due to industry-specific human capital w _F . Similarly, workers in non-union government jobs and private-sector union jobs can be used to separately identify union premiums w _U and public sector premiums w _G .³²

Assessing Bias in Wage Rent Decompositions Due to Selection into Post-Policy Occupation

The above method for decomposing wage rents assumes that displaced workers are of homogeneous ability and their distribution among post-policy occupations is as good as random. Table 7 examines whether systematic self-selection of displaced workers into post-policy occupations poses a threat to the above decomposition approach. For example, before privatization it is possible that wages of public employees masked heterogeneity in ability among workers, as the wage structure was determined by collective bargaining agreement rather than individual negotiations. This heterogeneity could result in non-random selection of displaced workers into post-policy occupations. If high (or low) ability workers systematically sort into high (or low) wage occupations post-policy, the above decomposition method based on subsamples of workers in various occupations may be downward (or upward) biased.

Table 7 Testing for post-policy occupational selection: multinomial logitistic regression of post-policy industry on observable characteristics of treated workers

Table 7 shows estimates from a multinomial logistic regression of indicators for each of the four occupations used for the rent decomposition (along with a fifth excluded category for all other occupations) on observed education, experience, experience squared, gender and race for the displaced workers who were employed post-policy. Following the usual practice for Mincerian wage equations, I use reported age as a proxy for labor market experience. The first four columns correspond to the occupations used in the above rent decompositions. All of the estimated coefficients are statistical zeros, and the model explains less than 8 percent of post-policy selection into occupations. The three right-hand columns show results for likelihood ratio tests of joint significance for all of the coefficients for each observable. In all cases, the tests fail to reject the null of zero coefficients with p-values ranging from 0.164 to 0.779. Although this test does not preclude the presence of occupational selection based on unobservable characteristics, there is no evidence in the data that selection on observables is an important concern.

Results

Effect on Earnings

Table 8 shows panel difference-in-differences estimates of the effect of privatization on wages for all workers from 2010 to 2013. The coefficient of interest is β ₃, the standard difference-in-differences estimator. Controls for gender and length of job tenure ($X_{i}^{\prime } {\Gamma }$ from Eq. 3) are omitted as they have essentially no effect on the results, and estimates that include them are reserved for the Appendix. Standard errors are reported in parentheses, which are clustered at the individual level. The difference-in-differences estimate of the treatment effect is $\hat {\beta _{3}}= -2.508$ per hour. The estimate is highly statistically significant, and represents a 17.2 percent loss in average wages for the treated workers.³³ As expected, liquor privatization resulted in significant earnings losses among displaced public employees and resulted in sharply lower wages during the post-policy period.

Table 8 Panel difference-in-differences estimates of the treatment effect of privatization on wages, all workers, 2010-2013

Figure 3 shows quantile regression results for treatment effects throughout the conditional wage distribution. The colored line plots estimates of β ₃ for quantiles ranging from the 5th to the 95th percentile, in 5-percent increments. The grey band plots the 95-percent confidence interval around these estimates. For comparison, the mean OLS treatment effect and confidence interval from Table 8 is shown as a horizontal dashed line in the figure. The impact of privatization varied widely throughout the wage distribution, with the most severe wage losses occurring in the lowest quintiles. All quintiles below the 60th percentile suffered larger wage losses than the mean, with losses of −$4.62 per hour or 32 percent for the most heavily affected workers at the 5th percentile. By contrast, wages at the 80th, 90th and 95th percentiles were essentially unaffected by the privatization. This is suggestive that low-wage workers were disproportionately adversely affected by the privatization, and that mean effects mask considerable heterogeneity among workers. This evidence is consistent with previous literature on the effect of wage compression in public-sector labor markets. Studies generally find employees at the bottom of the public-sector pay scale enjoy a large earnings advantage relative to private-sector workers at similar points on the earnings distribution, while public employees at the top of the earnings distribution enjoy little or no earnings advantage (see Gregory and Borland 1999 for a discussion of this literature).

Fig. 3

Quantile treatment effects for all displaced workers, 2010-2013

Effects in Subsamples

Effects by Gender

Tables 9 and 10 show results separately for male and female employees. Previous research has found female public employees tend to exhibit somewhat larger public sector wage rents than men (Gregory and Borland 1999). Table 9 presents results for men only, consisting of 63 treated individuals and 35 control individuals observed over 4 periods, for panel of size N T = 392. The estimated treatment effect for men is $\hat {\beta _{3}} = -2.200$ per hour, a 15.1 percent reduction in average hourly wages. The estimate is roughly 31 cents per hour smaller than for all workers, although the two figures are not statistically different.³⁴ Figure 4 presents quantile regression results for male workers. The size of treatment effects shows considerably more heterogeneity than in the full sample, with sharply different outcomes for workers at the tails of the distribution. The largest negative effects were concentrated in the lowest quantiles, with males at the 5th percentile experiencing treatment effects of −$4.225 per hour or a 29 percent drop in wages. However, male workers above the 65th percentile had a statistically zero treatment effect on wages from displacement.

Fig. 4

Quantile treatment effects for male workers only, 2010-2013

Table 9 Male workers only: panel difference-in-differences estimates of the treatment effect of privatization on wages, 2010-2013

Table 10 Female workers only: panel difference-in-differences estimates of the treatment effect of privatization on wages, 2010-2013

Table 10 shows results for female workers only. The sample consists of 80 treated individuals and 84 control workers observed over 4 years, for a panel of size of N T = 656 observations. The mean treatment effect for female workers is $\hat {\beta _{3}} = -2.871$ per hour, a 19.7 percent reduction in average wages. The effect of displacement on females is 36 cents larger than all workers, and 67 cents larger than for male workers, suggesting women’s earnings were disproportionately affected by job displacement. This is consistent with the presence of somewhat larger public sector wage premiums among female employes reported in past literature, although the difference between male and female treatment effects is not statistically significant. Figure 5 shows quantile regression results for female workers. Unlike males, treatment effects are more homogeneous and uniformly negative throughout the conditional wage distribution. The lowest quantiles suffered larger wage losses than the upper quantiles, but treatment effects were negative and significant for all quantiles examined. Women in the 5th percentile experienced wage declines of −$5.007 per hour, a 34 percent average decline, while those in the 95th percentile experienced losses of −$1.586 per hour, an 11 percent decline.

Fig. 5

Quantile treatment effects for female workers only, 2010-2013

Effects by Occupation, Age, Race and Education

Table 11 shows treatment effects for a variety of worker subsamples. Column (1) repeats the overall treatment effect for all workers as a comparison. Columns (2) to (10) show treatment effects for workers who found employment in a variety of industries during the post-policy period: those who remained in liquor retailing, those who were employed in other government agencies, those who worked in union-represented jobs, and so on. These subsample treatment effects serve as the basis for the decomposition of wage rents in the following section. Treatment effects varied widely by post-policy industry, from an insignificant −$0.223 per hour for those in non-union government jobs to a highly significant −$4.433 per hour for those in non-liquor-related retail jobs.

Table 11 Treatment effect of job displacement on wages in various subsamples, 2010-2013

Columns (11) to (15) show treatment effects for young, middle-age and older workers, as well as for white and non-white employees. The point estimate for younger workers aged 18 to 34 years of −$3.576 per hour is more than one dollar per hour larger than for middle aged or older workers, although it is not statistically different. White and non-white workers suffered similar wage losses from the policy, with slightly larger losses of −$2.568 per hour for white employees compared with −$2.211 per hour for non-white workers. Columns (16) to (20) show treatment effects by level of education. Wage losses from the policy were monotonically decreasing in years of education, ranging from −$3.894 per hour for those with a high-school diploma or less, to −$1.098 per hour for those with some graduate school or above. As with many labor market outcomes, the severity of the effect of job displacement on wages is strongly correlated with workers’ prior educational attainment.

Results for Wage Rent Decomposition

Table 12 presents the four subsamples from Table 11 used for the wage rent decomposition. Column (2) contains workers who remained in liquor retailing jobs (industry r _l ); Column (7) contains workers who moved into union-represented government jobs (industry g _u ); Column (8) contains workers who moved into non-union-represented government jobs (industry g _n ); and Column (10) contains workers who moved into union-represented, non-government jobs (industry u _n ). For each subsample, the table shows treatment effects and the type of wage rent(s) identified. Using these four subsamples there are ₄ C ₃ = (4!)/(3!(4−3)!) = 4 ways to decompose wage rents as the solution to a system of three equations in three unknowns. In order of reliability from largest to smallest sample size, Method 1 uses Columns (2), (7) and (10) to decompose wage rents based on labor market information from 73 treated individuals as follows:

$$\begin{array}{@{}rcl@{}} \begin{array}{rcccccccccc} \text{Column (2): \ \ } &E(\beta_{3} \mid D, T, I = r_{l}) &=& -2.054 &=E(& w_{U} & + & w_{G} & & &)\\ \text{Column (7): \ \ } &E(\beta_{3} \mid D, T, I = g_{u}) &=& -0.300 &=E(& & & & & w_{F} &)\\ \text{Column (10): \ \ } &E(\beta_{3} \mid D, T, I = u_{n}) &=& -2.319 &=E(& & & w_{G} & + & w_{F} &) \end{array} \end{array} $$

(6)

Method 2 uses treatment effects from Columns (2), (8) and (10) for 68 treated individuals:

$$\begin{array}{@{}rcl@{}} \begin{array}{rcccccccccc} \text{Column (2): \ \ } &E(\beta_{3} \mid D, T, I = r_{l}) &=& -2.054 &=E(& w_{U} & + & w_{G} & & &)\\ \text{Column (8): \ \ } &E(\beta_{3} \mid D, T, I = g_{n}) &=& -0.233 &=E(& w_{U} & & & + & w_{F} &)\\ \text{Column (10): \ \ } &E(\beta_{3} \mid D, T, I = u_{n}) &=& -2.319 &=E(& & & w_{G} & + & w_{F} &) \end{array} \end{array} $$

(7)

Method 3 uses estimates from Columns (2), (7) and (8) for 58 treated individuals:

$$\begin{array}{@{}rcl@{}} \begin{array}{rcccccccccc} \text{Column (2): \ \ } &E(\beta_{3} \mid D, T, I = r_{l}) &=& -2.054 &=E(& w_{U} & + & w_{G} & & &)\\ \text{Column (7): \ \ } &E(\beta_{3} \mid D, T, I = g_{u}) &=& -0.300 &=E(& & & & & w_{F} &)\\ \text{Column (8): \ \ } &E(\beta_{3} \mid D, T, I = g_{n}) &=& -0.223 &=E(& w_{U} & & & + & w_{F} &) \end{array} \end{array} $$

(8)

Finally, Method 4 uses treatment effects from Columns (7), (8) and (10) for 29 treated individuals:

$$\begin{array}{@{}rcl@{}} \begin{array}{rcccccccccc} \text{Column (7): \ \ } &E(\beta_{3} \mid D, T, I = g_{u}) &=& -0.300 &=E(& & & & & w_{F}&)\\ \text{Column (8): \ \ } &E(\beta_{3} \mid D, T, I = g_{n}) &=& -0.233 &=E(& w_{U} & & & + & w_{F} &)\\ \text{Column (10): \ \ } &E(\beta_{3} \mid D, T, I = u_{n}) &=& -2.319 &=E(& & & w_{G} & + & w_{F} &) \end{array} \end{array} $$

(9)

Table 12 Subsample treatment effects used to decompose lost wage rents

Table 13 shows the results of the decomposition. The rows corresponds to the four decomposition approaches described above, presenting separate estimates for union wage premiums w _U , public sector wage premiums w _G , and a residual wage premium attributable to lost industry-specific human capital w _F . Under all four approaches, the sum of lost wage rents is consistent with the overall treatment effect above, ranging from −$2.24 per hour to −$2.35 per hour, compared with the overall treatment effect of −$2.508 per hour. Wage losses attributable to public sector rents are by far the largest, accounting for −$2.02 to −$2.13 per hour or roughly 86 to 91 percent of total wage losses following privatization. Industry-specific human capital accounts for the second largest component, ranging from −$0.24 to −$0.30 per hour or roughly 11 to 13 percent of the total. Union premiums were negligible in all four decompositions, accounting for just −$0.03 per hour of wage losses using the first approach and a slightly negative union premium of between 2 and 8 cents in the remaining three approaches. The results are consistent with the presence of a roughly 16 percent public sector wage premium among the displaced WSLCB workers.³⁵

Table 13 Estimated decomposition of wage rents earned by former WSLCB employees

Conclusion

The issue of public employee compensation has long been controversial. Despite a well-established literature finding public sector wage premiums among federal workers, the evidence for the roughly 5.3 million state government employees currently employed in the United States remains mixed. This study contributes to the literature by providing new estimates of public sector wage rents for state employees based on quasi-experimental evidence from a 2012 privatization of liquor retailing in Washington State.

Based on a panel difference-in-difference estimator, I find that wages of state employees displaced by privatization fell roughly −$2.508 per hour or 17.2 percent relative to a similar group of public employees unaffected by the policy, with somewhat larger effects for female workers. By decomposing this overall effect into public sector wage rents, union premiums and losses due to industry-specific capital I find evidence of a roughly 16 percent public sector wage premium. The results are unaffected by the inclusion of controls for gender and length of job tenure; by excluding workers who reported a higher value of non-wage “fringe” benefits in post-policy jobs; and when estimated via a propensity score kernel matching estimator.

The finding of a roughly 16 percent public sector wage premium is considerably larger than estimates reported by previous longitudinal studies that do not rely on exogenous job separations, suggesting endogenous job switching may be a source of significant downward bias these estimates. However, the findings are broadly consistent with other studies that have examined earnings of government workers following privatization-related displacements in Brazil, Argentina and elsewhere. Although the estimated wage premium for liquor retail workers may not easily generalize to broader categories of state workers, it may be informative to other U.S. states considering privatization of liquor retailing.

Appendices

Appendix

Pre-Policy Wage Trends 2005 to 2013

Fig. 6

Evolution of pre-policy wages for treated and control workers, 2005-2013

Treatment Effects Including Worker Covariates

Table 14 shows treatment effects of displacement on wages including individual-level covariates for gender and job tenure, which are omitted from the baseline estimates presented in the paper. The figures correspond directly to my estimating Eq. 4 and are presented separately for all workers, males, and females. The additional covariates are shown in the first two rows. In the regression for all workers in Column (1), gender and length of job tenure are statistically insignificant. Job tenure is statistically significant only in the model restricted to female workers, in which case it has a small effect of $0.17 per hour. Overall, the point estimates for treatment effects $\hat {\beta _{3}}$ are identical to those that omit individual covariates presented in the paper.

Table 14 Panel difference-in-differences estimate of treatment effect, including gender and job tenure covariates, 2010-2013

Treatment Effects with Kernel Matching Difference-in-Differences Estimator

Table 16 shows estimated treatment effects of displacement on wages using a propensity score kernel matching difference-in-difference estimator. Table 15 shows the results of the first stage of the procedure in which individual characteristics are used to estimate treatment likelihoods. In the second stage, the resulting propensity scores are used to kernel match treated individuals to a composite group of control group members based on the epanechnikov kernel with a default bandwidth of 0.06. Overall, the procedure results in somewhat larger estimated treatment effects of −$2.790 per hour for all workers, and −$2.425 and −$2.926 per hour for males and females, respectively. However, none of the results are statistically different from the OLS difference-in-differences estimates presented in the paper.

Table 15 First stage propensity score estimation: estimated probability of treatment conditional on observables, 2010-2013

Table 16 Second stage: kernel matching difference-in-differences estimates of the treatment effect, 2010-2013

Treatment Effects Excluding Workers with Higher Value of Post-Policy Fringe Benefits

Table 17 shows treatment effects of displacement on wages excluding from the sample the 8 individuals who reported receiving more valuable non-cash “fringe” benefits in their post-policy employment. The estimates address the concern that observed wage losses among displaced WSLCB workers may have been partially or completely offset by increases in post-policy non-wage benefits. On the contrary, estimated wage losses are somewhat larger when the sample is restricted to workers reporting the same or less valuable fringe benefits (−$2.809 per hour compared with −$2.508), suggesting substitution between cash and non-cash compensation does not explain the pattern of treatment effected reported in the paper.

Table 17 Treatment effect of job displacement on wages, excluding individuals who reported higher value of fringe benefits post-policy, 2010-2013

Treatment Effects Including Voluntary Job Separators

The paper’s baseline estimates exclude all individuals from the sample who voluntarily separated from their WSLCB job prior to the policy enactment date of June 1, 2012. Table 18 shows treatment effects including in the sample the 10 individuals for whom wages are observed in all pre-policy years and who voluntarily separated. The treatment effect of job displacement is a somewhat smaller −$2.342 when these individuals are included, suggesting voluntary quitters fared better on average than involuntarily displaced workers. This is consistent with ordinary job shifting behavior that is unrelated to the policy change, as voluntary separators likely quit to accept higher wage offers elsewhere.

Table 18 Treatment effect of job displacement on wages, including individuals who voluntarily quit prior to the policy date of June 1, 2012, 2010-2013

Survey Materials

A copy of the survey questionnaire of displaced WSLCB workers is provided below. Information on institutional review board approval by the University of California, San Diego’s Human Research Protections Program is available at http://irb.ucsd.edu/.