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

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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.

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Notes

  1. Extensive reviews of the literature on public sector wage premiums are available in Gregory and Borland (1999) and Ehrenberg and Schwartz (1986).

  2. See for example, Ezra Klein, “Public Employees Don’t Make More than Private Employees,” Washington Post, September 16, 2010 (http://voices.washingtonpost.com/ezra-klein/2010/09/public_employees_dont_make_mor.html); and Sita Slavov, “How Politicians Buy Votes By Doling Out Public Worker Benefits,” U.S. News and World Report, May 2, 2013 (http://www.usnews.com/opinion/blogs/economic-intelligence/ 2013/05/02/public-sector-employees-receive-generous-benefits-due-to-politics).

  3. An ideal comparison group would be a collection of similar private sector workers subject to a parallel exogenous mass layoff. However, this is an infeasible identification strategy. Private sector job displacements are rarely exogenous and are typically the result of adverse demand conditions affecting both layoffs and wages. However, unlike most literature on mass layoffs, a unique feature of my setting is that demand conditions were stable throughout the period. I exploit this feature to directly estimate public wage rents.

  4. These alternative estimates are presented in the Appendix.

  5. In Section “Assessing Bias in Wage Rent Decompositions Due to Selection into Post-Policy Occupation” I examine whether these results are driven by non-random selection of displaced workers into post-policy industries. I find no evidence that selection on observables such as education, work experience and gender explain the results.

  6. For example, Pennsylvania and Oregon are currently engaged in active political debates regarding the privatization of their state-run liquor retailing systems. See Kate Giammarise, “Pennsylvania liquor overhaul brews big spending,” Pittsburgh Post-Gazette (May 26, 2014), available at http://www.post-gazette.com/news/politics-state/2014/05/26/Pa-liquor-overhaul-brews-big-spending/stories/201405260074; and Harry Esteve, “Liquor privatization initiative moves forward,” The Oregonian (May 17, 2014), available at http://www.oregonlive.com/politics/index.ssf/2014/05/liquor_privatization_initiativ.html.

  7. It is worth noting that most federal studies do not present separate estimates wage premiums for postal and non-postal workers, despite the fact that pay among postal employees is based on collective bargaining and is determined separately from other federal employees. Separate analyses of postal workers tend to find larger wage premiums than among other federal workers (Hirsch et al. 1999).

  8. One area modern literature has made progress on is the inclusion of non-wage “fringe” benefits in the estimation of public sector wage premiums, which was largely neglected in early research due to data limitations.

  9. An important caveat is that industry-specific human capital cannot be easily differentiated from occupation-specific human capital, as many occupations are highly clustered within specific industries. See Neal (1995), pp. 669-70, and citations therein for a discussion of this point.

  10. For workers who remain in unionized jobs following privatization, I assume union wage premiums are preserved. However, it is possible that a loss of tenure when transferring between unions could also affect wages. Because length of job tenure at the time of displacement is perfectly collinear with individual fixed effects, I am unable to fully resolve this issue in the data.

  11. By “liquor” I refer only to distilled spirits. Beer and wine have long been privately retailed in the state and were unaffected by the privatization initiative.

  12. Following Washington’s privatization 18 states maintain public monopolies over liquor retailing and distribution. The remaining “control” states are: Alabama, Idaho, Iowa, Maryland (Montgomery and Worcester counties only), Maine, Michigan, Mississippi, Montana, New Hampshire, North Carolina, Ohio, Oregon, Pennsylvania, Utah, Vermont, Virginia, West Virginia, and Wyoming. Source: National Alcohol Beverage Control Association (http://www.nabca.org).

  13. The state also maintained 162 privately owned “contract” liquor stores primarily located in rural areas of the state. Contract stores remained in operation following privatization, but were required to purchase all remaining inventory from the state.

  14. See Austin Jenkins, “Costco Breaks Records With $22M To Privatize Liquor,” NPR, October 19, 2011 (http://www.npr.org/templates/story/story.php?storyId=141531406).

  15. See Melissa Allison, “Costco offers job interviews to displaced state liquor-store workers,” Seattle Times (November 10, 2011), available at http://seattletimes.com/html/localnews/2016734642_costco11.html.

  16. See Melissa Allison, “Unions sue to block liquor initiative from taking effect” (December 6, 2011), available at http://seattletimes.com/html/localnews/2016947384_liquorsuit07.html.

  17. The survey was granted institutional review board approval by the “Human Research Protections Program” at the University of California, San Diego on March 12, 2013. Information about the review process is available at http://irb.ucsd.edu/about.shtml. For reference, a complete copy of the survey recruitment letter and questionnaire is provided in the Appendix.

  18. See the U.S. Census Bureau’s “Quarterly Census of Employment and Wages,” Series ID ENU5300 050292.

  19. I address the issue of possible misreporting of wages by survey respondents in the following section.

  20. Respondents were asked, “If you are employed, think about the dollar value of your current [fringe] benefits. Are the worth less, more, or about the same as the benefits you received at your Washington State liquor retail job?”

  21. Workers who resigned early may have done so due to ordinary job shifting that was unrelated to the policy, such as the acceptance of a superior outside offer. In the Appendix show estimates including these 37 individuals, and doing so has no effect on the main results.

  22. Because post-policy wages are unobserved for unemployed individuals, they are excluded from the sample. If instead unemployed workers are included with their post-policy wage \(w^{*}_{post}\) set equal to zero, estimated treatment effects are roughly three times larger.

  23. By comparison, the longest possible panel length consists of N = 43 over T = 7 periods (N T = 301), a significantly smaller sample size.

  24. To further examine differences in wages between respondents and nonrespondents, I estimated the “reverse” of Eq. 2 by regressing wages on a dummy indicator of survey response and all other controls. In all specifications I find the coefficient on survey response is not statistically significant, suggesting no important differences in wages between respondents and nonrespondents. I am grateful to an anonymous reviewer for suggesting this robustness check.

  25. A second concern is possible misreporting of wages by survey respondents. Displaced workers who were politically opposed to privatization may have incentives to strategically misreport earnings to maximize apparent harm suffered from displacement. It is possible to verify reported pre-policy wages based on administrative records. Survey respondents were asked to report both wages just prior to displacement in June 2012 to allow for such a verification. The average self-reported pre-policy wage was $14.44 per hour. From administrative records, the actual average pre-policy wage for these same individuals was $14.18 per hour, a small difference of 26 cents. The remaining gap is likely due to timing differences between self-recall wages and official records, as administrative records are based on a snapshot of wages in early January while self-reported wages are based on self-recall from the pay period immediately preceding displacement in June. For post-policy wages, there is unfortunately no way to independently verify their accuracy and is an inherent limitation of the survey data.

  26. Human resources representatives from the WA DOL reported several cases of retail liquor clerks moving into licensing customer service jobs following privatization, further confirming the broad similarity of the two occupational categories (obtained via telephone on April 2, 2014).

  27. In contrast to much of the previous literature on public-private pay differentials, I estimate effects on direct dollar wages rather than the log of wages. As noted in Blackburn (2007) and Blackburn (2008) the use of log transformations can provide misleading results for public-private pay differentials when wage distributions are less dispersed in the public compared to the private sector, which is clearly the case in this study’s data. This point has also been emphasized in Gittleman and Pierce (2012) and Falk (2015).

  28. Rewriting the linear model from Eq. 3 as \(w_{i} = X_{i}^{\prime }\beta + \epsilon _{i}\), the Koenker and Bassett (1978) quantile estimator \(\hat {\beta }_{q}\) for the average treatment effect at quantile q is given as the solution to \(\hat {\beta }_{q} = \underset {\beta \in R^{k}}{\arg \min } {\sum }_{i=1}^{N} \rho _{q} (w_{i} - X_{i}^{\prime }\beta )\), where \(\rho _{q} = (q - \mathbb {1}\{w_{i}- X_{i}^{\prime }\beta <0 \})(w_{i}- X_{i}^{\prime }\beta )\) is the usual “check function” that penalizes positive regression residuals by q and negative residuals by 1−q.

  29. As detailed in Heckman et al. (1998) and Todd (2008), the resulting kernel-matching difference-in-difference estimator \(\hat {\beta }_{M}\) is given by \(\hat {\beta _{M}} = \frac {1}{n_{1}} {\sum }_{i \in I_{1}} \left \{ (w_{1ti} -w_{0t^{\prime }i}) - {\sum }_{j \in I_{0}} W(i,j)(w_{0tj} - w_{0t^{\prime }j})\right \}\), where I 1 is the set of treated workers, I 0 is the set of control workers, t ′ and t are the pre- and post-policy periods, w 1 and w 0 are earnings for the treated and control groups, and W(i,j) is a weighting function based on the epanechnikov kernel with the default bandwidth of 0.06.

  30. See Andrew Garber, “Gregoire and Unions Reach Agreement on Pay, Benefit Cuts,” Seattle Times (December 15, 2010), available at http://seattletimes.com/html/localnews/2013680687_paycuts15m.html.

  31. In the Appendix, I include a figure illustrating parallel pre-policy wage trends for the longer (but smaller NT) panel from 2005 to 2013 as well.

  32. This approach is equivalent to specifying dummy indicators for post-policy occupation, and including interaction terms in my basic estimating Eq. 3 for P o s t x T r e a t m e n t x O c c u p a t i o n. Doing so yields identical results.

  33. For percentage wage gaps, I use the mean wage of treated workers as the denominator. This can be interpreted as an estimate of the percentage that public-sector wages were reduced by the policy. If mean private-sector wages–which are are significantly lower–are used as a denominator instead, percentage effects are roughly 1.5 percentage points larger (e.g., an −18.7 percent treatment effect compared with the −17.2 percent effect in Table 8).

  34. The pairwise test statistic comparing treatment effects for all workers to male workers (\(\hat {{\beta _{3}^{A}}} = \hat {{\beta _{3}^{M}}}\)) is z A,M = −0.75. Comparing all workers to female workers (\(\hat {{\beta _{3}^{A}}} = \hat {{\beta _{3}^{F}}}\)), z A,F = 1.09. And comparing male workers to female workers (\(\hat {{\beta _{3}^{M}}} = \hat {{\beta _{3}^{F}}}\)), z M,F = 0.91.

  35. It is important to note that the finding of a roughly zero union wage premium is the result of there being no detectible private-sector union wage differential in my data. It is likely the results would find a larger union premium if my survey revealed a private-sector union pay differential similar to those found in national studies based on Current Population Survey data.

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Authors and Affiliations

  1. Department of Economics, University of California, San Diego, CA, USA

    Andrew Chamberlain

  2. Glassdoor, Inc., Mill Valley, CA, USA

    Andrew Chamberlain

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Correspondence to Andrew Chamberlain.

Appendices

Appendix

Pre-Policy Wage Trends 2005 to 2013

Fig. 6
figure 6

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

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

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/.

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Chamberlain, A. Are State Workers Overpaid? Survey Evidence from Liquor Privatization in Washington State. J Labor Res 36, 347–388 (2015). https://doi.org/10.1007/s12122-015-9212-1

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