Recall bias in the displaced workers survey: Are layoffs really lemons? Younghwan Song Union College June 2006 Abstract This paper examines how the extent of recall bias in the Displaced Workers Surveys affects the often-cited empirical results found by Gibbons and Katz (1991) for the lemons effect of layoffs. Their finding that workers displaced by layoffs experience larger wage losses than do those displaced by plant closings is not due to the stigma attached to the layoff events. Rather it partly stems from recall bias in the 1984 and 1986 DWS, but mostly reflects the fact that workers displaced by layoffs have significantly higher predisplacement wage-tenure profiles than do those displaced by plant closings, while there is no such difference in postdisplacement wage-tenure profiles. A similar analysis using the 2000 and 2002 DWS shows that predisplacement wage losses are not different between workers displaced by layoffs and those displaced by plant closings. JEL Classification: J31, J63 Keywords: lemons effect of layoffs, recall bias, wage-tenure profiles I am grateful to Todd Idson, Brendan O Flaherty, Steve Cameron, Lawrence Kahn, Robert Gibbons, Ozgen Sayginsoy, and participants at the 2005 Society of Labor Economists meetings in San Francisco for valuable comments. I also thank Kevin Lang (editor) and two anonymous referees for helpful suggestions. Any remaining errors are mine. Correspondence: Department of Economics, Union College, Schenectady, NY 12308; E-mail: songy@union.edu.
1. Introduction Recall bias arises when the quality of survey data is affected because respondents forget less salient events from the distant past and fail to report them. The longer the recall period, the larger is the loss in the accuracy of data on less salient events (Neter and Waksberg 1964; Mathiowetz and Duncan 1988; Pierret 2001). While any piece of survey data could be subject to recall bias to a certain degree, the problem just might be critical with the biennial Displaced Workers Survey (DWS) because it collects information about worker displacement over a long recall period of five years (three years, starting with the 1994 DWS). This paper examines how the extent of recall bias in the DWS affects the often-cited empirical results found by Gibbons and Katz (1991) for the lemons effect of layoffs. Using data from the 1984 and 1986 DWS, they showed that white-collar workers displaced by layoffs receive lower postdisplacement wages and thus incur larger earnings losses than those displaced by plant closings. Finding no such effect of layoffs among blue-collar workers, Gibbons and Katz asserted that a layoff event from white-collar jobs signals the low ability of a worker because white-collar jobs are less likely to be covered by layoff-by-seniority rules than blue-collar jobs. However, given that less salient events, such as layoffs, are more likely to be forgotten and unreported than are more salient events, such as plant closings, the empirical results found by Gibbons and Katz are likely to be subject to recall bias. I show that in the subsample of workers displaced within two years prior to the survey date in the 1984 and 1986 DWS, contrary to the argument by Gibbons and Katz, blue-collar workers displaced by layoffs incur larger earnings losses than those displaced by plant 2
closings. And for the larger earnings losses incurred by workers displaced by layoffs, I provide an alternative explanation that workers displaced by layoffs have more to lose from the beginning, because they have significantly higher predisplacement wage-tenure profiles than do those displaced by plant closings, while there is no such difference in postdisplacement wage-tenure profiles. Finally, I show that in the recent 2000 and 2002 DWS, wage losses do not differ by cause of displacement. 2. The lemons effect of layoffs Gibbons and Katz (1991) have introduced a signaling model where a layoff event reveals the low ability of a worker to the market because firms lay off workers with low ability if they have discretion over whom to lay off. The model predicts that as a result, even though the predisplacement wages of observationally equivalent workers do not differ by cause of displacement, workers displaced by layoffs still have lower postdisplacement wages and thus incur larger wage losses than those displaced by plant closings. Using data from the 1984 and 1986 DWS, Gibbons and Katz showed empirical results consistent with the predictions of their model, the lemons effect of layoffs. They found that white-collar workers displaced by layoffs have significantly lower postdisplacement weekly earnings and larger earnings losses than do white-collar workers displaced by plant closings, while predisplacement earnings do not vary with cause of displacement. For blue-collar workers, no such difference is observed in the postdisplacement earnings. Gibbons and Katz ascribed the difference between whitecollar and blue-collar workers to the fact that blue-collar jobs are more likely to be 3
covered by unions, and unions often enforce layoff-by-seniority rules under collectivebargaining agreements. 1 Subsequent empirical studies testing the lemons effect of layoffs by means of various data sets have produced divergent results. Using data drawn from the Canadian Survey of Displaced Workers, Doiron (1995) confirmed that white-collar workers displaced by layoffs earn less in postdisplacement jobs than do those displaced by plant closings. When changes in wages are compared, however, the difference is not significant, even among non-union white-collar workers. Finding no lemons effect of layoffs among blue-collar workers regardless of union status, she concluded that it is the occupational breakdown that is important in explaining the presence of the lemons effect of layoffs, not the extent of unionization. Stevens (1997), using the Panel Study of Income Dynamics (PSID), also found that wage loss is larger for workers displaced by layoffs than for those displaced by plant closings. According to her, however, the real reason here is not that laid-off workers have lower wages after displacement but that they have higher wages prior to displacement, as compared to workers displaced by plant closings. She showed that it is because workers displaced by plant closings have very large wage reductions prior to the displacement, while those displaced by layoffs have no such reductions before displacement. Grund (1999) presented further evidence against the lemons effect of layoffs. Using the German Socio-Economic Panel, he found that wage loss is not larger for workers displaced by layoffs, even among white-collar workers, than those displaced by 1 The 1984 and 1986 DWS provide no information on unionization at an individual level. 4
plant closings. He partly ascribed the different results for Germany, as compared with the United States and Canada, to the differences in labor-market institutions. Lastly, Krashinsky (2002) provided a different explanation than the lemons effect of layoffs for the difference in earnings losses by cause of displacement. Using a sample drawn from the National Longitudinal Survey of Youth, he also found that workers displaced by layoffs suffer larger wage losses than those displaced by plant closings. According to Krashinsky, however, the reason laid-off workers suffer larger wage losses is not because a layoff event reveals the lower ability of a worker, but rather because laidoff workers have more to lose from the beginning because they have been displaced from larger establishments with higher wages. When he controlled for establishment size, the difference in wages losses between the two groups of displaced workers disappeared. The fact that most subsequent studies except Doiron (1995) have disproved the lemons effect of layoffs, and given that less salient events, such as layoffs, are more likely to be forgotten and unreported than are more salient events, such as plant closings, the empirical results found by Gibbons and Katz are likely to be subject to recall bias and should be reexamined. 3. Recall bias in the DWS The problem of recall bias might be critical with the 1984 and 1986 DWS because of the long recall period. The surveys asked respondents if, in the prior five years, they had lost or left a job owing to a plant closing, slack work, a position or shift abolished, or other reasons. Then, from those who answered affirmatively, detailed retrospective information about the predisplacement job was collected, including tenure and earnings. 5
In fact, the problem of recall bias is a highly familiar one to researchers using the DWS. Carrington (1990) was the first to show evidence of recall bias, doing so by comparing overlapping years from the 1984 and 1986 DWS. 2 He found that layoff events are less likely to be remembered and reported, especially if they occurred in the distant past, than are such relatively distinct events as plant closings. Topel (1990), comparing displaced-worker samples from the 1968-1985 waves of the PSID and the 1984 and 1986 DWS, indeed found that a larger proportion of displacements are caused by plant closings in the DWS than in the PSID. 3 Furthermore, he showed that displacement events reported in the DWS, as compared to those in the PSID, on average involve jobs with longer tenure. Evans and Leighton (1995), using the 1984, 1986, 1988, and 1990 DWS, have confirmed that recall bias is not random: individuals are more likely to forget displacement if they are less educated, have fewer years of tenure, are in the lowest-paid jobs, and are white-collar. 4 Recently, Oyer (2004), matching a survey similar to the DWS with personnel records from a firm, verified that displaced workers tend to slightly overstate predisplacement earnings whereas there is no bias in reported tenure. The lack of a validation data set for the DWS does not allow one to completely resolve the problem of recall bias. Nevertheless, in an effort to alleviate the problem of recall bias, researchers using the 1984 and 1986 DWS often restricted their analysis to the 2 To examine the quality of a data set, one needs a validation data set. As no such data set is available, however, for the 1984 and 1986 DWS, he used the three overlapping years from the 1984 and 1986 DWS. 3 The PSID is less likely to be subject to recall bias than the DWS because the PSID is panel data and displacement information is collected from a yearly survey. 4 Gibbons and Katz were aware of the problem of recall bias in the DWS. They acknowledged that if recall bias is a more serious problem in the case of workers displaced by layoffs, there is a possibility that recall bias explains their results. They rejected such a possibility, however, for three reasons. One of them is that recall bias cannot explain their different results for white-collar versus blue-collar workers. See the appendix in Gibbons and Katz (1989) for details. 6
sample of displaced workers who were displaced within two years prior to the survey date (Farber 1993; de la Rica 1995; Fairlie and Kletzer 1998). By restricting the sample in this way, they excluded the displacement events that happened long before the survey date and also eliminated any problems that might arise from the overlapping coverage of years of displacement in the two surveys with varying recall periods. 4. The layoffs-and-lemons sample In this section, I first replicate the regression results by Gibbons and Katz (1991) and then investigate how their results change in the restricted sample of displaced workers who were displaced within two years prior to the survey date. Panel A of Table 1 shows my replication of Table 3 of Gibbons and Katz (1991: 365). Using the same sample selection criteria described in their article, I have used a similar sample size and arrived at almost identical coefficients. 5 I too have found that workers displaced through layoffs experience approximately 4 percent larger wage reductions than do workers displaced by plant closings. When the sample is divided by occupation, the wage reduction is even stronger, among white-collar workers, for workers displaced by layoffs than for those displaced by plant closings. The explanatory factor 5 Because the program Gibbons and Katz used for their paper is unavailable, I have had to rely solely on the description in their paper for sample selection and earnings equations. The sample of displaced workers used in the analysis consists of male workers between the ages of 20 and 61 who were permanently displaced from a private-sector, full-time job owing to a plant closing, slack work, or a position or shift that was eliminated, and had been reemployed as of the survey date in wage and salary employment with reemployment earnings of at least $40 a week. Workers displaced from agricultural and construction jobs were excluded from the sample. Appendix Table A1 reports descriptive statistics of the sample. Compared with Gibbons and Katz, the difference in earnings equations is that tenure and its square are used instead of a spline function for previous tenure. The fact that some of the displaced workers are excluded from the sample because they are not reemployed as of the survey date could produce sample selection bias in the estimates. However, the Heckman sample-selection bias-correction method cannot be the solution in this case because there is no variable in the DWS that affects the probability of reemployment but does not affect earnings, and the Heckman estimates are quite poor when there is no valid exclusion restriction (Sartori 2003). 7
here is the significantly lower postdisplacement earnings of workers displaced by layoffs, as predicted by the lemons-effect-of-layoffs model. Among blue-collar workers, no such difference is observed by cause of displacement. These results appear to be nicely supportive of the lemons effect of layoffs. However, given the problem of recall bias in the 1984 and 1986 DWS reported in the previous section, there is a clear need to reexamine the lemons effect of layoffs in terms of recall bias. To minimize the problem of recall bias, therefore, a subsample of workers who were displaced within two years prior to the survey date has been used for the estimation of earnings equations in Panel B of Table 1. In the first row of Panel B, the additional wage reductions for workers displaced by layoffs, as compared to those displaced by plant closings, have increased to about 6 percent when the whole sample is used. In the sample of white-collar workers, workers displaced by layoffs still incur about 5 percent more earnings losses than do those displaced by plant closings, though now the difference is insignificant. What is most remarkable in Panel B of Table 1 is that the coefficient on the layoff dummy variable is now larger and significant among blue-collar workers in the wagechange equation of column 1. Differing from the prediction made by the lemons-effectof-layoffs model by Gibbons and Katz, Panel B s larger earnings losses for blue-collar workers displaced by layoffs do not arise from significantly lower postdisplacement earnings. Nevertheless, they do refute the prediction made by Gibbons and Katz that no lemons effect of layoffs would be observed among blue-collar workers owing to the difference in coverage by layoff-by-seniority rules. 8
Given the problem of recall bias noted in the previous section, the changes in the coefficients on layoff dummy in column 1 in Panel B suggest that it could be recall bias that explains why no support for the lemons effect of layoffs has been found among bluecollar workers in Panel A of Table 1. As a way to better examine this possibility, I have used two tests: the Hausman test and the Chow test. 6 Under the null hypothesis that there is no loss of data accuracy due to recall bias among the workers displaced between three to five years prior to the survey date, the estimators using the full sample of displaced workers are both consistent and efficient, whereas the estimators using the restricted sample of workers displaced within two years prior to the survey date are merely consistent. Therefore, one can apply a Hausman test to compare the overall regression coefficients from these two samples, including the coefficients on layoff dummy reported in Panels A and B. Alternatively, one can also employ a Chow test to examine the equality of the coefficients for the workers displaced between three to five years prior to the survey date and for those displaced within two years prior to the survey date. Panels C and D of Table 1 report the Chi-square statistics and p-values from the Hausman test and the F-statistics and p-values from the Chow test, respectively. It is apparent that the substantive results of the two tests are identical. In the cases of the wage change equations in column 1 and the postdisplacement earnings equations in column 3, one cannot reject the null hypothesis in both tests. In the case of the predisplacement earnings equations in column 2, however, the null hypothesis is rejected in both tests for the whole sample and the blue-collar sample, whereas it is not rejected for the white-collar sample. 6 I am very grateful to Kevin Lang for suggesting these tests. 9
Taken as a whole, Panels C and D indicate that, consistent with Oyer (2004), recall bias is a problem of loss of accuracy in reporting predisplacement earnings, but not in other features of lost jobs included as the independent variables in the estimation, presuming that postdisplacement earnings from current jobs are unlikely to suffer from recall bias. One more remarkable finding from these two tests is that the loss of accuracy due to recall bias does vary by occupation. Even though blue-collar workers are less likely to forget displacement events than white-collar workers (Evans and Leighton 1995), the former seem to be less accurate in reporting predisplacement earnings than the latter. Thus, it is neither the occupational difference in coverage by layoff-by-seniority rules as cited by Gibbons and Katz, nor the occupational breakdown itself as argued by Doiron (1995), but rather recall bias that seems to be causing the difference by occupation in the lemons effect of layoffs, especially in the 1984 and 1986 DWS. 5. Difference in wage-tenure profiles Once I had put aside the occupational differences, I found that workers displaced by layoffs still incur larger earnings losses than do the observationally equivalent workers displaced by plant closings in both Panels A and B of Table 1. This does not necessarily mean, however, that the lemons effect of layoffs is working, as Gibbons and Katz have proposed. When it comes to this phenomenon of the larger earnings losses incurred by workers displaced by layoffs, one can provide an alternative explanation based on the conventional explanation for earnings losses of displaced workers, as opposed to one based on signaling as done by Gibbons and Katz. 10
It is a well-known fact that displaced workers lose a substantial portion of their returns to tenure on the predisplacement job, since displacement and ensuing job changes rarely carry over job-specific attributes, regardless of whether the returns to tenure come as a result of shared rents, good job matches, or firm-specific human capital (Addison and Portugal 1989a, b; Kletzer 1989; Topel 1991). That is why displaced workers with longer tenure on the predisplacement job suffer larger wage losses. In addition to the length of tenure, the height of wage-tenure profiles also affects wage losses of displaced workers. If workers displaced by layoffs had higher wages due to higher returns to tenure than those displaced by plant closings, wage losses might then be larger for workers displaced by layoffs. The explanatory factor here, however, is not the signaling effect based on different cause of displacement but rather simply the fact that workers displaced by layoffs have more to lose right from the moment of displacement. Workers displaced by layoffs may have higher wage-tenure profiles than those displaced by plant closings for the following two reasons: First, laid-off workers tend to be displaced from larger firms than those displaced by plant closings (Kranshinsky 2002) and the returns to tenure are relatively higher in larger firms (Black, Noel, and Wang 1999; Hu 2003). 7 Second, workers displaced by plant closings have very large wage reductions prior to the displacement, while those displaced by layoffs have no significant wage reduction before displacement (Stevens 1997). Using the subsample of workers who were displaced within two years prior to the survey date, Table 2 presents the results of the attempt to test this hypothesis of differences in earnings losses after displacement. In addition to the coefficient on the 11
layoff dummy variable, in order to measure the differences in wage-tenure profiles, the coefficients on the interaction terms between the layoff dummy and predisplacement job tenure and its square in earnings equations are shown for each sample. The last row for each sample shows the percent differences in wage changes, predisplacement wages, and postdisplacement wages, calculated using these coefficients, at the mean level of tenure. In the wage-change estimation for the whole sample of displaced workers in column 1, both interaction terms between the layoff dummy and predisplacement job tenure and its square are statistically significant, with the expected signs. These results show that the larger wage reductions observed in Panel B of Table 1 for workers displaced by layoffs are due to the fact that these workers incur greater losses for their predisplacement job tenure than do comparable workers displaced by plant closings. 8 In fact, Gibbons and Katz also gained similar results in their Table 4 (1991: 368), where they reestimated earnings regressions after replacing the layoff dummy with two interaction terms between the layoff dummy and the two predisplacement tenure dummies a low-tenure dummy for predisplacement tenure less than two years and a high-tenure dummy for predisplacement tenure of at least two years. For low-tenure workers, regardless of occupation, they found no significantly different effect of a layoff in earnings losses, but for high-tenure workers displaced by layoffs in both the whole sample and the sample of white-collar workers, they found significantly larger earnings losses. The explanation provided by Gibbons and Katz is that the information content of 7 Unfortunately, the DWS do not provide information on the predisplacement firm size. 8 When the coefficients in column 1 are used, at the mean level of tenure (= 4.52 years), workers displaced by layoffs incur about 9 percent (= 0.004-0.025 * 4.52 + 0.0009 * 4.52 * 4.52) larger earnings losses than those displaced by plant closings. 12
a layoff is greater for laid-off workers with longer tenure because it takes some time for employers to gain fuller information about workers abilities. In order to distinguish between their signaling interpretation and mine the hypothesis of different predisplacement wage-tenure profiles by cause of displacement, one needs to compare the returns to predisplacement tenure in both predisplacement and postdisplacement jobs, in addition to earnings losses by predisplacement tenure level, between workers displaced by layoffs and those displaced by plant closings. For the signaling interpretation offered by Gibbons and Katz to be valid, predisplacement wagetenure profiles should not be different by cause of displacement, but postdisplacement wages should be lower for laid-off workers with longer predisplacement tenure. Column 2 in my Table 2 for the whole sample, however, shows that workers displaced by layoffs have significantly higher predisplacement wage-tenure profiles than do those displaced by plant closings. 9 And in column 3 one finds no significant difference in wage-tenure profiles in postdisplacement jobs, by cause of displacement. 10 In separate samples of white-collar and blue-collar workers, all three columns in Table 2 show the same pattern as those for the whole sample. Thus it can be asserted that it is not the difference in the information content of a layoff by predisplacement tenure level, but the difference in the height of predisplacement tenure profiles that causes the differences by cause of displacement in earnings losses, among the sample of displaced workers analyzed in this section. 9 At the mean level of tenure (= 4.52 years), workers displaced by layoffs have about 6 percent higher predisplacement wages than those displaced by plant closings. Between 2 and 25 years of tenure, the predisplacement wage levels of laid-off workers are higher than those of workers displaced by plant closings. 10 An F-test for the joint hypothesis that all coefficients on the three variables in column 3 are equal to zero could not be rejected at the 5 percent level of significance. In the separate samples of white-collar and blue-collar workers in Table 2, the F-test results are the same. 13
Without examining the differences in wage-tenure profiles by cause of displacement, it appears that workers with equivalent characteristics incur larger losses simply because they are displaced by layoffs. Workers are not equivalent in their predisplacement jobs, however. Those displaced by layoffs have more to lose when they are displaced than do those displaced by plant closings, because the former were receiving higher wages from their predisplacement tenure, which is unlikely to be recognized on the new job. 6. An analysis of the 2000 and 2002 Displaced Workers Surveys In order to reduce recall bias in the DWS, the retrospection period has been reduced to three years from five years beginning with the 1994 DWS. Given the findings in this paper that the lemons effect of layoffs is due partly to recall bias in the samples from the 1984 and 1986 DWS, it would be interesting to see if the lemons effect still exists in the more recent DWS with a shorter retrospection period. For this purpose, I employ the 2000 and 2002 DWS. The sample from the 2000 and 2002 DWS has been selected according to the same criteria described in footnote 5. Panels A and B of Table 3 show the results of testing the lemons effect of layoffs using the full sample of displaced workers and the restricted sample of workers displaced within two years prior to the survey date, respectively. The estimates vary slightly in Panels A and B but there is no evidence of the lemons effect of layoffs in both panels, regardless of occupation. When I tested whether predisplacement wage-tenure profiles are different by cause of displacement, though the results are not reported here, there was no evidence of higher predisplacement wage-tenure profiles for workers displaced by layoffs. It appears that the nature of 14
layoffs might have changed in recent years compared with the period covered by the 1984 and 1986 DWS. 11 Overall, the findings in Table 3 are yet consistent with the previous findings in this paper: When workers displaced by layoffs have higher wage-tenure profiles, they incur larger earnings losses than those displaced by plant closings. Otherwise, the earnings losses are not different between workers displaced by layoffs and those displaced by plant closings. Thus, it is the difference in the predisplacement wage-tenure profiles, not the lemons effect of layoffs, which determines the difference in wage losses among displaced workers by cause of displacement. 7. Conclusions In this paper I have shown that the differences by occupation in the lemons effect of layoffs found by Gibbons and Katz arise owing to recall bias, rather than because of the different coverage by collective-bargaining agreements by occupation. And the differences in predisplacement wage-tenure profiles among displaced workers, not the stigma attached to the layoff events, explain the overall differences in earnings losses between workers displaced by layoffs and those displaced by plant closings. In the sample drawn from the 2000 and 2002 DWS both predisplacement wage-tenure profiles and earnings losses are not different by cause of displacement. 11 In Appendix Table A1, there seem to be more educated workers and more white-collar workers among those displaced by layoffs in the 2000 and 2002 DWS than in the 1984 and 1986 DWS. Also while the years covered by the 1984 and 1986 DWS are mostly in recession periods, the years covered by the 2000 and 2002 DWS are mostly in expansion periods. 15
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Krashinsky, H., 2002. Evidence on adverse selection and establishment size in the labor market. Industrial and Labor Relations Review 56 (1), 84-96. Mathiowetz, N.A., Duncan, G.J., 1988. Out of work, out of mind: response errors in retrospective reports of unemployment. Journal of Business and Economic Statistics 6 (2), 221-229. Neter, J., Waksberg, J., 1964. A study of response errors in expenditures data from household interviews. Journal of the American Statistical Association 59 (305), 18-55. Oyer, P., 2004. Recall bias among displaced workers. Economics Letters 82 (3), 397-402. Pierret, C.R., 2001. Event history data and survey recall: an analysis of the national longitudinal survey of youth 1979 recall experiment. Journal of Human Resources 36 (3), 439-466. Sartori, A.E., 2003. An estimator for some binary-outcome selection models without exclusion restrictions. Political Analysis 11 (2), 111-138. Stevens, A.H., 1997. Persistent effects of job displacement: the importance of multiple job losses. Journal of Labor Economics 15 (1), 165-188. Topel, R., 1990. Specific capital and unemployment: measuring the costs and consequences of job loss. Carnegie-Rochester Conference Series in Public Policy. 33 (Autumn), 181-214. Topel, R., 1991. Specific capital, mobility, and wages: wages rise with job seniority. Journal of Political Economy 99 (1), 145-176. 17
Table 1 Coefficients on layoff dummy in earnings equations from the 1984 and 1986 DWS, males reemployed at survey date Sample N Wage Change (1) Panel A: All Displaced Workers Whole sample 3,439 -.037** (.018) White collar 1,183 -.051* (.028) Blue collar 2,256 -.025 (.023) Panel B: Workers Displaced within Two Years Prior to the Survey Date Whole sample 1,557 -.062** (.026) White collar 579 -.047 (.041) Blue collar 978 -.067** (.034) Panel C: Hausman Test Whole sample 37.49 (.2706) White collar 27.14 (.4564) Blue collar 25.75 (.6387) Panel D: Chow Test Whole sample 1.29 (.1289) White collar 1.09 (.3440) Blue collar 1.05 (.3939) Dependent Variable Predisplacement (2).018 (.014) -.008 (.025).025 (.018).034 (.021).014 (.037).039 (.026) 56.94** (.0043) 21.61 (.7567) 50.81** (.0052) 1.79** (.0048) 0.87 (.6424) 1.71** (.0131) Postdisplacement (3) -.017 (.017) -.059** (.030).004 (.022) -.029 (.026) -.032 (.044) -.029 (.033) 35.49 (.3561) 28.84 (.3686) 30.58 (.3855) 1.17 (.2349) 1.11 (.3148) 1.17 (.2477) NOTE: The reported regressions include previous tenure and its square, education, a dummy for advance notification of displacement, year-of-displacement dummies, eight previous-industry dummies, eight previous-occupation dummies, experience (age-education-6) and its square, a marriage dummy, a nonwhite dummy, and three region dummies. Columns 1 and 3 also include years since displacement. The whitecollar sample consists of workers with predisplacement jobs as managers and administrators, professional and technical workers, clerical workers, or sales workers. The blue-collar sample consists of workers with predisplacement jobs as craft and kindred workers, operatives, laborers, transport operatives, or service workers. Earnings are deflated by the GDP deflator. The numbers in parentheses are standard errors in Panels A and B and p-values in Panels C and D. Dependent variable: col. (1) = log (current weekly wage/previous weekly wage); col. (2) = log (previous weekly wage); col. (3) = log (current weekly wage). * Statistically significant at the.10 level. ** Statistically significant at the.05 level. 18
Table 2 Comparison of coefficients on the interactions of layoff dummy and predisplacement job tenure in earnings equations from the 1984 and 1986 DWS, males displaced within two years prior to survey date and reemployed at survey date Sample Whole sample (N=1,557) White collar (N=579) Blue collar (N=978) Dependent Variable Variable Wage Change Predisplacement Postdisplacement (1) (2) (3) Layoff.004 -.023 -.019 Layoff tenure (.038) (.032) (.039) -.025**.022** -.003 (.010) (.009) (.011).0009** -.0008**.0000 Layoff tenure square (.0004) (.0004) (.0004) Difference at the mean tenure (4.52 years) -.091.061 -.031 Layoff.071 -.067.005 Layoff tenure (.060) (.054) (.065) -.039**.027* -.012 (.016) (.015) (.017).0010 -.0007.0003 Layoff tenure square (.0006) (.0005) (.0007) Difference at the mean tenure (4.36 years) -.079.037 -.042 Layoff -.020 -.006 -.026 Layoff tenure (.050) (.039) (.049) -.027*.026** -.001 Layoff tenure square Difference at the mean tenure (4.61 years) (.014).0015** (.0007) (.011) -.0015** (.0005) (.014).0000 (.0007) -.112.082 -.030 NOTE: The reported regressions include previous tenure and its square, education, a dummy for advance notification of displacement, year-of-displacement dummies, eight previous-industry dummies, eight previous-occupation dummies, experience (age-education-6) and its square, a marriage dummy, a nonwhite dummy, and three region dummies. Columns 1 and 3 also include years since displacement. The whitecollar sample consists of workers with predisplacement jobs as managers and administrators, professional and technical workers, clerical workers, or sales workers. The blue-collar sample consists of workers with predisplacement jobs as craft and kindred workers, operatives, laborers, transport operatives, or service workers. Earnings are deflated by the GDP deflator. The numbers in parentheses are standard errors. Dependent variable: col. (1) = log (current weekly wage/previous weekly wage); col. (2) = log (previous weekly wage); col. (3) = log (current weekly wage). * Statistically significant at the.10 level. ** Statistically significant at the.05 level. 19
Table 3 Coefficients on layoff dummy in earnings equations from the 2000 and 2002 DWS, males reemployed at survey date Sample N Wage Change (1) Panel A: All Displaced Workers Whole sample 1,510.004 (.027) White collar 780.004 (.038) Blue collar 730 -.0004 (.041) Panel B: Workers Displaced within Two Years Prior to the Survey Date Whole sample 1,110 -.007 (.032) White collar 576 -.008 (.044) Blue collar 524 -.0007 (.050) Dependent Variable Predisplacement (2).026 (.026).012 (.039).045 (.036).012 (.031) -.023 (.046).052 (.042) Postdisplacement (3).033 (.026).019 (.045).049 (.038).005 (.035) -.031 (.053).046 (.045) NOTE: The reported regressions include previous tenure and its square, three education dummies, a dummy for advance notification of displacement, year-of-displacement dummies, eight previous-industry dummies, eight previous-occupation dummies, age and its square, a marriage dummy, a nonwhite dummy, and three region dummies. Columns 1 and 3 also include years since displacement. The white-collar sample consists of workers with predisplacement jobs as managers and administrators, professional and technical workers, clerical workers, or sales workers. The blue-collar sample consists of workers with predisplacement jobs as craft and kindred workers, operatives, laborers, transport operatives, or service workers. Earnings are deflated by the GDP deflator. The numbers in parentheses are standard errors. Dependent variable: col. (1) = log (current weekly wage/previous weekly wage); col. (2) = log (previous weekly wage); col. (3) = log (current weekly wage). * Statistically significant at the.10 level. ** Statistically significant at the.05 level. 20
Appendix Table A1 Descriptive statistics for the sample of displaced workers 1984 and 1986 DWS 2000 and 2002 DWS Variable Plant Closing Layoff Plant Closing Layoff Log weekly earnings 5.95 5.93 6.49 6.52 Age at displacement 33.04 30.96 37.01 36.36 Tenure in years 5.87 3.73 5.64 4.38 White collar.34.34.49.54 Education in years 12.42 12.80 Less than high school.07.07 High school graduate.34.30 Some college.33.34 College or higher.26.30 Number of observations 1,620 1,819 651 859 NOTE: Weekly earnings are in 1986 current dollars for the sample from the 1984 and 1986 DWS and in 2002 current dollars for the sample from the 2000 and 2002 DWS, deflated by the GDP deflator. Because of the changes in educational attainment questions in the Current Population Surveys since 1992, four educational categories, instead of years of education, are reported for the 2000 and 2002 DWS. 21