Does measurement error bias xed-effects estimates of the union wage effect?

Transcription

1 OXFORD BULLETIN OF ECONOMICS AND STATISTICS, 63, 4 (2001) Does measurement error bias xed-effects estimates of the union wage effect? Joanna K. Swaffield Centre for Economic Performance, London School of Economics. I. Introduction The estimation of the union wage differential has become increasingly re ned as improved data have become available. Just as micro-level data heralded the start of improved estimates over those using aggregate data the availability of individual-level panel data offered a further improvement. However, whereas estimates of the union wage effect were undoubtedly improved by the use of cross-section individual-level rather than aggregate data, the equivalent advantage of panel over cross-section estimates is far less clear. If the observed union wage differential is a result of systematic productivity differences between union and non-union workers and some or all of these productivity differences are not observed in the data, cross-section estimates of the union wage differential will be biased. This bias can potentially be removed through the estimation of the union wage differential with panel data or by simultaneous equation methods, which control for unobserved heterogeneity. Unfortunately, simultaneous equation methods require an instrument that is correlated with union status but not with the wage. The generation of persuasive estimates of the union wage differential under these models requires the instruments to be convincing. The alternative method of controlling for unobserved heterogeneity, by using panel data, does not require instruments. However, this does not mean that the panel I thank Steve Nickell, Mark Stewart, an anonymous referee and seminar participants at the Centre for Economic Performance, London School of Economics and the Manchester Labour Economics seminar, Department of Economics, University of Manchester for helpful comments, and the ESRC Corporate Performance Programme of the Centre for Economic Performance for nancial support. The BHPS data used in this paper were collected by the ESRC Research Centre on Micro-social Change at the University of Essex and made available through the ESRC Data Archive. Neither bears any responsibility for the analyses or interpretations presented here. 437 # Blackwell Publishers Ltd, Published by Blackwell Publishers, 108 Cowley Road, Oxford OX4 1JF, UK and 350 Main Street, Malden, MA 02148, USA.

2 438 Bulletin estimates of the union wage effect are automatically superior to cross-section estimates. Comparisons of cross-section and panel estimates of the union wage effect have been well documented in the US literature (see Mellow (1981), Mincer (1983), Freeman (1984), Jakubson (1991) and Card (1996)), tending to conclude that cross-section estimates are upwardly biased (Lewis (1986)). However, the evidence also suggests that xed-effects estimates tend to be biased downwards. For instance, Freeman (1984), using data from the CPS, NLS, PSID and QES, shows xed-effects estimation to suffer from potentially severe measurement error that biases downwards panel estimates. Card (1996), using an estimation method that explicitly accounts for misclassi cation error in reported union status, nds that `for the sample as a whole the [measurement-error] corrected [longitudinal] estimator is almost identical to the cross-sectional wage gap (17% versus 15±16%)' (pp. 974). Mincer (1983), using PSID and NLS data, nds panel estimates to be smaller than cross-section union estimates but highlights the problem of union changes without job changes. This leads Mincer (1983) to conclude that `the gures for job stayers who change union status appear to be in ated by misreporting or misclassi cation' (pp. 222). Whether the general conclusions in the US literature are fundamentally different for the British labour market is an empirical question. Relatively little research has yet been undertaken to investigate this owing to the lack of data. However, in recent work Andrews et al. (1998a), using the New Earnings Survey Panel Data set (NESPD) 1978 and 1985, nd that crosssection estimates of the wage effect of coverage are approximately 4 percent and xed-effects panel estimates are 2 percent. 1 Hildreth (1999), using data from the BHPS waves 1 and 5 for private sector male and female employees, concludes that `male workers are union members from positive selection in the production sector, but negatively selected in the service sector' (pp.15). For women, union membership appears to result from negative selection, where in both cases union membership is conditional upon union coverage. Blanch ower (1997), using the BHPS waves 1, 2 and 3, presents evidence that cross-section estimates of union membership are upwardly biased. Using data from the British Household Panel Survey (BHPS) waves 1 to 6 (1991±1997), this paper investigates whether the general conclusions from the US literature, on comparisons of cross-section and xed-effects estimates of the union wage effect and the impact of measurement error, hold for British data. 1 Coverage is de ned as the employee being covered by a negotiated collective agreement, which affects pay and/or conditions of employment. In the BHPS coverage is de ned as if `there is a trade union or similar body such as a staff association recognized by your management for the negotiating pay or conditions for the people doing your sort of job in your workplace '.

3 Does measurement error bias xed-effects estimates of the union wage effect? 439 II. Data, Sample and Variables De nitions The two regression samples used throughout the paper are unbalanced panel samples of female employees and male manual full-time employees. 2 Results for both the female employee and male manual full-time employee samples are presented for two main reasons. Firstly, although the most often used sample for union wage effect estimation is male manual workers, unions raise the relative wages of lower paid workers of whom women make up a larger proportion than men. Secondly, choosing these two samples provides a comparison between one (the male manual full-time employee sample) which could be argued to suffer from sample selection bias and the other (the full female employee sample) possibly open to criticism on the basis of false homogeneity assumptions. 3 Each sample includes employees (not full-time students) who were original sample members aged 18±65 with no missing or imputed data. 4 The wage equation is a function of human capital variables including age at which the person last left full-time education, potential labour market experience, tenure length with the employer, along with controls for type of rm in which employed (such as rm size and occupation). 5 The wage measure is (log) gross average (nominal) hourly earnings, with wave dummies included for each wave other than the base group. 6 Male manual employees are the `traditional' sample for estimating the union wage effect. Historically unions have had a greater power base and been more active within the (lower paid) manual rather than non-manual occupations. This distinction is particularly so for men as the manual and non-manual occupations are strongly indicative of type of employment in terms of skill, educational attainment and remuneration etc. At rst sight the argument for restricting the sample to full-time workers may appear less compelling as the dependent variable is de ned as the hourly wage and a part-time control could have been included in the wage equation (as in the female regression). However, including the part-time employees would have 2 The unbalanced panel sample has a minimum of two wage observations per individual. With xed-effects estimators the minimum number of observations per individual has to be two, otherwise the individual would just drop out of the model. The unbalanced rather than balanced panel sample was chosen for analysis due to the information loss and potential sample selection bias that is present within balanced panel samples. 3 Although the female sample will not suffer from the potential sample selection bias caused by restricting the employee group to only manuals, there still remains the possibility that the female sample suffers from sample selection bias caused by the participation decision. 4 Only original sample members were included, as these were the individuals, in the households, that were randomly selected at the start of the BHPS. 5 See Appendix A, Table A.1 for a full list of variables and sample means. 6 Using hourly rather than weekly earnings may slightly raise the union wage differential as union workers tend to work fewer hours per week on average than non-union workers (Oswald & Walker (1993), Stewart & Swaf eld (1997)).

4 440 Bulletin yielded relatively small gains in sample size at the expense of a potential increase in the heterogeneity of the sample. By contrast, the female sample includes full-time, part-time, manual and non-manual employees. Firstly, the full-time/part-time distinction was ignored on the grounds that (unlike for men) the exclusion of part-time female employees would have been likely to cause a serious sample selection bias in the panel, since women are more likely to move between these states over a working lifetime and within this six period panel. Secondly, both manuals and non-manuals were included in the sample as the distinction between the two groups was considered to be far less marked (in terms of skill, wage etc) than for male employees. Non-manual women tend to be at the lower skill end of the non-manual group, and so their earnings are similar to those of manual workers. As a result the distinction between the union wage effects for manual and non-manual workers is not as apparent for females as it is for males. 7 In each wave of the BHPS employees are surveyed concerning their union status. In waves 1, 5 and 6 the employment section union questions were put to all employees. Unfortunately in waves 2, 3 and 4 this was not the case: only those employees who changed job/position since 1 st September of the previous year and/or were not surveyed in the previous wave were asked all the union status questions as part of the employment questionnaire. This produced a serious discontinuity in the BHPS survey data, with implications for panel use of the union status data. However, in each of waves 1 to 5 an additional union membership question was asked, as part of the `values and opinions'section of the BHPS questionnaire. The questions in the employment section of the BHPS permit the construction of union variables for union coverage (cover) and union membership (member). The second membership question (in the BHPS values and opinions section) permits a second separate variable to be constructed to measure union membership (member V). For all six BHPS waves, the best measure of union status available is union membership (taken from the values and opinions section of the BHPS questionnaire). 8 7 For example, the raw union membership wage differential (calculated as a percentage of the non-union wage) for the female employee pooled cross-section sample is similar across the six occupational groups. The raw union membership wage differential is approximately 24.4% for professionals, 36.7% for intermediate non-manuals, 36.0% for foreman and skilled manuals, 26.3% for semi-skilled manuals, 11.2% for unskilled manuals and 6.8% for agricultural workers. Overall the raw female manual union membership wage differential is 28.5% compared to the raw nonmanual union membership wage differential of 36.5%. By contrast, for men we have a raw union membership wage differential of 22.8% for manual workers and 10.4% for non-manual. 8 Its worth noting that all wave 6 `member V' values are replaced by the union membership (member) value from the employment section. This is because the values and opinions section did not include the second trade union membership question at wave 6. Although this will produce a degree of discontinuity, due to the question de nitions, this was felt to be outweighed by the sample size improvements and having a full panel of the rst six BHPS waves.

5 Does measurement error bias xed-effects estimates of the union wage effect? 441 For waves 1, 5 and 6 information is available on both the employee's union status in terms of membership of the union and whether the union covers them for the purpose of collective bargaining. Therefore, three additional union status groups can be de ned, these are `covered member' (tmcv), `covered non-member' (ntmcv) and the base group of `uncovered' (regardless of membership status). These are important union variables to consider as analysis of the union wage differential at the establishment points towards those with a closed shop or high union density having an aboveaverage differential. At the individual-level, whilst members and non-members doing the same job in the same establishment will earn the same, when comparing across establishments membership will be a closer indicator of the differential than coverage. In short, the conditional probability of a closed shop or high union density is greater given membership than given coverage. 9 III. Estimates of the Union Wage Effect In estimating the union wage effect the rst question to address is: which union wage effect to estimate ± the impact of union coverage, union membership or membership conditional upon coverage? The second question is: which estimator to use ± cross-section OLS, between-effects, randomeffects or xed-effects? Some general points concerning the choice between these estimators should rst be made. For example, is the xed-effects or random-effects the superior panel estimator? The fundamental difference between the estimators is that the random-effects estimator assumes that there is no correlation between the explanatory variables and the unobservables. If part of the union wage differential is due to higher productivity workers having union status, the unobservable will be correlated with the union status variable. If this is the case the assumption of the random-effects estimator will be violated and the estimates will not be consistent and ef cient. A second general point relates to comparisons between pooled OLS and panel estimates. If the errors in the pooled OLS equation are correlated across individuals across time the residuals will not ful l the classical linear regression (CLR) assumption of being identical and independently distributed (i.i.d). This problem could be dealt with in a number of ways. One is to separate the waves of data in the pooled sample into separate equations such that for each individual there is only one wage observation in each equation. 9 The basic problem is that coverage multiplied by density is a potentially important omitted variable. If density at the establishment was observed then this effect could be convincingly controlled for. See Andrews et al (1998b) for discussion of this point.

6 442 Bulletin Alternatively, the equation could be estimated using the between-effects estimator, where an average of each variable in the equation is taken for each individual across all the time periods. 10 A third approach is to estimate the original OLS equation under a Generalized Least Squares (GLS) equation. 11 If the standard errors in the classical linear regression are not i.i.d then the off diagonals of the variance-covariance matrix will not equal zero. The GLS equation minimizes a weighted sum of squared residuals rather than the sum of squared residuals as in the CLR. In Table 1 estimates of the union wage effect for the female (manual and non-manual, full-time and part-time) and male manual full-time employee OLS TABLE 1 Estimates of the Union Wage Effect Between-effects Random-effects (GLS) Fixed-effects (1) (2) (3) (4) Waves 1-6 Female employees Member V (9.19) (4.28) (7.92) (4.82) Adj. R Hausman (1978) test ± ± 2 (30) ˆ 658:66 a ± Sample 8,673 8,673 8,673 8,673 Male manual full-time employees Member V (8.34) (4.39) (6.22) (3.64) Adj. R Hausman (1978) test ± ± 2 (27) ˆ 140:91 a ± Sample 3,187 3,187 3,187 3, All between-effects estimates based on the unbalanced panel sample use weighted least squares (WLS) rather than OLS. Both methods produce consistent estimates. The estimates are not substantially affected by this choice. It is worth noting though that the between-effects estimator requires the same assumption of no correlation between the explanatory variables and the residuals, as does the random-effects (GLS) estimator. In fact, if this assumption does hold, the random-effects (GLS) estimator is more ef cient than the between-effects estimator as the between-effects estimator discards information over time in favour of simple sample means. 11 The GLS estimates can be considered as both panel and cross-section estimates. All that distinguishes GLS from the OLS estimates is that the OLS restriction that the residual does not contain a person effect, í i, is not applied in the GLS. In the GLS equation the random distribution applied to the standard residual or error is also applied to the person-speci c effect í i. To clarify further, the variance minimising weight (j) in the GLS equation is a function of the variance of person-speci c effect í i and the residual u i. If the variance of the person-speci c effect í i is assumed to equal zero (so í i is always equal to zero) j will also equal zero, and therefore the GLS equation is exactly equivalent to the OLS equation.

7 Does measurement error bias xed-effects estimates of the union wage effect? 443 OLS TABLE 1 (continued) Between-effects Random-effects (GLS) Fixed-effects (1) (2) (3) (4) Waves 1, 5 & 6 Female employees Tmcv (6.58) (3.82) (7.18) (5.07) Ntmcv (1.57) (0.80) (2.27) (2.45) Adj. R Hausman (1978) test ± ± 2 (28) ˆ 235:08 a ± Cover (4.83) (2.87) (5.26) (4.03) Adj. R Hausman (1978) test ± ± 2 (27) ˆ 232:22 a ± Member (6.77) (3.92) (7.13) (4.61) Adj. R Hausman (1978) test ± ± 2 (27) ˆ 242:93 a ± Member V (6.69) (3.88) (6.89) (4.38) Adj. R Hausman (1978) test ± ± 2 (27) ˆ 233:02 a ± Sample 3,457 3,457 3,457 3,457 Male manual full-time employees Tmcv (3.35) (2.08) (2.95) (1.19) Ntmcv (1.90) (0.47) (2.62) (2.51) Adj. R Hausman (1978) test ± ± 2 (25) ˆ 53:91 a ± Cover (3.37) (1.82) (3.44) (2.37) Adj. R Hausman (1978) test ± ± 2 (24) ˆ 52:88 a ± Member (3.45) (2.31) (2.94) (1.23) Adj. R Hausman (1978) test ± ± 2 (24) ˆ 314:13 a ± Member V (3.70) (2.22) (3.49) (2.09) Adj. R Hausman (1978) test ± ± 2 (24) ˆ 314:13 a ± Sample 1,220 1,220 1,220 1,220 Notes: a Null hypothesis of the Hausman (1978) test rejected at 1%. b Adjusted R-squared in the table refers to overall R-squared for random-effects (GLS), between R-squared for between-effects and within R-squared for xed-effects estimates. c Sample sizes refer to unbalanced panel samples and asymptotic t-ratios are in parentheses.

8 444 Bulletin samples are shown. In column 1 the OLS estimates of the various union wage effects are shown. These results con rm (as do the equivalent between-effects estimates) the standard result in the British literature, that the return to union membership is greater than the return to union coverage and the return to union membership conditional upon coverage (tmcv) is greater than coverage alone (ntmcv). For example, covered member (tmcv) and covered nonmember (ntmcv) wage effect estimates are (t-ratio 6.58) and (t-ratio 1.57) respectively for the female sample. While the equivalent sample wage effect estimates for union coverage and union membership are and respectively (both signi cant). For females the union membership (member V) wage effects are estimated under the random-effects (GLS) estimator and under the xed-effects estimator (both signi cant). For males the equivalent estimates are (random-effects) and ( xed-effects), again both signi cant. A comparison of panel estimates of union membership wage effects with the cross-section OLS estimates appears to provide evidence that the OLS estimates are upwardly biased, suggesting that unobserved heterogeneity is positively correlated with union status. 12 The xed-effects and random-effects (GLS) estimates of the covered member (tmcv) wage effect con rm the above ndings for males. Randomeffects (GLS) and xed-effects estimates of the union wage effect fall from the OLS estimates of to and respectively. In contrast, the estimates of the covered non-member (ntmcv) wage effect rises under both panel estimators. For women, both the covered member and covered nonmember wage effect estimates rise. These results suggest that OLS estimates are downwardly biased, implying that the unobserved heterogeneity is negatively correlated with union status. 13 Estimates of union coverage under cross-section and panel estimators show little change for either sample. For union membership, xed-effects estimates are below the OLS estimates for both samples. The GLS estimates are generally similar in magnitude and signi cance to those of the pooled OLS equation. The xed-effects estimates are smaller in signi cance and magnitude than the GLS (random-effects) estimates. Estimates for union member and covered union member suggest that unobserved heterogeneity is positively correlated with union status, leading to an upward bias in the cross-section estimates. The null hypothesis of the Hausman 12 These results are similar to those presented in Blanch ower (1997). BHPS union membership cross-section estimates across waves 1-3 are reported to fall from to for women under xed-effects estimators and from to for men. 13 The magnitude of these estimates for covered member are similar to those presented in Hildreth (1999) where the impact of membership conditional on coverage estimated under a xed-effects estimator is reported as for female workers.

9 Does measurement error bias xed-effects estimates of the union wage effect? 445 (1978) test, that (assuming correct model speci cation) there is no correlation between explanatory variables and unobservables, is rejected for all randomeffects (GLS) estimates in Table 1. Therefore, more weight should be placed upon the union wage effect estimated under the xed-effects rather than random-effects estimator. To summarize, if OLS estimates suffer from omitted variable bias (in particular unobserved heterogeneity bias) the estimates of the union wage effect will not be convincing. Estimating the wage equation with panel data should remove this potential bias, and comparisons with the cross-section estimates should provide evidence for the direction and magnitude of bias. Comparisons of the OLS and xed-effects estimates above would seem to suggest that OLS union wage effect estimates are upwardly biased. However, this conclusion relies on the xed-effects estimator producing unbiased estimates that are `superior' to those based on OLS. The remainder of the paper investigates whether this is likely to be the case by focussing on the impact of measurement error on xed-effects estimates. 14 IV. Measurement Error Bias in the Fixed-effects Estimates of the Union Wage Effect Measurement error will cause OLS and xed-effects estimates to be biased towards zero and inconsistent. 15 However, the measurement error bias is likely to be more exaggerated in the xed-effects estimates, for two reasons: random misclassi cation in two periods will produce a larger number of misclassi ed workers than in one period and, due to the small number of union changes that identify the xed-effects estimate of the union wage effect, the proportion of observations in error will be greater (Freeman (1984)). 16 In the remainder of the paper three main methods are used to reduce the (likely) measurement error in the union status variable: rstly by comparing responses from the two membership questions asked in the survey, secondly, by re-constructing the union variable over time so that changes in union status (observed after the initial period) only occur when the individual 14 A number of issues are also important here such as sample selection bias and identi cation (see Swaf eld (1998) for a discussion of these points). 15 The union status variable and the measurement error are negatively correlated. This correlation arises because when the union status variable equals 1 the measurement error will be 0 or 1 and when the union status variable equals 0 the measurement error will be 0 or The measurement error bias is exaggerated in the xed-effects estimates, as the variance of the true union status variable is less than the variance of the measurement error in the union changes. This is due to serial correlation in the union status variable across time and weak or no serial correlation in the measurement error.

10 446 Bulletin changes employer (and/or job), thirdly, by using averages to reduce the measurement error in the union status variables. 17 Measurement error in the union membership response Waves 1 and 5 of the BHPS questionnaire contain two questions on union membership asked unconditionally of all respondents. These two membership questions allow a check both of whether the individual is reporting consistently and whether we are measuring what we think we are. If the individual answered `yes' to the values and opinions section question on union membership (i.e. are you a member of a trade union) he or she should also have answered `yes' to whether they belong to a trade union or a similar body recognised by management for bargaining. This is because the values and opinions trade union membership question is a narrower de nition of membership, i.e. it applies only to trade unions and not to staff associations. Observations with answers (yes, no) to these questions are categorised as measurement error (mea 6ˆ 0). Answers (no, yes) suggest that the individual belongs to a staff association but not a trade union, and are labelled as meb 6ˆ 0. In Table 2, the impact of restricting the samples on the basis of the measurement error (meb) assessments are shown for waves 1 and For both female and male samples, the restriction of union membership to trade unions rather than trade unions and other staff associations increases the union impact on the wage under each of the union de nitions and under both the OLS and xed-effects estimators. These results suggest that the inclusion of worker organizations which are not formally de ned by the employee as trade unions result in a downward bias on the effect of the `trade union' on the wage. 17 The measurement error in the union status variables can arise from three sources. Firstly, individuals may misreport their true union status, secondly the interviewer may record the wrong response, and nally there may be errors in entering the response recorded by the interviewer into the data. In the case of the last two sources one can clearly see how misclassi cation of the true response can arise. In the case of the individual's own response it could be the case that a worker is covered by a union for the purposes of pay bargaining and is not aware of it, and likewise they may assume they are when they are not. Such incorrect reporting by the individual seems clearly possible. Individual errors in reporting union membership status are slightly less clear. If an individual is not a member, why would they think that they are? They could be a lapsed union member or they may think membership of some professional body is equivalent to that of a trade union when it is not. How the opposite reporting error arises is less clear. However, the important point is that very few misclassi cations are required for the measurement error to affect the xedeffects estimates as relatively few union changes drive the xed-effects estimates of the union wage effect. 18 As wave 6 of the BHPS does not contain the trade union membership question in the value and opinions section and waves 2, 3 and 4 do not contain unconditionally asked union questions in the employment sections.

11 Does measurement error bias xed-effects estimates of the union wage effect? 447 TABLE 2 Union Wage Effect Estimates with Measurement Error Sample Restrictions Full sample meb ˆ 0 OLS Fixed-effects OLS Fixed-effects Waves 1 & 5 Female employees Tmcv (4.56) (3.55) (4.78) (3.64) Ntmcv (1.93) (2.64) (1.87) (2.67) Adj. R Cover (3.83) (3.45) (3.67) (3.43) Adj. R Member (4.13) (2.45) (4.35) (2.39) Adj. R Sample 1,820 1,820 1,568 1,568 Male manual full-time employees Tmcv (4.09) (1.56) (4.34) (1.97) Ntmcv (1.98) (1.45) (2.02) (1.53) Adj. R Cover (4.00) (1.85) (4.19) (2.11) Adj. R Member (3.25) (1.14) (3.69) (1.49) Adj. R Sample Notes: a Adjusted R-squared in the table refers to within R-squared for xed-effects estimates. b Sample sizes refer to unbalanced panel samples and asymptotic t-ratios are in parentheses. c meb equals zero if the two membership question responses exclude membership of staff associations. Comparisons of similar questions concerning union membership highlight very few inconsistent responses. 19 Either there is very little measurement error or individuals respond consistently (although not necessarily correctly) when asked the same or very similar questions over a short period of time. Although this method of investigating measurement error was not very 19 Restrictions to the sample based on mea are not presented here, as very few individuals appear to have this form of identi ed measurement error. For the male manual full-time employee sample none of the responses to the two membership questions are inconsistent. For the female sample only four observations show this inconsistency in either wave 1 and/or 5 and estimates are the same if not extremely similar for the restricted sample (mea ˆ 0).

12 448 Bulletin enlightening, it did show that returns to formal trade union status appear slightly larger than those to any employee representation. Restricting union changes to those with employer and/or job changes A second method to identify measurement error bias in the union estimates is to restrict changes in the union status variable to only those that have a higher probability of being a true change ± those who change employers and/or jobs over the same period. 20 In Table 3, the union wage effect for each of the three union de nitions is shown for union changes restricted to those who also experience a change in employer and/or job change across the waves 1, 5 and 6 and waves 1 to 6 samples. For the female employee sample comparisons with Table 1 (the original estimates) suggests that the xed-effects estimates for covered member, coverage and membership (member and member V) are downwardly biased. For the male manual full-time sample, the xed-effects estimated returns to union membership (member V) and coverage increase quite considerably when the changes in union status are restricted. 21 Waves 2, 3 and 4 of the BHPS do not contain unconditionally asked questions in the employment section for trade union coverage and membership. However, if the union status is de ned as that of the rst observed period, with changes to this status only if an accompanying employer (and/or job) change occurred, (as in Table 3), the data in these three waves can be used. In Table 4 the estimated union wage effect, under the three de nitions of union, are shown for all six waves. Although these results cannot be compared with the unrestricted or `original' union estimates, they do provide an interesting comparison with the gures in Table 3. Table 4, with a larger sample size than Table 3 shows the female estimates to be smaller. In comparison, the male manual full-time estimates (under both xed-effects and OLS) appear downwardly biased in Table 3 (particularly in the case of union membership). De ning union changes to occur only when employer or job changes occur, a comparison of the measurement error described in the previous 20 The distinction between job and employer changes is that an individual who changes job does not have to change employer. Therefore all employer changes are job changes but not all job changes are employer changes. 21 An alternative method to including this adjusted union status variable in the wage equation would be to use an instrumental variable i.e. one correlated with the true union status variable but not the measurement error. Additional estimates (not presented here) were found that used this adjusted union status variable (i.e. union changes restricted to changes with employer and/or job change) as an instrument rather than as an alternative regressor. The results also provided evidence that (conditional upon the assumption of no correlation between measurement error and the instrument) measurement error biases downwards the xed-effects estimates of the union wage effect.

13 Does measurement error bias xed-effects estimates of the union wage effect? 449 TABLE 3 Union Wage Effect Estimates with Union Status Changes Restricted to Employer or Job Changers Female Male manual full-time OLS Fixed-effects OLS Fixed-effects Waves 1, 5 & 6 Union Ä if Employer Ä Tmcv (7.12) (4.75) (3.06) (0.63) Ntmcv (1.90) (1.43) (2.15) (2.98) Adj. R Cover (5.12) (3.48) (3.26) (2.27) Adj. R Member (7.17) (4.45) (2.48) (0.35) Adj. R Union Ä if Job Ä Tmcv (6.97) (5.34) (3.01) (0.60) Ntmcv (1.84) (2.36) (2.20) (3.18) Adj. R Cover (5.03) (4.20) (3.26) (2.27) Adj. R Member (7.00) (4.88) (2.40) (0.06) Adj. R Sample 3,457 3,457 1,220 1,220 Waves 1± 6 Union Ä if Employer Ä Member V (9.08) (3.14) (6.47) (4.34) Adj. R Union Ä if Job Ä Member V (9.67) (4.48) (6.78) (3.55) Adj. R Sample 8,673 8,673 3,187 3,187 Notes: a Adjusted R-squared in the table refers to within R-squared for xed-effects estimates. b Sample sizes refer to unbalanced panel samples and asymptotic t-ratios are in parentheses. section by deviation between the `member' and `member V' responses can also be made for waves 1 to 5. In Table 4, the restricted sample estimates for consistent union membership responses (mea ˆ 0) and the stricter de nition of union membership (meb ˆ 0) are shown for the full female and male

14 TABLE 4 Union Wage Effect Estimates with Union Status Changes and Measurement Error Sample Restrictions Waves 1±6 Waves 1±5 Waves 1±5 Waves 1±5 Full Full mea ˆ 0 meb ˆ 0 OLS Fixed-effects OLS Fixed-effects OLS Fixed-effects OLS Fixed-effects (1) (2) (3) (4) (5) (6) (7) (8) Female employees Tmcv (9.40) (5.08) (8.61) (4.79) (8.55) (4.76) (8.71) (4.59) Ntmcv (3.04) (4.28) (2.93) (4.36) (2.90) (4.34) (3.03) (4.40) Adj. R Cover (7.02) (5.56) (6.55) (5.49) (6.49) (5.46) (6.32) (5.43) Adj. R Member (9.56) (3.87) (8.74) (3.19) (8.70) (3.15) (8.74) (2.56) Adj. R Sample 7,838 7,838 6,598 6,598 6,591 6,591 6,092 6, Bulletin

15 Male manual full-time employees Tmcv (8.48) (4.07) (8.79) (4.87) (8.82) (4.89) (8.76) (4.91) Ntmcv (3.81) (3.52) (3.96) (3.61) (4.00) (3.64) (4.10) (3.60) Adj. R Cover (7.85) (4.88) (8.23) (5.53) (8.27) (5.56) (8.24) (5.56) Adj. R Member (6.99) (4.16) (7.15) (4.25) (7.17) (4.26) (6.93) (4.30) Adj. R Sample 2,865 2,865 2,404 2,404 2,402 2,402 2,341 2,341 Notes: a Adjusted R-squared in the table refers to within R-squared for xed-effects estimates. b Sample sizes refer to unbalanced panel samples and asymptotic t-ratios are in parentheses. c mea equals zero if the two membership question responses appear consistent. d meb equals zero if the two membership question responses exclude membership of staff associations. Does measurement error bias xed-effects estimates of the union wage effect? 451

16 452 Bulletin samples across waves 1 to 5. As before, restricting the sample to exclude the very small number of inconsistent (mea 6ˆ 0) answers makes very little difference. Restricting the sample to the stricter de nition of union membership (meb ˆ 0) reduces the sample by more, and generally indicates that the wage effects of formal trade unions are greater than those of employee organisations under both the OLS and xed-effects estimators. In summary, restricting changes in union status to those where an accompanying employer and/or job change also occurred generally increased the xed-effects estimates of the union wage effect. This result is consistent with measurement error causing a downward bias to xed-effects estimates, but has two caveats. Firstly, the observed changes in the magnitude of the union wage effect estimate are relatively small compared to the standard error. Secondly, it must be remembered that by restricting union changes in an attempt to remove some of the potential misclassi cation and misreporting of union status, some true changes will also be excluded. For example, recognition and de-recognition of a union for the purpose of pay bargaining will take place over time and such changes may well have an impact on an individual's wage between periods without an employer or job change having to occur. The same argument holds for membership changes, particularly if by joining (leaving) the union the individual takes the membership density above (below) a critical point at the establishment. Reducing measurement error through averaging The nal method used in this paper to investigate the degree of measurement error bias in the xed-effects estimates is reported in Table 5. This method was used by Chowdhury & Nickell (1985), who showed that by averaging across the union observations potential measurement error through misreporting and misclassi cation can be reduced. This is because measurement error exhibits no serial correlation itself but the actual union variable does. The measurement error bias falls because the variance of the averaged measurement error falls by more than the variance of the averaged union variable. The higher the serial correlation between the true union status across periods, the greater the relative change in the variance of the averaged measurement error and union variable. 22 In Table 5, the cross-section OLS and xed-effects estimates are shown for the balanced panel sample across waves 1 to A comparison with the 22 Estimates of the serial correlation coef cient for this balanced sample across waves 1 to 6 for the female employees and male manual full-time employees were and respectively. Both gures will be an understatement of the true serial correlation because of the measurement error. 23 The balanced panel was used so that the full three-year averages could be found.

17 Does measurement error bias xed-effects estimates of the union wage effect? 453 TABLE 5 Union Wage Effect Estimates with Union Status Measurement Error Reduced Through Averaging Actual variables 2 year averages (1991±1992), (1993±1994) and (1995±1996) 3 year averages (1991±1993) and (1994±1996) OLS Fixedeffects OLS Fixedeffects OLS Fixedeffects Waves 1-6 Female employees Member V (5.63) (1.82) (4.44) (2.43) (3.71) (2.23) Adj. R No. of observations 3,294 1,647 1,098 No. of individuals Male manual full-time employees Member V (4.24) (1.49) (3.23) (1.69) (3.10) (3.44) Adj. R No. of observations No. of individuals Notes: a Adjusted R-squared in the table refers to within R-squared for xed-effects estimates. b Sample sizes refer to balanced panel samples and asymptotic t-ratios are in parentheses. xed-effects estimates in column 1 (the original gures) clearly shows that the three-year average estimate of the union wage effect is higher for both the female and male manual full-time employee samples. The male estimate increases by a particularly large margin that may partly be due to the small sample size. If it is true that the measurement error in the union variable decreases as a longer period is used to calculate the average, one would expect the panel estimate of the union membership wage effect to decrease as the average becomes shorter. The results for the two-year average in Table 5 appear to con rm this. 24 To summarize, reducing measurement error by taking averages provides 24 These gures compare well with the estimates reported in Chowdhury & Nickell (1985) where the original xed-effects estimate of for union membership increased to (t-ratio 2.0) with a two-period xed-effects estimate using a three-year average. The union membership wage effect increased further to (t-ratio 3.0) when a four-year average was used.

18 454 Bulletin further evidence that measurement error in the union status variable causes a downward bias in the xed-effects estimates. Averaging decreased the measurement error and increased the returns to union status. The longer the period over which the average was taken, the greater the reduction in bias caused by measurement error. V. Conclusions This paper investigated the impact of estimating the union wage effect (variously de ned) for female employees and male manual full-time employees under cross-section and panel estimators, with data from the British Household Panel Survey, waves 1 to 6. The union membership (member V) wage effect is estimated as under both OLS and between-effects estimators for female employees across waves 1 to 6, the equivalent estimates for the male manual full-time employees being and Using union membership conditional upon coverage (tmcv) instead raises the estimate for women, but lowers it for men. Fixed-effects estimates of the union membership (member V) wage effect (across waves 1±6) were approximately half the cross-section estimates in both the female and male samples. Equivalent comparisons of the union wage effect estimates of membership (conditional upon coverage) across waves 1, 5 and 6, show similar reductions for the male manual full-time employees, but a slight increase for female employees. These results appear consistent with previous research (Blanch ower (1997), Hildreth (1999)) using the BHPS and are generally in line with union wage effect estimates in the British literature of between 3 and 19 percent (see Booth (1995)). Union wage effect estimates presented here (across different sample and estimators) range between 4 and 15 percent (approximately), where union status is de ned as coverage, membership or membership conditional upon coverage. The relative magnitudes of the cross-section and xed-effects estimates of the union wage effect would appear to suggest that cross-section estimates are upwardly biased. However two points need to be made. Firstly, the extent to which cross-section estimates can be argued to be biased by unobserved heterogeneity, through comparisons with xed-effects estimates, depends on the superiority of the xed-effects estimates. If the xed-effects estimates are themselves downwardly biased by measurement error, the divergence between the two estimates will be overstated, thus leading to inaccurate conclusions concerning the degree of bias in cross-section estimates. Secondly, the degree to which the panel estimates are smaller than the cross-section varies across samples and union de nitions. The potential importance of measurement error in biasing xed-effects estimates should not be underestimated as xed-effects estimates rely cru-

19 Does measurement error bias xed-effects estimates of the union wage effect? 455 cially on changes in union status. Even a relatively small amount of measurement error can have a considerable impact on the xed-effects estimates. Two methods used to reduce the measurement error seemed to con rm that xedeffects estimates were biased downwards. Firstly, reducing the measurement error through averages decreases the measurement error, thereby increasing estimates of the union wage effect. Secondly, restricting a change in union status to those with an accompanying employer change generally increases the returns to union status under the xed-effects estimator. Finally, it was found that formal trade unions have a larger impact on the wage than other employee organizations (such as staff associations). To conclude, panel estimates of the union wage effect have advantages over cross-section estimates, which are likely to suffer from unobserved heterogeneity bias. However, panel estimation also has disadvantages, most importantly the problem of measurement error in the union status variable. This will cause a downward bias in xed-effects estimates, thus overstating the divergence of the cross-section and xed-effects estimates of the union wage effect. As in the US study by Freeman (1984), there is evidence for the British labour market in the 1990s, that the cross-section and xed-effects estimates `bound the true impact of unionism' (pp. 24). Date of Receipt of Final Manuscript: May References Andrews, M. J. Bell, D. and Upward, R. (1998a). `Union coverage differentials: Some estimates for Britain using the New Earnings Survey Panel Data Set', BULLETIN, Vol. 60, pp. 47±77. Andrews, M. J. Stewart, M. B. Swaf eld, J. K. and Upward, R. (1998b). `The estimation of union wage differentials and the impact of methodological choices', Labour Economics, Vol. 5, pp. 449±74. Blanch ower, D. G. (1997). Changes in time in union relative wage effects in Great Britain and the United States. The labour market consequence of technical and structural change discussion paper no. 15, February. Oxford: Institute of Economics and Statistics, University of Oxford. Booth, A. L. (1995). The Economics of the Trade Union, Cambridge University Press, Cambridge. Card, D. (1996). `The effect of unions on the structure of wages: A longitudinal analysis', Econometrica, Vol. 64, pp. 957±79. Chowdhury, G. and Nickell, S. J. (1985). `Hourly earnings in the United States: Another look at unionization, schooling, sickness and unemployment using PSID data', Journal of Labor Economics, Vol. 5, pp. 38±69. Freeman, R. B. (1984). `Longitudinal analyses of the effects of trade unions,' Journal of Labor Economics, Vol. 2, pp. 1±26. Hausman, J. (1978). `Speci cation tests in econometrics,' Econometrica, Vol. 46, pp. 1251± 71.

20 456 Bulletin Hildreth, A. (1999). `What has happened to the union wage differential in Britain in the 1990's?' BULLETIN, Vol. 61, pp. 5±31. Jakubson, G. (1991). `Estimation and the testing of the union wage effect using panel data', Review of Economic Studies, Vol. 58, pp. 971±91. Lewis, H. G. (1986). Union Relative Wage Effects: A Survey, University of Chicago Press, Chicago. Mellow, W. (1981). `Unionism and wages: A longitudinal analyses', Review of Economics and Statistics, Vol. 63, pp. 43±52. Mincer, J. (1983). `Union effects: wages, turnover and job training', in Reid, J. D. Jr (ed.) New Approaches to Labor Unions (supplement no. 2 to Ehrenberg, R. G. (ed.) Research in Labor Economics ). JAI Press Inc., Greenwich, Connecticut. Oswald, A. and Walker, I. (1993). Labour supply, contract theory, and unions. University of Keele, mimeo, November. Stewart, M. B. and Swaf eld, J. K. (1997). `Constraints on the desired hours of work of British men', Economic Journal, Vol. 107, pp. 520±35. Swaf eld, J. K. (1998) `Wage differentials in the 1990s: Estimates of employer tenure, union status and gender wage effects and modelling issues in estimation', September, Ph.D. thesis, Department of Economics, University of Warwick, UK. Appendix 1 Variables and sample means TABLE A.1 De nition Waves 1, 5 & 6 Waves 1±6 Male manual full-time Female Male manual full-time Female Log of gross average hourly wage: weekly wage divided by usual paid hours (basic plus overtime) Union membership (employment section): `member' ± ± Union coverage: `cover' ± ± Covered union member: `tmcv' ± ± Covered non±member: `ntmcv' ± ± Union membership (values and opinions section): `member V' Union membership density at 2 digit industry level ± ± (member) Union membership density at 2 digit industry level (member V) Full-time employee dummy Public sector employee dummy Regional price index (log) Employer tenure in years Firm size base group (employees,25) Firm size dummy (employees 25±99) Firm size dummy (employees 100±499)