Partial employment protection and perceived job security: evidence from France

Partial employment protection and perceived job security: evidence from France Abstract This paper assesses the causal effect of partial employment protection on workers’ subjective job security via the perceived probability of layoff. We consider the rise in the French Delalande tax, which is paid by private firms if they lay off older workers. This reform was restricted to large firms and therefore allows us to use a difference-in-differences strategy. In ECHP data, we find that the change in the perceived probability of layoffs induced by the higher Delalande tax improved the subjective job security of older (protected) workers, but at the cost of a negative externality on other workers. The changes in job security in both groups are of similar size, but as unprotected workers are the large majority of the sample, the population effect of the tax on layoffs was to reduce job security. 1. Introduction There is by now a great deal of empirical evidence that employment protection reduces worker flows.1 We here ask whether this affects workers’ perceived job security, both positively for those who are covered and negatively for those who are not. These are important questions, as we know that workers’ subjective evaluations of their job predict their labour-market behaviour (Freeman, 1978; Akerlof et al., 1988; Clark et al., 1998; Clark, 2001) and may affect firm outcomes such as productivity and profit (Harter et al., 2002). The existing empirical literature on the relationship between employment protection and the subjective perception of job security has mostly relied on cross-country analysis, and generally finds a negative correlation (Böckerman, 2004; Postel-Vinay and Saint-Martin, 2004; Clark and Postel-Vinay, 2009). This surprising result can be explained by the perverse effects of employment protection, in particular via less job creation. Subjective job security is related to both separations and hirings (Böckerman et al., 2011), via the transition probabilities between employment and unemployment. This paper complements existing work by using a natural experiment to assess the causal impact of partial employment protection on workers’ self-assessed job security, partial meaning here that all workers are not eligible for employment protection. We focus on changes in the perceived probability of layoff from a French employment-protection reform implemented in 1999: an increase in the Delalande tax, which is paid by private-sector firms if they lay off workers aged over 50 in permanent contracts. This 1999 rise was restricted to firms with more than 50 employees, and as such provides a natural quasi-experiment that can be analysed via difference-in-differences estimation. We consider private-sector workers with permanent contracts in European Community Household Panel (ECHP) survey data. These data cover the period 1994–2001. We should emphasize that this estimation does not allow us to examine the effect of the reform through job creation and perceived job-finding probabilities, as workers in large firms might be hired in small firms later on, and vice versa. We here assess the effect of partial protection through layoff probabilities only. Our main finding is that the change in the cost of layoffs from the higher Delalande tax led to greater feelings of job security for protected workers, but at the cost of less job security for other workers. The job security movements are of similar size for both groups, at 10% of a standard deviation. As there are far more unprotected than protected workers, the rise in the Delalande tax reduced aggregate job security. The largest fall in job security is for unprotected workers who are closer to 50, as this is the group that firms have the greatest incentive to lay off (before they become covered by the Delalande tax). There are different issues that our empirical analysis needs to address. We first need to rule out potential confounding French reforms. In 1998, the French Ministry of Labour announced that there would be a reduction of standard weekly hours from 39 to 35 hours in firms with over 20 employees; this reform was enacted in 2000. These expected changes may therefore have affected perceived job security in firms with over 20 employees in our ECHP data from 1998 onwards. We show, however, that the difference in subjective job security between firms with less than and more than 50 employees (which is the threshold for the Delalande tax) is also found when we drop workers from firms with under 20 employees (i.e. when we restrict the sample to include only firms that were subject to the 35-hour week). Potential minor changes in the French early retirement system are also considered. We prove in the robustness checks that these changes are not driving our estimates. Second, macro-economic trends may produce different changes in job security in large and small firms. We address this issue by taking advantage of the cross-country dimension of ECHP data. We replicate the identification strategy in bordering countries and show that the difference-in-differences estimates there are insignificant. Our results highlight that the perverse effects of partial employment protection on the perceived job security of unprotected workers may more than offset its beneficial effects on protected workers. In addition, as we do not consider the negative effects of protection on job creation, our estimates of these perverse effects constitute a lower bound. In addition, we also contribute to the literature by assessing the external validity of Ferrer-i-Carbonell and Frijters (2004). They conclude that assuming ordinality or cardinality in subjective well-being scores makes little differences in panel regressions. Our analysis differs on several aspects (dependent variable, dataset, and identification strategy), and we check and confirm the conclusion of Ferrer-i-Carbonell and Frijters (2004): we show that, once controlling for individual fixed effects, using linear or nonlinear models does not affect the sign and the significance of the treatment effects. The remainder of the paper is organized as follows. Section 2 presents the institutional background and the theoretical implications, while Section 3 describes the ECHP data that we use. Section 4 explains the empirical strategy, the results and the heterogeneity analysis appear in Section 5, and robustness checks are displayed in Section 6. Finally, Section 7 concludes. 2. Institutional background, theoretical implications, and expected impacts 2.1 Institutional background The Delalande tax was proposed and introduced in the French legislative system in 1987 to restore the financial balance of the unemployment-insurance system and reduce the rise in the layoffs of older workers. Despite numerous changes over time, the principle of the tax has remained unchanged: firms laying off workers of over a certain age have to pay the Delalande tax to the unemployment-insurance system. This tax is proportional to the worker’s gross wage and covers private-sector workers with permanent contracts. From 1987 to 1992, the tax amount was three months of gross wages for all workers aged over 55. The first major changes to this tax were introduced in July 1992. Table 1 shows how the tax profile has changed. In particular, in 1992 the tax started to depend on firm size, the age threshold of workers covered was lowered to 50, and the maximum tax amount increased to 6 months of gross wages. However, workers who were hired after age 50 and had been unemployed for at least 3 months were exempt from the tax. Additional changes to the tax scheme were made in January 1993 and January 1999. From 1993 to December 1998, the tax did not depend on firm size but only on the worker’s age. In January 1999, the tax was increased for firms with over 50 employees only. The tax was equal to 2 months of gross wages for 50-year-old workers and reached 12 months of gross wages for workers between age 56 and 57. This tax represents an important share of the total separation costs: Behaghel et al. (2004) estimate for instance the average French separation costs to be equal to almost 4 months of gross wages, while Abowd and Kramarz (2003) estimate these costs to be equal to 5 to 7 months of gross wages. Table 1 The Delalande tax scheme Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Source: Legislative texts. Note: For each age group, the table displays the tax due by the firm to the unemployment insurance system if it lays the worker off. The tax is a function of previous wages, and is stated in months of gross wage. Table 1 The Delalande tax scheme Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Source: Legislative texts. Note: For each age group, the table displays the tax due by the firm to the unemployment insurance system if it lays the worker off. The tax is a function of previous wages, and is stated in months of gross wage. The 1999 rise in the Delalande tax was announced by the French government one year beforehand. According to the article entitled ‘Pénalisation des licenciements des plus de 50 ans: le projet de Martine Aubry’ published in the French newspaper Les Echos in 1998, the increase in the Delalande tax was not expected, especially by unions, even though they were satisfied by this reform. The reintroduction of firm size discontinuity was publicly known for months by the end of 1998. This means that the timing of the reform is the following: the reform of the Delalande tax is announced in 1998, and this may translate into anticipation effects, while the actual impacts of the reform will be identified from 1999 onwards. 2.2 Theoretical implications of partial employment protection and expected effects on perceived job security Theoretical analysis (see among others Mortensen and Pissarides, 1999; Cahuc and Postel-Vinay, 2002) predicts that employment protection reduces job and worker flows. The intuition behind this is summarized in Cahuc and Postel-Vinay (2002): ‘Higher firing costs limit job destruction by making layoffs more expensive, while they also inhibit job creation by reducing the overall expected profitability of jobs’ (p.79). This prediction has been confirmed in a variety of empirical contributions.2 Following Mortensen and Pissarides (1994) and Pissarides (2000), Behaghel (2007) proposes a stochastic job-matching model that accounts for the Delalande tax.3 This tax reduces both the separation rate and the probability of a return to work for older workers, while it increases the separation rate and reduces the probability to return to work for younger workers. Behaghel et al. (2008) test these theoretical predictions on hirings and layoffs using French data from the Labour Force Survey. We here extend these predictions to workers’ perceived job security, and focus only on the separation channel: we specifically ask how the 1999 rise in the Delalande tax affected worker’s subjective job security by changing their perceived probability of layoff. We expect two effects in large firms as the tax rises. First, lower separation rates should increase the perceived job security of workers aged over 50. On the contrary, higher separation rates should reduce the job security of younger workers.4 On top of the 1999 rise in the Delalande tax, we may expect anticipation effects on perceived job security. With the reform being announced months before its implementation, we may expect employers to strategically adjust their labour demand. They may have the incentive to lay off workers around the 50-year-old threshold before the rise in the Delalande tax. 3. Data Our data come from the European Household Community Panel (ECHP). The ECHP is a longitudinal survey carried out in 14 European countries, including France. A nationally representative sample of household and individuals was interviewed each year between 1994 and 2001 in each country. In France, 15,000 individuals were surveyed per wave on average. The interviews mainly took place between October and December. The ECHP contains detailed information on socio-economic characteristics, incomes, employment conditions, social relations, and so on.5 The rise in the Delalande tax in 1999 only applied to workers aged over 50 in firms with over 50 employees. We identify the covered respondents in the ECHP by their reported age in the survey (we correct misreporting by comparing birth and interview dates). The size of the firm in which the respondent works, measured by the number of employees in the firm, is recorded in the following categories: ‘None’, ‘1 to 4’, ‘5 to 19’, ‘20 to 49’, ‘50 to 99’, ‘100 to 499’, and ‘500 or more’. The ECHP also contains a number of questions on job domain satisfaction. Subjective job security is our main dependent variable, and is measured by the following question: ‘How satisfied are you with your present job in terms of job security?’ Respondents answered on a 6-point scale, 1 meaning ‘Not Satisfied’ and 6 meaning ‘Fully Satisfied’. Fig. 1 shows the distribution of subjective job security. It can be seen that 70% of responses are 4 or 5. This negative skewness is commonly found for satisfaction measures. Fig. 1 View largeDownload slide The distribution of satisfaction with job security. Source: Own calculations. Fig. 1 View largeDownload slide The distribution of satisfaction with job security. Source: Own calculations. Our main sample consists of adult respondents working in the private sector with permanent contracts, and with valid information on job characteristics and perceived job security. We restrict the sample to workers who do not cross the age-50 threshold during the post-treatment sample period (i.e. who were born before September 1949 or after December 1951), and who were hired when under 50. We thus split the sample into two age groups with clear ‘treatment’ nature: workers who are either protected (older workers) or not protected (younger workers) during the whole post-reform sample period. This leaves us with 14,110 observations based on 3,003 individuals. The complete descriptive statistics appear in Tables A1 and A2 in the Supplementary Appendix. Table 2 The rise in the Delalande tax and perceived job security Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 2 The rise in the Delalande tax and perceived job security Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. 4. Identification strategy and empirical specification Our main goal here is to assess the causal effect of partial employment protection on workers’ subjective job security via changes in the perceived probability of layoff. In principle, workers below age 50 in firms with more than 50 workers might be considered to be the ideal control group. They would allow to compare workers above and below age 50 in firms of similar size before and after the reform. The age threshold is appealing; because it is exogenous, it cannot be manipulated. But the stochastic job-matching model used by Behaghel (2007) predicts that the Delalande tax is also likely to affect workers below age 50 in firms with more than 50 workers via higher separation rates. We therefore exploit the firm-size discontinuity of the 1999 Delalande tax reform: the layoff tax paid to the unemployment-insurance system rose for firms with more than 50 employees only. This reform provides a natural quasi-experimental design for difference-in-differences (D-i-D) estimation, in which workers in large firms constitute the treatment group and those in smaller firms the control group. We propose first to estimate the following standard D-i-D equation, which only distinguishes between larger and smaller firms:6 JSit=α+β1(BFit*Postt)+BFit+β2Xit+μi+λt+ϵit (1) Here JSit is the subjective job security of a worker i at year t, Xit a vector of individual socio-demographic controls (age and age-squared, marital status, number of children, and region dummies), and λt years fixed effects. This equation also controls for individual fixed effects μi. As the outcome is a subjective assessment of job security, the presence of individual fixed effects in the equation allows us to control for individual unobserved and time-invariant heterogeneity (referring to the interpretation of the scale or personality traits). The variable BFit is the treatment dummy, and is one if the worker is in a large firm and zero if the worker i is in a small firm at time t. The variable Postt is a dummy for observations after January 1999. As this equation includes year fixed effects, we do not include the variable Postt, as it is perfectly collinear with the year dummies. Finally, the coefficient of interest is that on the interaction BFit * Postt: β1. Firm size being self-reported, measurement errors may affect the estimation of β1. However, if we assume that the measurement error in the firm size has a mean zero and is uncorrelated with the true dependent and independent variables, measurement error is likely to produce an attenuation bias and it will not amplify the treatment effect (see the Classical Measurement Error model in Hyslop and Imbens [2001] for more details). The coefficient β1 shows how the rise in the Delalande tax affected the subjective job security of all workers in large firms by changing their probability of layoffs. We have a number of hypotheses regarding the expected sign of β1. If older workers in large firms benefited from fewer layoffs, this should translate into higher subjective job security for them. But the same tax rise may have generated negative externalities on other workers. As the cost of layoffs rose for older workers, unprotected younger workers in larger firms became relatively less costly to fire, with consequently lower subjective job security. As the expected effects on older and younger workers go in opposite directions, the sign of β1 is ambiguous.7 We then separate the impact of the reform between older and younger workers, and estimate the following equation: JSit=α+β3(BFit*Postt*BornBefore1949i)+β4(BFit*Postt*BornAfter1951i)+BFit+β5Xit+μi+λt+ϵit (2) Equation (2) is the counterpart of eq. (1), except that we now interact the treatment with the following dummy variables: ‘Born before 1949’ and ‘Born after 1951’. As such, β3 in eq. (2) isolates the effect of job protection on the perceived job security of older workers while β4 analogously picks up any effect on younger workers. By using OLS with individual fixed effects, we treat job security as cardinal. As job security is measured on an ordinal scale, ordered response models may be more appropriate. Ferrer-i-Carbonell and Frijters (2004) conclude that the assumption of the ordinality or cardinality in subjective well-being scores makes little difference in panel regressions. However, the present analysis differs from Ferrer-i-Carbonell and Frijters (2004) on crucial aspects such as the dependent variable, the dataset, and the identification strategy. We propose then to test the external validity of Ferrer-i-Carbonell and Frijters (2004) by also using a fixed-effects ordered logit model. There has been no clear consensus in the literature regarding efficient fixed-effects estimators in ordered logits. In a recent paper, Baetschmann et al. (2015) compare the performance of various estimators for the fixed-effects ordered logit model in a Monte Carlo study (among them the Chamberlain estimator [Chamberlain, 1980] and the FF estimator [Ferrer-i-Carbonell and Frijters, 2004]), and recommend the ‘Blow-up and Cluster’ (or BUC) estimator. This estimator recodes the dependent variable with k categories into k – 1 different dichotomizations using k – 1 thresholds. Each observation is then duplicated k – 1 times, one for each dichotomization, ‘blowing up’ the sample. Finally, a standard conditional logit estimation with clustered standard errors is applied to the sample (see Baetschmann et al. [2015] for more details). The interpretation of interaction terms in nonlinear models has now to be considered. In a widely cited paper, Ai and Norton (2003) show that the coefficient of an interaction term in the case of a nonlinear model is not informative per se. However, Puhani (2012) responds to Ai and Norton (2003) and demonstrates that ‘the sign of the treatment effect in a nonlinear “difference-in-differences” model with a strictly monotonic transformation function of a linear index (like probit, logit or tobit) is equal to the sign of the coefficient of the interaction term’ (p.87). This means that the sign of the interaction term is directly informative in our setting. Following again Puhani (2012), we used the bootstrap method for standard errors. However, calculating marginal effects in ordered logit with individual fixed effect can only be done by assuming that individual fixed effects are zero (Karaca-Mandic et al., 2012). This is conceptually paradoxical since the computation of marginal effects assumes homogeneity between individuals while the fundamental objective of the BUC estimator is to account for individual heterogeneity. Then, the results presented in this article based on the BUC estimator will be odd ratios. We again emphasize that those equations assess the effect of partial protection via the probability of layoff, and do not reflect the effect of the reform on job creation and the perceived job-finding probability: workers in small firms might be subsequently hired in large firms, and vice versa. 5. Results 5.1 Main results The results from the difference-in-differences estimate of the baseline regression eq. (1) appear in columns (1) and (5) of Table 2 respectively for the linear and nonlinear models. These suggest that the reform reduced subjective job security in the whole sample of workers, whatever the model used.8 Columns (2) and (6) split the treated workers (in firms with over 50 employees) into two groups: the older (‘Born before 1949’), who are protected by the Delalande tax, and the younger (‘Born after 1951’). Again, the results are the same when linear or nonlinear models are used and they show that older workers benefited from the reform, while the job security of younger workers fell. Considering only the OLS with individual fixed effects, the estimated coefficients for both groups are very similar at 0.11 of a standard deviation in job security. As unprotected workers constitute the large majority of the sample, the aggregate effect on the whole sample is negative (as shown in columns (1) and (5)).9 Our assumption here is that, conditional on controls, the change in job security over time between workers in large and small firms would have been the same without the rise in the Delalande tax. This parallel trend assumption can be tested by plotting the evolution of the job security regression residual on the controls: if the pattern is similar in the two groups prior to the reform, we can conclude that this assumption is reasonable. This is borne out in Figs A1 to A3: a clear difference in the movement over time only starts in the year the reform was announced (1998) in Figs A1 and A2. This gap is in favour of the control group, and suggests a negative (anticipated) effect of the reform for the whole sample, and for younger (unprotected) workers. Figure A3 instead shows a positive effect on job security for older (protected) workers that starts the year the reform is implemented (1999). Fig. 2 View largeDownload slide Layoff and perceived job security regression coefficients over time—younger workers. Note: Results in Panel A come from the French Labour Survey (152,795 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before December 1951 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. Fig. 2 View largeDownload slide Layoff and perceived job security regression coefficients over time—younger workers. Note: Results in Panel A come from the French Labour Survey (152,795 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before December 1951 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. Fig. 3 View largeDownload slide Layoff and perceived job security regression coefficients over timeolder workers. Note: Results in Panel A come from the French Labour Survey (55,159 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before September 1949 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. Fig. 3 View largeDownload slide Layoff and perceived job security regression coefficients over timeolder workers. Note: Results in Panel A come from the French Labour Survey (55,159 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before September 1949 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. We then account for anticipation due to the government announcement in Table 2 by adding an interaction term indicating if the individual was in the treatment group in 1998: ‘Treatment x 1998’. Columns (3), (4), (7), and (8) of Table 2 confirm that job security was lower in 1998 for the treatment group, especially for young unprotected workers. Overall, results from Table 2 confirm the conclusion of Ferrer-i-Carbonell and Frijters (2004): treating perceived job security as ordinal or cardinal does not make qualitative difference in panel regressions. 5.2 Channels According to Böckerman et al. (2011), perceived job security is a decreasing function of layoff rates. Following the theoretical model developed in Behaghel (2007), we expect the layoff rates of younger and older workers in large firms to react to the Delalande reform in opposite ways: the layoff probability of younger workers should rise, while that of older protected workers should fall. To check whether perceived job security mirrors the evolution in layoff rates, we calculate the layoff rates of younger and older workers in large and small firms using the French Labour Force Survey and estimate the following equation where Outcomesit stands for perceived job security and layoff rates: Outcomesit=α+BFit*λt+BFit+β2Xit+μi+λt+ϵit (3) In order to capture the dynamics of the effect on both perceived job security and layoff rates, eq. (3) above decomposes the treatment effect by year with 1995 as the reference period. Figures A4 and A5 show the layoff rates for these two groups of workers. As expected, Fig. A4 reveals similar movements in the layoffs of younger workers in large and small firms until 1997, followed by a clear increase in large firms in 1998, the year the reform was announced. The time profile of layoff rates is thereafter similar: the negative effect of higher protection on non-protected workers came into effect as soon as the reform was announced. Figure A5 reveals the same parallel movements before 1998 for older workers, followed by a spike in layoffs in large firms in 1998. Firms thus anticipated the higher firing costs starting in 1999. More surprisingly, the gap in layoffs between large and small firms returns to the pre-1998 level from 1999 onwards. We instead here would have expected a greater drop in layoffs in large firms in 1999. However, higher firing costs do not seem to have translated into lower layoff rates here. These results suggest greater layoff consequences for unprotected (younger) workers than for protected (older) workers. Fig. 4 View largeDownload slide Heterogeneity—age at the time of the reform. Note: Confidence intervals are at the 10% level. Standard errors are clustered at the individual level. Controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. Source: Own calculations. Fig. 4 View largeDownload slide Heterogeneity—age at the time of the reform. Note: Confidence intervals are at the 10% level. Standard errors are clustered at the individual level. Controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. Source: Own calculations. Figures 2 and 3 show the estimated coefficients from the dynamic difference-in-differences regression equation on the subsamples of younger and older workers, with the dependent variable being a dummy for being laid off in Panel A and perceived job security in Panel B. The results in Panel A confirm the previous conclusions in both figures, with positive and significant coefficients for younger workers from 1998 onwards, while only the 1998 coefficient is significantly positive for older workers. The insignificant coefficients for years before 1998 are in line with Figs A4 and A5 and confirm that the time profile of layoffs in small and large firms was similar prior to the rise in the Delalande tax. The significant coefficients on years after the reform can therefore reasonably be interpreted as having been caused by the reform. If perceived job security is a decreasing function of layoff rates, we should then expect coefficients displayed in Panel B of Figs 2 and 3 to mirror the coefficients in Panel A. This is confirmed for younger workers: as soon as their layoff rates significantly increase at the time of the reform’s announcement, their perceived job security starts to fall. But Fig. 3 displays a different pattern. We do not identify significant variations in layoff rates, except a spike in 1998 when the reform was announced. Then, even if there is no significant decreases in layoff rates of older workers, their perceived job security rises from 1999 onwards. These results imply that layoff rates may definitely affect perceived job security, but this is not the only channel. We have so far considered that perceived job security only depends on the absolute level of employment protection as measured by layoff rates. However, we know that subjective assessments of job quality depends on relative job characteristics. Clark and Oswald (1996) demonstrate for instance that job satisfaction is positively correlated with income but negatively correlated with the income in the reference group. Following the same reasoning, perceived job security may also depend on the relative level of employment protection. Even if their actual layoff rate was not affected by the reform of the Delalande tax, older workers in large firms may feel more protected because younger workers are now more likely to be laid off: older workers feel relatively more protected. 5.3 Heterogeneity For the sake of presentation, most of the reported results are now based on linear models with individual fixed effects. The occasional use of different models is motivated and explicitly specified in the remainder of this article. The D-i-D estimates in Table 2 show the average ‘treatment’ effect for workers in large firms. Tables 3–5 ask whether these effects differ across groups; column (1) in both tables reproduces the baseline results. As it is known that the determinants of subjective variables differ by gender (Fugl-Meyer et al., 2002), column (2) of Table 3 first interacts our treatment estimates with a female dummy, and finds no significant sex difference. Table 3 The rise in the Delalande tax—panel results by gender Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 3 The rise in the Delalande tax—panel results by gender Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 4 The rise in the Delalande tax—panel results by education Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. ‘Low education’: less than lower secondary education; ‘Intermediate education’: upper secondary education; “High education”: higher education. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 4 The rise in the Delalande tax—panel results by education Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. ‘Low education’: less than lower secondary education; ‘Intermediate education’: upper secondary education; “High education”: higher education. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 5 The rise in the Delalande tax—panel results by pre-reform wage Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 5 The rise in the Delalande tax—panel results by pre-reform wage Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. We then look at education in Table 4: older workers with lower education may be more concerned about employment protection if it is more difficult for them to find a new job. Education in the ECHP is measured by the highest diploma obtained using the International Standard Classification of Education–1976 (or ISCED): ‘High education’ for tertiary education, ‘Intermediate education’ for upper-secondary education, and ‘Low education’ for lower levels of education. Column (2) of Table 4 shows the results with education interactions. The fall in perceived job security for the younger is independent of education, but the average positive coefficient for older workers is mainly driven by those with intermediate and lower education. This result supports that workers with lower education benefit more from employment protection. As the Delalande tax was stated in months of gross wage, the higher the monthly wage, the more layoffs cost. For older workers, higher monthly wages translated into more protection. On the contrary, higher wages for younger workers may have provided incentives for employers to lay them off before they become protected by the Delalande tax. We hence interact the treatment dummy with a dummy indicating the individuals’ pre-reform wage quartile. Column (2) of Table 5 shows the results. First, the pattern of the results is in line with our predictions for higher-income older workers: the higher the pre-reform wage, the higher the treatment effect. The pattern for younger workers is different. While the negative effect seems to be concentrated on low-wage workers, none of the pre-reform wage interaction terms turns out to be significant. The treatment effect might also differ by age: the closer to 50 the worker is, the greater the probability to become more costly to fire in the near future. This might translate into a larger tax effect for workers who are closer to 50 than for younger workers. We thus interact the treatment estimate with the following age dummies (age being measured at the time of the reform): 18 to 30,10 30 to 35, 35 to 40, 40 to 45, 45 to 48, 50 to 55, and over 55. Figure 4 depicts the results. All the estimated coefficients up to age 45 are negative but are not very significant. It is between 45 and 48 years old that the rise in the Delalande tax has its largest negative effect on perceived job security. The impact is very similar for workers aged 50 to 55, and over 55 to the right of the figure.11 6. Robustness checks 6.1 Ruling out confounding reforms and shocks The estimated coefficients in Table 2 show how job security changed for the treated and control groups after 1998. To ensure that these only reflect the change in the Delalande tax, we need to be sure to have ruled out any effect from other confounding policies or macroeconomic events. One issue regarding our identification assumption lies in the French reform of the mandatory weekly working time. In 1998, the French Ministry of Labour announced a reduction in the standard workweek from 39 to 35 hours in companies with more than 20 employees. This may have affected workers’ perceived job security in those firms. To ensure that our main result of lower job security following the Delalande tax is not picking up this other reform, we rerun the baseline regression excluding workers in firms with under 20 employees. These results appear in column (1) of Table 6, and are consistent with the baseline results. The positive impact on the perceived job security of older workers is less significant due to the smaller sample size.12 Table 6 The rise in the Delalande tax—ruling out confounding shocks and reforms Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Source: Own calculations. Table 6 The rise in the Delalande tax—ruling out confounding shocks and reforms Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Source: Own calculations. The only major retirement reform implemented between 1994 and 2001 is the creation of the French Reserve Fund in 1999, whose main mission is to guarantee the equilibrium of the pension system. While the creation of this establishment may affect the perceived job security of older workers, there is no reason to believe that it would have affected workers in small and large firms differently. Still, two minor changes of the early retirement scheme, implemented in 2000 and 2001, may be of concern. In 2000, workers above age 57 may apply for early retirement if they occupy physically demanding jobs for a long time. This may affect our estimates if the propensity to be eligible to early retirement via this change in the legislation is correlated to firm size. To test for this, we rerun our regressions without workers above age 57. The results are presented in column (2) of Table 6 and remain unchanged. In 2001, the French government created the ‘pension-equivalent benefit’ (revenu équivalent retraite) scheme for unemployed people below age 60 who contributed more than 40 years. This corresponds to a minimum of EUR 762 per month (replacing, by the way, a previous similar provision). To ensure that our estimates are not influenced by this change, we rerun our regressions excluding observations from 2001. Results, presented in column (3) of Table 6, remain unchanged. While no simultaneous reform is likely to be a valid threat, we may still suspect that small and large firms are hardly comparable and that our estimates only reflect time-varying trends in perceived job security between these two types of firms. To ensure that the treatment and control are really comparable, we can limit the sample to firms relatively close to the 50-employee threshold, in a Regression Discontinuity Design spirit. To do so, we compare firms with 20 to 49 employees to firms with 50 to 100 employees.13 Applying this restriction reduces the sample size by more than 70%. Still, results in column (4) of Table 6 confirm our conclusions. The lower sample size induces higher standard errors, but the estimates remain significant. Finally, we would like to check that our results reflect the French reform, rather than some broader macro-economic trend. We do so by rerunning our baseline regressions on similar samples of workers in neighbouring countries, as the ECHP is harmonized across European countries. Data limitations restrict this comparison to Spain and Italy.14 The difference-in-differences estimates in these countries appear in columns (5) and (6) of Table 6 and are not significantly different from zero. Macroeconomic trends do not seem to be behind our results. 6.2 Using alternative control groups The previous identification strategy uses workers in small firms as the control group to assess the impact of the reform on workers in large firms. We also check our findings using public-sector workers as the controls. As they were not covered by the Delalande tax, we assume that their perceived job security was not affected by the tax scheme. Column (1) of Table 7 shows the results. The new estimates are very similar to the baseline estimates.15 Table 7 The rise in the Delalande tax—robustness checks Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Source: Own calculations. Note: The treatment is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The standard errors in parentheses are clustered at the individual level. The controls include individual FE (expect in columns (2) and (3)), age squared, and dummies for marital status, children in the household, region, and year. Columns (2) and (3) also control for age, gender, and tenure. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 7 The rise in the Delalande tax—robustness checks Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Source: Own calculations. Note: The treatment is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The standard errors in parentheses are clustered at the individual level. The controls include individual FE (expect in columns (2) and (3)), age squared, and dummies for marital status, children in the household, region, and year. Columns (2) and (3) also control for age, gender, and tenure. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. 6.3 Using different estimation methods In the baseline regressions, we demonstrated that considering treated job security as cardinal or ordinal does not affect our conclusions, which is consistent with Ferrer-i-Carbonell and Frijters (2004). However, individual fixed effects make a difference in Ferrer-i-Carbonell and Frijters (2004). We propose to check whether individual fixed effects make a difference in the present analysis by reestimating our main regressions using a pooled OLS and a pooled ordered logit. Columns (2) and (3) of Table 7 report the results. The results are again qualitatively similar, even if the coefficients do differ slightly from those in the baseline estimates. The FE and OLS estimates may differ for two main reasons. First, fixed-effects models introduce attenuation bias in the case of measurement error, so that OLS estimates are always higher than their FE counterparts in absolute terms. This is not the case here, as the pooled OLS coefficients are smaller than the FE estimates in absolute terms. Selection also plays a role: the OLS estimates are biased if the treatment is correlated with individual unobserved time-invariant characteristics. Comparing the results in columns (2) and (3) of Table 7 to the baseline estimates suggests that treated individuals were those with somewhat lower job security to start with. 6.4 Addressing attrition and self-selection Attrition is a threat to the estimation of our main coefficients. The main plausible scenario is that some workers may have left the sample not randomly but because of the reform. These workers being absent from the sample, they no longer contribute to the estimation of the reform impact. In our case, attrition is a threat if the leaving status is correlated to the changes in perceived job security that the workers would have experienced if they would have remained in the sample. While this assumption seems more plausible for older workers, we proposed in Table 8 to compute the attrition rate that would have been necessary in each age group to cancel out the reform impacts we previously estimated under different hypothetical scenarios. Knowing that the actual attrition rate in each age group is about 8%, any variation lower than one standard deviation of perceived job security is not strong enough to annihilate the main estimates. However, the actual attrition rates are high enough in the most extreme scenarios displayed in columns (5) and (10). To cancel out the reform impacts with 8% of attrition, the loss of older leavers should be at least equal to 1.52 s.d. and the gain of younger leavers should be at least of 1.73 s.d. While attrition is a fair concern in this setting, this calibration exercise shows that it is hardly a real threat to our main estimates. Table 8 Attrition rate and calibration Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Source: Own calculations. Note: This calibration exercise assumes that attrition does not affect the evolution of subjective job security in the control group. A total of 485 individuals constitute the group of non-leavers among older workers and experience an increase of 0.1108 s.d. in perceived job security among older workers. A total of 1,142 individuals constitute the group of non-leavers among younger workers and experience an increase of 0.1108 s.d. in perceived job security. The “Maximal Loss” is equal to the distance between the average perceived job security of leavers just before the reform and 1 (1 being the lowest satisfaction score with respect to job security). This “Maximal Loss” equals 3.13 s.d. and 3.02 s.d., respectively, in columns (5) and (10) for older and younger workers. Table 8 Attrition rate and calibration Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Source: Own calculations. Note: This calibration exercise assumes that attrition does not affect the evolution of subjective job security in the control group. A total of 485 individuals constitute the group of non-leavers among older workers and experience an increase of 0.1108 s.d. in perceived job security among older workers. A total of 1,142 individuals constitute the group of non-leavers among younger workers and experience an increase of 0.1108 s.d. in perceived job security. The “Maximal Loss” is equal to the distance between the average perceived job security of leavers just before the reform and 1 (1 being the lowest satisfaction score with respect to job security). This “Maximal Loss” equals 3.13 s.d. and 3.02 s.d., respectively, in columns (5) and (10) for older and younger workers. Self-selection is another plausible source of bias. Knowing that the reform was announced in 1998 and that we identified significant anticipation effects (especially among young workers), we may also suspect firms close to the 50 employees threshold to marginally adjust their size to select their treatment status. Individual workers may also self-select their treatment status by changing firms before 1999. To account for this potential issue, we exclude employees who switch from a large (small) to a small (large) firm, and those who stay in the same firm but report a change in its size between 1998 and 2001. Applying this restriction reduces the sample size by almost 5%, but results, displayed in column (4) of Table 7, remain strictly unchanged. 7. Conclusion This paper asked how partial employment protection might affect workers’ subjective job security by changing their perceived probability of layoff. We find that the increase in the French Delalande tax, a firing tax restricted to older workers, translates into greater subjective job security for older workers. However, this exogenous rise in older workers’ employment protection also reduced the relative firing cost of younger workers, leading to lower job security for this group. As uncovered workers constitute the large majority of the sample, the aggregate effect on the whole sample of workers is negative. As perceived job security falls with the probability of job loss, the lower perceived job security of younger workers is perfectly consistent with the increase in their layoff rate, compared to younger workers in smaller firms. But the increase in perceived job security of older workers in large firms is not mirrored in their layoff rate. This may reflect that perceived job security not only depends on absolute employment protection but also on its relative level. With the increase in the Delalande tax, older workers may have felt more protected as the layoff rate of their younger colleagues increased. We confirm the predictions of Behaghel (2007) regarding layoffs and the subjective job security of younger workers. However, we should also emphasize that we have not explored his predictions regarding job creation, which might affect both workers and the unemployed. In particular, our analysis did not allow us to see whether employment protection reduces the probability that the unemployed find work. The investigation of the relation between partial employment-protection reforms and job finding, and how this affects workers’ subjective job security, is a promising subject for future research. Since the results are estimated using unweighted linear and nonlinear models, we should stress that the average negative effect induced by the Delalande tax reform only supports a basic utilitarian welfare analysis. We could assume that job security may be more important for the well-being of older workers than younger workers, producing a greater weight on the job satisfaction of the former, and the potential for net welfare gains. Supplementary material Supplementary material is available online at the OUP website. This material consists of an online appendix and the replication (stata.do) files. The data used in this paper is confidential. Footnotes 1 See among others Kugler et al. (2002); Gómez-Salvador et al. (2004); Boeri and Jimeno (2005); Autor et al. (2007); Von Below and Thoursie (2010). 2 See Blanchard and Landier (2002); Dolado et al. (2002); Kugler et al. (2002); Gómez-Salvador et al. (2004); Boeri and Jimeno (2005); Autor et al. (2007); Kugler and Pica (2008). 3 The main differences from previous models are segmentation of the labour market into age sub-markets, each of which has its own matching function, and the inclusion of firing costs for older workers. See Behaghel (2007) for more technical details. 4 There is of course also an effect on hiring, as with any transaction tax on the labour market. By the construction of the Law, this hiring effect applies to all age groups equally. 5 More details are available at http://ec.europa.eu/eurostat/web/microdata/european-community-household-panel (last accessed 18 December 2017). 6 We do not use weights in our regressions, but the ECHP provides different survey weights. We followed the documentation and used the survey weights designed for longitudinal analysis at the country level. Whatever the model used or the equation estimated, results are not affected by the use of the ECHP weights. 7 A large branch of the literature has already suggested that utility is relative. If subjective job security is also relative, we might also expect comparison effects here. 8 The difference in sample size is due to the use of the BUC estimator that increases artificially the number of individual observations. 9 A total of 76% of treated workers are younger unprotected workers. 10 This age interval is larger than the other intervals, as the age distribution in our sample is left-skewed. 11 The estimates and standard errors appear in Table A3 in the Appendix. 12 One may also fear that firms with more than 50 workers were early adopters of the reduced workweek. We tested whether working time was reduced earlier in firms with more than 50 workers than firms with 20 to 49 workers. But working time only started to decrease significantly in 2001, and there is no significant difference across firm size. Results are available upon request. 13 A strict Regression Discontinuity Design would require estimating the treatment effect in a narrower window, but firm size in ECHP is only reported using bands. 14 Perceived job security is not measured after 1997 in Germany, and the information in the last waves of the ECHP in Belgium is insufficient to accurately differentiate the public and private sectors. 15 We also used both workers from small firms and in the public sector as a control group. This led to very similar results, which are available on request. Acknowledgments We are particularly indebted to Andrew Clark and Claudia Senik. We are also grateful to Philippe Askenazy, Fabrice Etilé, Paul Frijters, Marc Gurgand, David Margolis, Barbara Petrongolo, and Gilles Saint-Paul. We would like to thank the two anonymous referees for their constructive and detailed advice, which has substantially improved the paper. Funding This work was funded by the Labex OSE and the Université Paris 1 - Panthéon Sorbonne. References Abowd J.M. , Kramarz F. ( 2003 ) The costs of hiring and separations , Labour Economics , 10 , 499 – 530 . Google Scholar CrossRef Search ADS Ai C. , Norton E.C. ( 2003 ) Interaction terms in logit and probit models , Economics Letters , 80 , 123 – 29 . Google Scholar CrossRef Search ADS Akerlof G.A. , Rose A.K. , Yellen J.L. , Ball L. , Robert E.H. ( 1988 ) Job switching and job satisfaction in the US labor market , Brookings Papers on Economic Activity , 1988 , 495 – 594 . Google Scholar CrossRef Search ADS Autor D.H. , Kerr W.R. , Kugler A.D. ( 2007 ) Does employment protection reduce productivity? Evidence from US states , Economic Journal , 117 , F189 – 217 . Google Scholar CrossRef Search ADS Baetschmann G. , Staub K.E. , Winkelmann R. 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Google Scholar CrossRef Search ADS © Oxford University Press 2018 All rights reserved This article is published and distributed under the terms of the Oxford University Press, Standard Journals Publication Model (https://academic.oup.com/journals/pages/about_us/legal/notices) http://www.deepdyve.com/assets/images/DeepDyve-Logo-lg.png Oxford Economic Papers Oxford University Press

Partial employment protection and perceived job security: evidence from France

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Abstract

Abstract This paper assesses the causal effect of partial employment protection on workers’ subjective job security via the perceived probability of layoff. We consider the rise in the French Delalande tax, which is paid by private firms if they lay off older workers. This reform was restricted to large firms and therefore allows us to use a difference-in-differences strategy. In ECHP data, we find that the change in the perceived probability of layoffs induced by the higher Delalande tax improved the subjective job security of older (protected) workers, but at the cost of a negative externality on other workers. The changes in job security in both groups are of similar size, but as unprotected workers are the large majority of the sample, the population effect of the tax on layoffs was to reduce job security. 1. Introduction There is by now a great deal of empirical evidence that employment protection reduces worker flows.1 We here ask whether this affects workers’ perceived job security, both positively for those who are covered and negatively for those who are not. These are important questions, as we know that workers’ subjective evaluations of their job predict their labour-market behaviour (Freeman, 1978; Akerlof et al., 1988; Clark et al., 1998; Clark, 2001) and may affect firm outcomes such as productivity and profit (Harter et al., 2002). The existing empirical literature on the relationship between employment protection and the subjective perception of job security has mostly relied on cross-country analysis, and generally finds a negative correlation (Böckerman, 2004; Postel-Vinay and Saint-Martin, 2004; Clark and Postel-Vinay, 2009). This surprising result can be explained by the perverse effects of employment protection, in particular via less job creation. Subjective job security is related to both separations and hirings (Böckerman et al., 2011), via the transition probabilities between employment and unemployment. This paper complements existing work by using a natural experiment to assess the causal impact of partial employment protection on workers’ self-assessed job security, partial meaning here that all workers are not eligible for employment protection. We focus on changes in the perceived probability of layoff from a French employment-protection reform implemented in 1999: an increase in the Delalande tax, which is paid by private-sector firms if they lay off workers aged over 50 in permanent contracts. This 1999 rise was restricted to firms with more than 50 employees, and as such provides a natural quasi-experiment that can be analysed via difference-in-differences estimation. We consider private-sector workers with permanent contracts in European Community Household Panel (ECHP) survey data. These data cover the period 1994–2001. We should emphasize that this estimation does not allow us to examine the effect of the reform through job creation and perceived job-finding probabilities, as workers in large firms might be hired in small firms later on, and vice versa. We here assess the effect of partial protection through layoff probabilities only. Our main finding is that the change in the cost of layoffs from the higher Delalande tax led to greater feelings of job security for protected workers, but at the cost of less job security for other workers. The job security movements are of similar size for both groups, at 10% of a standard deviation. As there are far more unprotected than protected workers, the rise in the Delalande tax reduced aggregate job security. The largest fall in job security is for unprotected workers who are closer to 50, as this is the group that firms have the greatest incentive to lay off (before they become covered by the Delalande tax). There are different issues that our empirical analysis needs to address. We first need to rule out potential confounding French reforms. In 1998, the French Ministry of Labour announced that there would be a reduction of standard weekly hours from 39 to 35 hours in firms with over 20 employees; this reform was enacted in 2000. These expected changes may therefore have affected perceived job security in firms with over 20 employees in our ECHP data from 1998 onwards. We show, however, that the difference in subjective job security between firms with less than and more than 50 employees (which is the threshold for the Delalande tax) is also found when we drop workers from firms with under 20 employees (i.e. when we restrict the sample to include only firms that were subject to the 35-hour week). Potential minor changes in the French early retirement system are also considered. We prove in the robustness checks that these changes are not driving our estimates. Second, macro-economic trends may produce different changes in job security in large and small firms. We address this issue by taking advantage of the cross-country dimension of ECHP data. We replicate the identification strategy in bordering countries and show that the difference-in-differences estimates there are insignificant. Our results highlight that the perverse effects of partial employment protection on the perceived job security of unprotected workers may more than offset its beneficial effects on protected workers. In addition, as we do not consider the negative effects of protection on job creation, our estimates of these perverse effects constitute a lower bound. In addition, we also contribute to the literature by assessing the external validity of Ferrer-i-Carbonell and Frijters (2004). They conclude that assuming ordinality or cardinality in subjective well-being scores makes little differences in panel regressions. Our analysis differs on several aspects (dependent variable, dataset, and identification strategy), and we check and confirm the conclusion of Ferrer-i-Carbonell and Frijters (2004): we show that, once controlling for individual fixed effects, using linear or nonlinear models does not affect the sign and the significance of the treatment effects. The remainder of the paper is organized as follows. Section 2 presents the institutional background and the theoretical implications, while Section 3 describes the ECHP data that we use. Section 4 explains the empirical strategy, the results and the heterogeneity analysis appear in Section 5, and robustness checks are displayed in Section 6. Finally, Section 7 concludes. 2. Institutional background, theoretical implications, and expected impacts 2.1 Institutional background The Delalande tax was proposed and introduced in the French legislative system in 1987 to restore the financial balance of the unemployment-insurance system and reduce the rise in the layoffs of older workers. Despite numerous changes over time, the principle of the tax has remained unchanged: firms laying off workers of over a certain age have to pay the Delalande tax to the unemployment-insurance system. This tax is proportional to the worker’s gross wage and covers private-sector workers with permanent contracts. From 1987 to 1992, the tax amount was three months of gross wages for all workers aged over 55. The first major changes to this tax were introduced in July 1992. Table 1 shows how the tax profile has changed. In particular, in 1992 the tax started to depend on firm size, the age threshold of workers covered was lowered to 50, and the maximum tax amount increased to 6 months of gross wages. However, workers who were hired after age 50 and had been unemployed for at least 3 months were exempt from the tax. Additional changes to the tax scheme were made in January 1993 and January 1999. From 1993 to December 1998, the tax did not depend on firm size but only on the worker’s age. In January 1999, the tax was increased for firms with over 50 employees only. The tax was equal to 2 months of gross wages for 50-year-old workers and reached 12 months of gross wages for workers between age 56 and 57. This tax represents an important share of the total separation costs: Behaghel et al. (2004) estimate for instance the average French separation costs to be equal to almost 4 months of gross wages, while Abowd and Kramarz (2003) estimate these costs to be equal to 5 to 7 months of gross wages. Table 1 The Delalande tax scheme Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Source: Legislative texts. Note: For each age group, the table displays the tax due by the firm to the unemployment insurance system if it lays the worker off. The tax is a function of previous wages, and is stated in months of gross wage. Table 1 The Delalande tax scheme Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Worker’s age 50 51 52 53 54 55 56–57 58 59 July 1987–June 1992 All firm sizes 3 3 3 3 July 1992–Dec. 1992 More than 20 employees 1 1 2 2 4 5 6 6 6 Less than 20 employees 0.5 0.5 1 1 2 2.5 3 3 3 Jan. 1993–Dec. 1998 All firm sizes 1 1 2 2 4 5 6 6 6 After Jan. 1999 More than 50 employees 2 3 5 6 8 10 12 10 8 Less than 50 employees 1 1 2 2 4 5 6 6 6 Source: Legislative texts. Note: For each age group, the table displays the tax due by the firm to the unemployment insurance system if it lays the worker off. The tax is a function of previous wages, and is stated in months of gross wage. The 1999 rise in the Delalande tax was announced by the French government one year beforehand. According to the article entitled ‘Pénalisation des licenciements des plus de 50 ans: le projet de Martine Aubry’ published in the French newspaper Les Echos in 1998, the increase in the Delalande tax was not expected, especially by unions, even though they were satisfied by this reform. The reintroduction of firm size discontinuity was publicly known for months by the end of 1998. This means that the timing of the reform is the following: the reform of the Delalande tax is announced in 1998, and this may translate into anticipation effects, while the actual impacts of the reform will be identified from 1999 onwards. 2.2 Theoretical implications of partial employment protection and expected effects on perceived job security Theoretical analysis (see among others Mortensen and Pissarides, 1999; Cahuc and Postel-Vinay, 2002) predicts that employment protection reduces job and worker flows. The intuition behind this is summarized in Cahuc and Postel-Vinay (2002): ‘Higher firing costs limit job destruction by making layoffs more expensive, while they also inhibit job creation by reducing the overall expected profitability of jobs’ (p.79). This prediction has been confirmed in a variety of empirical contributions.2 Following Mortensen and Pissarides (1994) and Pissarides (2000), Behaghel (2007) proposes a stochastic job-matching model that accounts for the Delalande tax.3 This tax reduces both the separation rate and the probability of a return to work for older workers, while it increases the separation rate and reduces the probability to return to work for younger workers. Behaghel et al. (2008) test these theoretical predictions on hirings and layoffs using French data from the Labour Force Survey. We here extend these predictions to workers’ perceived job security, and focus only on the separation channel: we specifically ask how the 1999 rise in the Delalande tax affected worker’s subjective job security by changing their perceived probability of layoff. We expect two effects in large firms as the tax rises. First, lower separation rates should increase the perceived job security of workers aged over 50. On the contrary, higher separation rates should reduce the job security of younger workers.4 On top of the 1999 rise in the Delalande tax, we may expect anticipation effects on perceived job security. With the reform being announced months before its implementation, we may expect employers to strategically adjust their labour demand. They may have the incentive to lay off workers around the 50-year-old threshold before the rise in the Delalande tax. 3. Data Our data come from the European Household Community Panel (ECHP). The ECHP is a longitudinal survey carried out in 14 European countries, including France. A nationally representative sample of household and individuals was interviewed each year between 1994 and 2001 in each country. In France, 15,000 individuals were surveyed per wave on average. The interviews mainly took place between October and December. The ECHP contains detailed information on socio-economic characteristics, incomes, employment conditions, social relations, and so on.5 The rise in the Delalande tax in 1999 only applied to workers aged over 50 in firms with over 50 employees. We identify the covered respondents in the ECHP by their reported age in the survey (we correct misreporting by comparing birth and interview dates). The size of the firm in which the respondent works, measured by the number of employees in the firm, is recorded in the following categories: ‘None’, ‘1 to 4’, ‘5 to 19’, ‘20 to 49’, ‘50 to 99’, ‘100 to 499’, and ‘500 or more’. The ECHP also contains a number of questions on job domain satisfaction. Subjective job security is our main dependent variable, and is measured by the following question: ‘How satisfied are you with your present job in terms of job security?’ Respondents answered on a 6-point scale, 1 meaning ‘Not Satisfied’ and 6 meaning ‘Fully Satisfied’. Fig. 1 shows the distribution of subjective job security. It can be seen that 70% of responses are 4 or 5. This negative skewness is commonly found for satisfaction measures. Fig. 1 View largeDownload slide The distribution of satisfaction with job security. Source: Own calculations. Fig. 1 View largeDownload slide The distribution of satisfaction with job security. Source: Own calculations. Our main sample consists of adult respondents working in the private sector with permanent contracts, and with valid information on job characteristics and perceived job security. We restrict the sample to workers who do not cross the age-50 threshold during the post-treatment sample period (i.e. who were born before September 1949 or after December 1951), and who were hired when under 50. We thus split the sample into two age groups with clear ‘treatment’ nature: workers who are either protected (older workers) or not protected (younger workers) during the whole post-reform sample period. This leaves us with 14,110 observations based on 3,003 individuals. The complete descriptive statistics appear in Tables A1 and A2 in the Supplementary Appendix. Table 2 The rise in the Delalande tax and perceived job security Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 2 The rise in the Delalande tax and perceived job security Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Perceived job security OLS with individual FE BUC ordered logit model Baseline results Accounting for anticipation in 1998 Baseline results Accounting for anticipation in 1998 (1) (2) (3) (4) (5) (6) (7) (8) BF*Post –0.07** –0.10*** –0.22** –0.31*** (0.03) (0.03) (0.09) (0.10) BF*Post*Born before 1949 0.11** 0.11** 0.43** 0.43** (0.05) (0.06) (0.20) (0.18) BF*Post*Born after 1951 –0.11*** –0.15*** –0.37*** –0.48*** (0.03) (0.03) (0.08) (0.10) BF*1998 –0.09** –0.29*** (0.03) (0.11) BF*1998*Born before 1949 –0.01 –0.03 (0.06) (0.18) BF*1998*Born after 1951 –0.11*** –0.36*** (0.04) (0.13) Observations 14,110 14,110 14,110 14,110 24,681 24,681 24,681 24,681 Individuals 3,003 3,003 3,003 3,003 3,003 3,003 3,003 3,003 Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. 4. Identification strategy and empirical specification Our main goal here is to assess the causal effect of partial employment protection on workers’ subjective job security via changes in the perceived probability of layoff. In principle, workers below age 50 in firms with more than 50 workers might be considered to be the ideal control group. They would allow to compare workers above and below age 50 in firms of similar size before and after the reform. The age threshold is appealing; because it is exogenous, it cannot be manipulated. But the stochastic job-matching model used by Behaghel (2007) predicts that the Delalande tax is also likely to affect workers below age 50 in firms with more than 50 workers via higher separation rates. We therefore exploit the firm-size discontinuity of the 1999 Delalande tax reform: the layoff tax paid to the unemployment-insurance system rose for firms with more than 50 employees only. This reform provides a natural quasi-experimental design for difference-in-differences (D-i-D) estimation, in which workers in large firms constitute the treatment group and those in smaller firms the control group. We propose first to estimate the following standard D-i-D equation, which only distinguishes between larger and smaller firms:6 JSit=α+β1(BFit*Postt)+BFit+β2Xit+μi+λt+ϵit (1) Here JSit is the subjective job security of a worker i at year t, Xit a vector of individual socio-demographic controls (age and age-squared, marital status, number of children, and region dummies), and λt years fixed effects. This equation also controls for individual fixed effects μi. As the outcome is a subjective assessment of job security, the presence of individual fixed effects in the equation allows us to control for individual unobserved and time-invariant heterogeneity (referring to the interpretation of the scale or personality traits). The variable BFit is the treatment dummy, and is one if the worker is in a large firm and zero if the worker i is in a small firm at time t. The variable Postt is a dummy for observations after January 1999. As this equation includes year fixed effects, we do not include the variable Postt, as it is perfectly collinear with the year dummies. Finally, the coefficient of interest is that on the interaction BFit * Postt: β1. Firm size being self-reported, measurement errors may affect the estimation of β1. However, if we assume that the measurement error in the firm size has a mean zero and is uncorrelated with the true dependent and independent variables, measurement error is likely to produce an attenuation bias and it will not amplify the treatment effect (see the Classical Measurement Error model in Hyslop and Imbens [2001] for more details). The coefficient β1 shows how the rise in the Delalande tax affected the subjective job security of all workers in large firms by changing their probability of layoffs. We have a number of hypotheses regarding the expected sign of β1. If older workers in large firms benefited from fewer layoffs, this should translate into higher subjective job security for them. But the same tax rise may have generated negative externalities on other workers. As the cost of layoffs rose for older workers, unprotected younger workers in larger firms became relatively less costly to fire, with consequently lower subjective job security. As the expected effects on older and younger workers go in opposite directions, the sign of β1 is ambiguous.7 We then separate the impact of the reform between older and younger workers, and estimate the following equation: JSit=α+β3(BFit*Postt*BornBefore1949i)+β4(BFit*Postt*BornAfter1951i)+BFit+β5Xit+μi+λt+ϵit (2) Equation (2) is the counterpart of eq. (1), except that we now interact the treatment with the following dummy variables: ‘Born before 1949’ and ‘Born after 1951’. As such, β3 in eq. (2) isolates the effect of job protection on the perceived job security of older workers while β4 analogously picks up any effect on younger workers. By using OLS with individual fixed effects, we treat job security as cardinal. As job security is measured on an ordinal scale, ordered response models may be more appropriate. Ferrer-i-Carbonell and Frijters (2004) conclude that the assumption of the ordinality or cardinality in subjective well-being scores makes little difference in panel regressions. However, the present analysis differs from Ferrer-i-Carbonell and Frijters (2004) on crucial aspects such as the dependent variable, the dataset, and the identification strategy. We propose then to test the external validity of Ferrer-i-Carbonell and Frijters (2004) by also using a fixed-effects ordered logit model. There has been no clear consensus in the literature regarding efficient fixed-effects estimators in ordered logits. In a recent paper, Baetschmann et al. (2015) compare the performance of various estimators for the fixed-effects ordered logit model in a Monte Carlo study (among them the Chamberlain estimator [Chamberlain, 1980] and the FF estimator [Ferrer-i-Carbonell and Frijters, 2004]), and recommend the ‘Blow-up and Cluster’ (or BUC) estimator. This estimator recodes the dependent variable with k categories into k – 1 different dichotomizations using k – 1 thresholds. Each observation is then duplicated k – 1 times, one for each dichotomization, ‘blowing up’ the sample. Finally, a standard conditional logit estimation with clustered standard errors is applied to the sample (see Baetschmann et al. [2015] for more details). The interpretation of interaction terms in nonlinear models has now to be considered. In a widely cited paper, Ai and Norton (2003) show that the coefficient of an interaction term in the case of a nonlinear model is not informative per se. However, Puhani (2012) responds to Ai and Norton (2003) and demonstrates that ‘the sign of the treatment effect in a nonlinear “difference-in-differences” model with a strictly monotonic transformation function of a linear index (like probit, logit or tobit) is equal to the sign of the coefficient of the interaction term’ (p.87). This means that the sign of the interaction term is directly informative in our setting. Following again Puhani (2012), we used the bootstrap method for standard errors. However, calculating marginal effects in ordered logit with individual fixed effect can only be done by assuming that individual fixed effects are zero (Karaca-Mandic et al., 2012). This is conceptually paradoxical since the computation of marginal effects assumes homogeneity between individuals while the fundamental objective of the BUC estimator is to account for individual heterogeneity. Then, the results presented in this article based on the BUC estimator will be odd ratios. We again emphasize that those equations assess the effect of partial protection via the probability of layoff, and do not reflect the effect of the reform on job creation and the perceived job-finding probability: workers in small firms might be subsequently hired in large firms, and vice versa. 5. Results 5.1 Main results The results from the difference-in-differences estimate of the baseline regression eq. (1) appear in columns (1) and (5) of Table 2 respectively for the linear and nonlinear models. These suggest that the reform reduced subjective job security in the whole sample of workers, whatever the model used.8 Columns (2) and (6) split the treated workers (in firms with over 50 employees) into two groups: the older (‘Born before 1949’), who are protected by the Delalande tax, and the younger (‘Born after 1951’). Again, the results are the same when linear or nonlinear models are used and they show that older workers benefited from the reform, while the job security of younger workers fell. Considering only the OLS with individual fixed effects, the estimated coefficients for both groups are very similar at 0.11 of a standard deviation in job security. As unprotected workers constitute the large majority of the sample, the aggregate effect on the whole sample is negative (as shown in columns (1) and (5)).9 Our assumption here is that, conditional on controls, the change in job security over time between workers in large and small firms would have been the same without the rise in the Delalande tax. This parallel trend assumption can be tested by plotting the evolution of the job security regression residual on the controls: if the pattern is similar in the two groups prior to the reform, we can conclude that this assumption is reasonable. This is borne out in Figs A1 to A3: a clear difference in the movement over time only starts in the year the reform was announced (1998) in Figs A1 and A2. This gap is in favour of the control group, and suggests a negative (anticipated) effect of the reform for the whole sample, and for younger (unprotected) workers. Figure A3 instead shows a positive effect on job security for older (protected) workers that starts the year the reform is implemented (1999). Fig. 2 View largeDownload slide Layoff and perceived job security regression coefficients over time—younger workers. Note: Results in Panel A come from the French Labour Survey (152,795 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before December 1951 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. Fig. 2 View largeDownload slide Layoff and perceived job security regression coefficients over time—younger workers. Note: Results in Panel A come from the French Labour Survey (152,795 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before December 1951 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. Fig. 3 View largeDownload slide Layoff and perceived job security regression coefficients over timeolder workers. Note: Results in Panel A come from the French Labour Survey (55,159 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before September 1949 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. Fig. 3 View largeDownload slide Layoff and perceived job security regression coefficients over timeolder workers. Note: Results in Panel A come from the French Labour Survey (55,159 observations). The controls in Panel A are gender, education level, age, age squared, and dummies for children under 3, 6, 18, region, and year. Results in Panel B come from the ECHP. The controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. The sample is restricted to workers born before September 1949 in both panels. The confidence intervals are at the 10% level. The standard errors are clustered at the individual level. Source: Own calculations. We then account for anticipation due to the government announcement in Table 2 by adding an interaction term indicating if the individual was in the treatment group in 1998: ‘Treatment x 1998’. Columns (3), (4), (7), and (8) of Table 2 confirm that job security was lower in 1998 for the treatment group, especially for young unprotected workers. Overall, results from Table 2 confirm the conclusion of Ferrer-i-Carbonell and Frijters (2004): treating perceived job security as ordinal or cardinal does not make qualitative difference in panel regressions. 5.2 Channels According to Böckerman et al. (2011), perceived job security is a decreasing function of layoff rates. Following the theoretical model developed in Behaghel (2007), we expect the layoff rates of younger and older workers in large firms to react to the Delalande reform in opposite ways: the layoff probability of younger workers should rise, while that of older protected workers should fall. To check whether perceived job security mirrors the evolution in layoff rates, we calculate the layoff rates of younger and older workers in large and small firms using the French Labour Force Survey and estimate the following equation where Outcomesit stands for perceived job security and layoff rates: Outcomesit=α+BFit*λt+BFit+β2Xit+μi+λt+ϵit (3) In order to capture the dynamics of the effect on both perceived job security and layoff rates, eq. (3) above decomposes the treatment effect by year with 1995 as the reference period. Figures A4 and A5 show the layoff rates for these two groups of workers. As expected, Fig. A4 reveals similar movements in the layoffs of younger workers in large and small firms until 1997, followed by a clear increase in large firms in 1998, the year the reform was announced. The time profile of layoff rates is thereafter similar: the negative effect of higher protection on non-protected workers came into effect as soon as the reform was announced. Figure A5 reveals the same parallel movements before 1998 for older workers, followed by a spike in layoffs in large firms in 1998. Firms thus anticipated the higher firing costs starting in 1999. More surprisingly, the gap in layoffs between large and small firms returns to the pre-1998 level from 1999 onwards. We instead here would have expected a greater drop in layoffs in large firms in 1999. However, higher firing costs do not seem to have translated into lower layoff rates here. These results suggest greater layoff consequences for unprotected (younger) workers than for protected (older) workers. Fig. 4 View largeDownload slide Heterogeneity—age at the time of the reform. Note: Confidence intervals are at the 10% level. Standard errors are clustered at the individual level. Controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. Source: Own calculations. Fig. 4 View largeDownload slide Heterogeneity—age at the time of the reform. Note: Confidence intervals are at the 10% level. Standard errors are clustered at the individual level. Controls include an individual FE, age squared, and dummies for marital status, children in the household, region, and year. Source: Own calculations. Figures 2 and 3 show the estimated coefficients from the dynamic difference-in-differences regression equation on the subsamples of younger and older workers, with the dependent variable being a dummy for being laid off in Panel A and perceived job security in Panel B. The results in Panel A confirm the previous conclusions in both figures, with positive and significant coefficients for younger workers from 1998 onwards, while only the 1998 coefficient is significantly positive for older workers. The insignificant coefficients for years before 1998 are in line with Figs A4 and A5 and confirm that the time profile of layoffs in small and large firms was similar prior to the rise in the Delalande tax. The significant coefficients on years after the reform can therefore reasonably be interpreted as having been caused by the reform. If perceived job security is a decreasing function of layoff rates, we should then expect coefficients displayed in Panel B of Figs 2 and 3 to mirror the coefficients in Panel A. This is confirmed for younger workers: as soon as their layoff rates significantly increase at the time of the reform’s announcement, their perceived job security starts to fall. But Fig. 3 displays a different pattern. We do not identify significant variations in layoff rates, except a spike in 1998 when the reform was announced. Then, even if there is no significant decreases in layoff rates of older workers, their perceived job security rises from 1999 onwards. These results imply that layoff rates may definitely affect perceived job security, but this is not the only channel. We have so far considered that perceived job security only depends on the absolute level of employment protection as measured by layoff rates. However, we know that subjective assessments of job quality depends on relative job characteristics. Clark and Oswald (1996) demonstrate for instance that job satisfaction is positively correlated with income but negatively correlated with the income in the reference group. Following the same reasoning, perceived job security may also depend on the relative level of employment protection. Even if their actual layoff rate was not affected by the reform of the Delalande tax, older workers in large firms may feel more protected because younger workers are now more likely to be laid off: older workers feel relatively more protected. 5.3 Heterogeneity For the sake of presentation, most of the reported results are now based on linear models with individual fixed effects. The occasional use of different models is motivated and explicitly specified in the remainder of this article. The D-i-D estimates in Table 2 show the average ‘treatment’ effect for workers in large firms. Tables 3–5 ask whether these effects differ across groups; column (1) in both tables reproduces the baseline results. As it is known that the determinants of subjective variables differ by gender (Fugl-Meyer et al., 2002), column (2) of Table 3 first interacts our treatment estimates with a female dummy, and finds no significant sex difference. Table 3 The rise in the Delalande tax—panel results by gender Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 3 The rise in the Delalande tax—panel results by gender Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Perceived job security (1) (2) BF*Post*Born after 1951 –0.11*** –0.09*** (0.03) (0.03) BF*Post*Born after 1951*Women –0.06 (0.05) BF*Post*Born before 1949 0.11** 0.12** (0.05) (0.05) BF*Post*Born before 1949*Women –0.04 (0.10) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Younger men –0.09*** (0.03)  Younger women –0.15*** (0.05)  Older men 0.12** (0.05)  Older women 0.08 (0.09) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 4 The rise in the Delalande tax—panel results by education Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. ‘Low education’: less than lower secondary education; ‘Intermediate education’: upper secondary education; “High education”: higher education. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 4 The rise in the Delalande tax—panel results by education Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** 0.14*** (0.05) (0.05) BF*Post*Born before 1949*High education –0.16 (0.11) BF*Post*Born before 1949*Interm. education 0.03 (0.15) BF*Post*Born after 1951 –0.11*** –0.11*** (0.03) (0.04) BF*Post*Born after 1951*High education –0.01 (0.05) BF*Post*Born after 1951*Interm. education –0.02 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for young:  Workers with low level of education –0.11*** (0.04)  Workers with intermediate level of education –0.12*** (0.05)  Workers with high level of education –0.12* (0.07) Total implied effect for older:  Workers with low level of education 0.14*** (0.05)  Workers with intermediate level of education 0.18 (0.15)  Workers with high level of education –0.02 (0.10) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. ‘Low education’: less than lower secondary education; ‘Intermediate education’: upper secondary education; “High education”: higher education. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 5 The rise in the Delalande tax—panel results by pre-reform wage Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 5 The rise in the Delalande tax—panel results by pre-reform wage Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Perceived job security (1) (2) BF*Post*Born before 1949 0.11** –0.18 (0.05) (0.14) BF*Post*Born before 1949*Pre-reform wage in second quartile 0.23 (0.16) BF*Post*Born before 1949*Pre-reform wage in third quartile 0.37** (0.15) BF*Post*Born before 1949*Pre-reform wage in fourth quartile 0.28** (0.14) BF*Post*Born after 1951 –0.11*** –0.13* (0.03) (0.07) BF*Post*Born after 1951*Pre-reform wage in second quartile –0.08 (0.07) BF*Post*Born after 1951*Pre-reform wage in third income 0.01 (0.07) BF*Post*Born after 1951*Pre-reform wage in fourth quartile –0.01 (0.07) Observations 14,110 14,110 Individuals 3,003 3,003 Total implied effect for:  Older workers with pre-reform wage in first quartile –0.18 (0.14)  Older workers with pre-reform wage in second quartile 0.05 (0.10)  Older workers with pre-reform wage in third quartile 0.20*** (0.07)  Older workers with pre-reform wage in fourth quartile 0.11* (0.06)  Younger workers with pre-reform wage in first quartile –0.13* (0.07)  Younger workers with pre-reform wage in second quartile –0.21*** (0.05)  Younger workers with pre-reform wage in third quartile –0.12*** (0.04)  Younger workers with pre-reform wage in fourth quartile –0.14*** (0.04) Source: Own calculations. Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. We then look at education in Table 4: older workers with lower education may be more concerned about employment protection if it is more difficult for them to find a new job. Education in the ECHP is measured by the highest diploma obtained using the International Standard Classification of Education–1976 (or ISCED): ‘High education’ for tertiary education, ‘Intermediate education’ for upper-secondary education, and ‘Low education’ for lower levels of education. Column (2) of Table 4 shows the results with education interactions. The fall in perceived job security for the younger is independent of education, but the average positive coefficient for older workers is mainly driven by those with intermediate and lower education. This result supports that workers with lower education benefit more from employment protection. As the Delalande tax was stated in months of gross wage, the higher the monthly wage, the more layoffs cost. For older workers, higher monthly wages translated into more protection. On the contrary, higher wages for younger workers may have provided incentives for employers to lay them off before they become protected by the Delalande tax. We hence interact the treatment dummy with a dummy indicating the individuals’ pre-reform wage quartile. Column (2) of Table 5 shows the results. First, the pattern of the results is in line with our predictions for higher-income older workers: the higher the pre-reform wage, the higher the treatment effect. The pattern for younger workers is different. While the negative effect seems to be concentrated on low-wage workers, none of the pre-reform wage interaction terms turns out to be significant. The treatment effect might also differ by age: the closer to 50 the worker is, the greater the probability to become more costly to fire in the near future. This might translate into a larger tax effect for workers who are closer to 50 than for younger workers. We thus interact the treatment estimate with the following age dummies (age being measured at the time of the reform): 18 to 30,10 30 to 35, 35 to 40, 40 to 45, 45 to 48, 50 to 55, and over 55. Figure 4 depicts the results. All the estimated coefficients up to age 45 are negative but are not very significant. It is between 45 and 48 years old that the rise in the Delalande tax has its largest negative effect on perceived job security. The impact is very similar for workers aged 50 to 55, and over 55 to the right of the figure.11 6. Robustness checks 6.1 Ruling out confounding reforms and shocks The estimated coefficients in Table 2 show how job security changed for the treated and control groups after 1998. To ensure that these only reflect the change in the Delalande tax, we need to be sure to have ruled out any effect from other confounding policies or macroeconomic events. One issue regarding our identification assumption lies in the French reform of the mandatory weekly working time. In 1998, the French Ministry of Labour announced a reduction in the standard workweek from 39 to 35 hours in companies with more than 20 employees. This may have affected workers’ perceived job security in those firms. To ensure that our main result of lower job security following the Delalande tax is not picking up this other reform, we rerun the baseline regression excluding workers in firms with under 20 employees. These results appear in column (1) of Table 6, and are consistent with the baseline results. The positive impact on the perceived job security of older workers is less significant due to the smaller sample size.12 Table 6 The rise in the Delalande tax—ruling out confounding shocks and reforms Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Source: Own calculations. Table 6 The rise in the Delalande tax—ruling out confounding shocks and reforms Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Perceived job security More than 20 employees Keeping workers below age 57 Excluding year 2001 Restricting to firms with 20 to 100 employees Spain Italy (1) (2) (3) (4) (5) (6) BF*Post*Born before 1949 0.08 0.11** 0.08* 0.19* 0.01 –0.06 (0.06) (0.05) (0.05) (0.10) (0.06) (0.06) BF*Post*Born after 1951 –0.12*** –0.10*** –0.08** –0.12* –0.04 –0.05 (0.04) (0.03) (0.04) (0.07) (0.04) (0.03) Observations 9,363 13,897 12,508 3,959 10,485 14,187 Individuals 2,043 2,980 3,003 1,276 2,637 3,361 Note: BF is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The interaction BF*Post is the treatment effect. The standard errors in parentheses are clustered at the individual level. The controls include individual FE, age squared, and dummies for marital status, children in the household, region, and year. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Source: Own calculations. The only major retirement reform implemented between 1994 and 2001 is the creation of the French Reserve Fund in 1999, whose main mission is to guarantee the equilibrium of the pension system. While the creation of this establishment may affect the perceived job security of older workers, there is no reason to believe that it would have affected workers in small and large firms differently. Still, two minor changes of the early retirement scheme, implemented in 2000 and 2001, may be of concern. In 2000, workers above age 57 may apply for early retirement if they occupy physically demanding jobs for a long time. This may affect our estimates if the propensity to be eligible to early retirement via this change in the legislation is correlated to firm size. To test for this, we rerun our regressions without workers above age 57. The results are presented in column (2) of Table 6 and remain unchanged. In 2001, the French government created the ‘pension-equivalent benefit’ (revenu équivalent retraite) scheme for unemployed people below age 60 who contributed more than 40 years. This corresponds to a minimum of EUR 762 per month (replacing, by the way, a previous similar provision). To ensure that our estimates are not influenced by this change, we rerun our regressions excluding observations from 2001. Results, presented in column (3) of Table 6, remain unchanged. While no simultaneous reform is likely to be a valid threat, we may still suspect that small and large firms are hardly comparable and that our estimates only reflect time-varying trends in perceived job security between these two types of firms. To ensure that the treatment and control are really comparable, we can limit the sample to firms relatively close to the 50-employee threshold, in a Regression Discontinuity Design spirit. To do so, we compare firms with 20 to 49 employees to firms with 50 to 100 employees.13 Applying this restriction reduces the sample size by more than 70%. Still, results in column (4) of Table 6 confirm our conclusions. The lower sample size induces higher standard errors, but the estimates remain significant. Finally, we would like to check that our results reflect the French reform, rather than some broader macro-economic trend. We do so by rerunning our baseline regressions on similar samples of workers in neighbouring countries, as the ECHP is harmonized across European countries. Data limitations restrict this comparison to Spain and Italy.14 The difference-in-differences estimates in these countries appear in columns (5) and (6) of Table 6 and are not significantly different from zero. Macroeconomic trends do not seem to be behind our results. 6.2 Using alternative control groups The previous identification strategy uses workers in small firms as the control group to assess the impact of the reform on workers in large firms. We also check our findings using public-sector workers as the controls. As they were not covered by the Delalande tax, we assume that their perceived job security was not affected by the tax scheme. Column (1) of Table 7 shows the results. The new estimates are very similar to the baseline estimates.15 Table 7 The rise in the Delalande tax—robustness checks Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Source: Own calculations. Note: The treatment is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The standard errors in parentheses are clustered at the individual level. The controls include individual FE (expect in columns (2) and (3)), age squared, and dummies for marital status, children in the household, region, and year. Columns (2) and (3) also control for age, gender, and tenure. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. Table 7 The rise in the Delalande tax—robustness checks Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Perceived job security Control group: Public-sector employees OLS Ordered logit Ruling out potential self-selection (1) (2) (3) (4) BF*Post*Born before 1949 0.13*** 0.08 0.13* 0.11** (0.05) (0.05) (0.07) (0.05) BF*Post*Born after 1951 –0.08*** –0.09*** –0.11*** –0.12*** (0.03) (0.04) (0.04) (0.03) Observations 15,497 14,110 14,110 13,484 Individuals 3,361 3,003 3,003 3,003 Source: Own calculations. Note: The treatment is 1 if the individual is working in a big firm and Post is set equal to 1 from 1999 onwards. The standard errors in parentheses are clustered at the individual level. The controls include individual FE (expect in columns (2) and (3)), age squared, and dummies for marital status, children in the household, region, and year. Columns (2) and (3) also control for age, gender, and tenure. *, **, *** indicate significance at the 10%, 5%, and 1% levels, respectively. 6.3 Using different estimation methods In the baseline regressions, we demonstrated that considering treated job security as cardinal or ordinal does not affect our conclusions, which is consistent with Ferrer-i-Carbonell and Frijters (2004). However, individual fixed effects make a difference in Ferrer-i-Carbonell and Frijters (2004). We propose to check whether individual fixed effects make a difference in the present analysis by reestimating our main regressions using a pooled OLS and a pooled ordered logit. Columns (2) and (3) of Table 7 report the results. The results are again qualitatively similar, even if the coefficients do differ slightly from those in the baseline estimates. The FE and OLS estimates may differ for two main reasons. First, fixed-effects models introduce attenuation bias in the case of measurement error, so that OLS estimates are always higher than their FE counterparts in absolute terms. This is not the case here, as the pooled OLS coefficients are smaller than the FE estimates in absolute terms. Selection also plays a role: the OLS estimates are biased if the treatment is correlated with individual unobserved time-invariant characteristics. Comparing the results in columns (2) and (3) of Table 7 to the baseline estimates suggests that treated individuals were those with somewhat lower job security to start with. 6.4 Addressing attrition and self-selection Attrition is a threat to the estimation of our main coefficients. The main plausible scenario is that some workers may have left the sample not randomly but because of the reform. These workers being absent from the sample, they no longer contribute to the estimation of the reform impact. In our case, attrition is a threat if the leaving status is correlated to the changes in perceived job security that the workers would have experienced if they would have remained in the sample. While this assumption seems more plausible for older workers, we proposed in Table 8 to compute the attrition rate that would have been necessary in each age group to cancel out the reform impacts we previously estimated under different hypothetical scenarios. Knowing that the actual attrition rate in each age group is about 8%, any variation lower than one standard deviation of perceived job security is not strong enough to annihilate the main estimates. However, the actual attrition rates are high enough in the most extreme scenarios displayed in columns (5) and (10). To cancel out the reform impacts with 8% of attrition, the loss of older leavers should be at least equal to 1.52 s.d. and the gain of younger leavers should be at least of 1.73 s.d. While attrition is a fair concern in this setting, this calibration exercise shows that it is hardly a real threat to our main estimates. Table 8 Attrition rate and calibration Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Source: Own calculations. Note: This calibration exercise assumes that attrition does not affect the evolution of subjective job security in the control group. A total of 485 individuals constitute the group of non-leavers among older workers and experience an increase of 0.1108 s.d. in perceived job security among older workers. A total of 1,142 individuals constitute the group of non-leavers among younger workers and experience an increase of 0.1108 s.d. in perceived job security. The “Maximal Loss” is equal to the distance between the average perceived job security of leavers just before the reform and 1 (1 being the lowest satisfaction score with respect to job security). This “Maximal Loss” equals 3.13 s.d. and 3.02 s.d., respectively, in columns (5) and (10) for older and younger workers. Table 8 Attrition rate and calibration Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Older workers (1) (2) (3) (4) (5) Hypothetical losses 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal loss Attrition rate 30.71% 18.14% 12.87% 9.97% 3.81% Younger workers (6) (7) (8) (9) (10) Hypothetical gains 0.25 s.d. 0.50 s.d. 0.75 s.d. 1 s.d. Maximal gain Attrition rate 30.82% 18.22% 12.93% 10.02% 4.37% Source: Own calculations. Note: This calibration exercise assumes that attrition does not affect the evolution of subjective job security in the control group. A total of 485 individuals constitute the group of non-leavers among older workers and experience an increase of 0.1108 s.d. in perceived job security among older workers. A total of 1,142 individuals constitute the group of non-leavers among younger workers and experience an increase of 0.1108 s.d. in perceived job security. The “Maximal Loss” is equal to the distance between the average perceived job security of leavers just before the reform and 1 (1 being the lowest satisfaction score with respect to job security). This “Maximal Loss” equals 3.13 s.d. and 3.02 s.d., respectively, in columns (5) and (10) for older and younger workers. Self-selection is another plausible source of bias. Knowing that the reform was announced in 1998 and that we identified significant anticipation effects (especially among young workers), we may also suspect firms close to the 50 employees threshold to marginally adjust their size to select their treatment status. Individual workers may also self-select their treatment status by changing firms before 1999. To account for this potential issue, we exclude employees who switch from a large (small) to a small (large) firm, and those who stay in the same firm but report a change in its size between 1998 and 2001. Applying this restriction reduces the sample size by almost 5%, but results, displayed in column (4) of Table 7, remain strictly unchanged. 7. Conclusion This paper asked how partial employment protection might affect workers’ subjective job security by changing their perceived probability of layoff. We find that the increase in the French Delalande tax, a firing tax restricted to older workers, translates into greater subjective job security for older workers. However, this exogenous rise in older workers’ employment protection also reduced the relative firing cost of younger workers, leading to lower job security for this group. As uncovered workers constitute the large majority of the sample, the aggregate effect on the whole sample of workers is negative. As perceived job security falls with the probability of job loss, the lower perceived job security of younger workers is perfectly consistent with the increase in their layoff rate, compared to younger workers in smaller firms. But the increase in perceived job security of older workers in large firms is not mirrored in their layoff rate. This may reflect that perceived job security not only depends on absolute employment protection but also on its relative level. With the increase in the Delalande tax, older workers may have felt more protected as the layoff rate of their younger colleagues increased. We confirm the predictions of Behaghel (2007) regarding layoffs and the subjective job security of younger workers. However, we should also emphasize that we have not explored his predictions regarding job creation, which might affect both workers and the unemployed. In particular, our analysis did not allow us to see whether employment protection reduces the probability that the unemployed find work. The investigation of the relation between partial employment-protection reforms and job finding, and how this affects workers’ subjective job security, is a promising subject for future research. Since the results are estimated using unweighted linear and nonlinear models, we should stress that the average negative effect induced by the Delalande tax reform only supports a basic utilitarian welfare analysis. We could assume that job security may be more important for the well-being of older workers than younger workers, producing a greater weight on the job satisfaction of the former, and the potential for net welfare gains. Supplementary material Supplementary material is available online at the OUP website. This material consists of an online appendix and the replication (stata.do) files. The data used in this paper is confidential. Footnotes 1 See among others Kugler et al. (2002); Gómez-Salvador et al. (2004); Boeri and Jimeno (2005); Autor et al. (2007); Von Below and Thoursie (2010). 2 See Blanchard and Landier (2002); Dolado et al. (2002); Kugler et al. (2002); Gómez-Salvador et al. (2004); Boeri and Jimeno (2005); Autor et al. (2007); Kugler and Pica (2008). 3 The main differences from previous models are segmentation of the labour market into age sub-markets, each of which has its own matching function, and the inclusion of firing costs for older workers. See Behaghel (2007) for more technical details. 4 There is of course also an effect on hiring, as with any transaction tax on the labour market. By the construction of the Law, this hiring effect applies to all age groups equally. 5 More details are available at http://ec.europa.eu/eurostat/web/microdata/european-community-household-panel (last accessed 18 December 2017). 6 We do not use weights in our regressions, but the ECHP provides different survey weights. We followed the documentation and used the survey weights designed for longitudinal analysis at the country level. Whatever the model used or the equation estimated, results are not affected by the use of the ECHP weights. 7 A large branch of the literature has already suggested that utility is relative. If subjective job security is also relative, we might also expect comparison effects here. 8 The difference in sample size is due to the use of the BUC estimator that increases artificially the number of individual observations. 9 A total of 76% of treated workers are younger unprotected workers. 10 This age interval is larger than the other intervals, as the age distribution in our sample is left-skewed. 11 The estimates and standard errors appear in Table A3 in the Appendix. 12 One may also fear that firms with more than 50 workers were early adopters of the reduced workweek. We tested whether working time was reduced earlier in firms with more than 50 workers than firms with 20 to 49 workers. But working time only started to decrease significantly in 2001, and there is no significant difference across firm size. Results are available upon request. 13 A strict Regression Discontinuity Design would require estimating the treatment effect in a narrower window, but firm size in ECHP is only reported using bands. 14 Perceived job security is not measured after 1997 in Germany, and the information in the last waves of the ECHP in Belgium is insufficient to accurately differentiate the public and private sectors. 15 We also used both workers from small firms and in the public sector as a control group. This led to very similar results, which are available on request. Acknowledgments We are particularly indebted to Andrew Clark and Claudia Senik. We are also grateful to Philippe Askenazy, Fabrice Etilé, Paul Frijters, Marc Gurgand, David Margolis, Barbara Petrongolo, and Gilles Saint-Paul. We would like to thank the two anonymous referees for their constructive and detailed advice, which has substantially improved the paper. 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Oxford Economic PapersOxford University Press

Published: Mar 19, 2018

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