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Who Pays for it? The Heterogeneous Wage Effects of Employment Protection Legislation

Who Pays for it? The Heterogeneous Wage Effects of Employment Protection Legislation Abstract This study estimates the effect of employment protection legislation on wages, exploiting the 1990 Italian reform that introduced unjust dismissal costs for firms below 15 employees. We find that the slight average wage reduction induced by the reform hides highly heterogeneous effects. Workers who change firm during the reform period suffer a drop in the entry wage, while incumbent workers are left unaffected. Also, the negative effect of the reform is stronger for young blue collars, low‐wage workers and workers in low‐employment regions. This pattern suggests that the ability of employers to shift firing costs onto wages depends on workers’ relative bargaining power. Since the work of Lazear (1990), it is well known that, in a perfectly competitive labour market and in the absence of contractual frictions, a government‐mandated pure transfer (e.g. a severance payment) from firms to risk‐neutral workers can be neutralised by an appropriately designed wage contract that lowers the entry wage by an amount equal to the expected present value of the future transfer. A negative effect of Employment Protection Legislation (EPL) on the entry wage is also predicted by models with labour market frictions and decentralised bargaining in which job‐security provisions weaken the threat point of the firm in negotiations with already employed workers. In both contexts, the impact of EPL on the wage profile is tantamount to a newly hired worker posting a bond equal to his share of the future severance payment (Mortensen and Pissarides, 1999; Ljungqvist, 2002; Garibaldi and Violante, 2005). Thus, theory predicts a differential impact of firing costs across incumbent and newly‐hired workers – insiders and outsiders in Lindbeck and Snower’s (1988) terminology. The impact of EPL on wages is also likely to be heterogeneous across workers with different characteristics potentially correlated with their bargaining position and across local labour markets. For instance, workers with a high degree of risk aversion who value job security may be more willing to accept a wage cut in exchange for an increase in EPL (Pissarides, 2001; Bertola, 2004), while workers in tight labour markets may be able to avoid paying for the increased protection thanks to a better outside option (Pissarides, 2000). Overall, the impact of EPL on wages is likely to depend on the bargaining position of workers vis‐à‐vis employers, which in turn depends on the labour market status of the worker (incumbent/new‐hire), on his individual characteristics and on the aggregate labour market conditions that determine firms’ and workers’ outside options. This study provides an empirical analysis of the effects of EPL on wages, exploiting the variation in EPL induced by an Italian reform, which raised dismissal costs for firms with 15 or fewer employees and left costs unchanged for larger firms. We provide complementary evidence to Kugler and Pica (2008), who use the same reform episode to estimate, as most of the empirical literature on EPL, the effect of firing costs on worker and job flows.1 We focus, instead, on the adjustment through the wage rate, a margin on which the available evidence is scant and provides ambiguous results: Autor et al. (2006) find no significant effect of wrongful‐discharge laws on wage levels in the US; Cervini Plá et al. (2010) show that the 1997 Spanish reform that lowered both firing costs and payroll taxes had a positive effect on wages; Van der Wiel (2010) finds opposite results for the Netherlands using a reform that affected differently high and low‐tenured workers. The contribution of this study is not only to quantify the causal effect of EPL on wages but also and foremost to highlight the heterogeneity of the effect and to relate it to the role of the relative bargaining power of workers and firms, thus drawing a lesson which goes arguably beyond the Italian experience. The focus on the heterogeneity of the wage effects of EPL across workers makes this study distinct also from previous studies, which use firm‐level data on wages (Bird and Knopf, 2009; Martins, 2009) or productivity (Autor et al., 2007; Cingano et al., 2010). The analysis is based on administrative data from the Italian Social Security Institute (INPS), and exploits a matched employer–employee panel, which contains the entire population of workers and firms located in the Italian provinces of Vicenza and Treviso in the north‐eastern region of Veneto. The data are well suited for studying the effect of the 1990 EPL reform because the Italian North‐East is characterised by a high concentration of small firms and a tight labour market, which makes it similar to many manufacturing regions in Europe. Moreover, as explained below, the richness of this data set allows us to build suitable instruments and apply instrumental variables (IV) techniques. Our identification strategy exploits an EPL reform, which provides variation both across firms and over time, allowing us to combine a regression discontinuity design (RDD) with a difference‐in‐difference (DID) approach. Until 1990, the Italian labour code provided a sharp discontinuity in the application of EPL, with no protection for workers employed in small firms below the 15‐employee threshold and high protection for those employed in firms above the threshold. In July 1990, severance payments were increased from zero to between 2.5 and 6 months of pay for firms with 15 or fewer employees and left unchanged for firms with more than 15 employees. In the course of the study, we address the potential endogeneity of the treatment status. On the one side, to control for the sorting of firms into (or out of) the treatment group according to time‐invariant characteristics, we estimate models with firm fixed effects. In addition, we instrument the treatment status with firm size in 1988 and 1987, when the reform was not in place and was unexpected, to control for time‐varying factors that may affect firms’ sorting behaviour. On the other side, we control for the sorting of workers according to fixed individual characteristics into firms above or below the threshold by estimating worker and match (worker–firm) fixed‐effects models. We regard the IV model with worker fixed effects as our preferred specification, because it controls both for the sorting of workers due to time‐invariant characteristics and for the sorting of firms due to time‐varying factors, including the reform itself. Our analysis indicates a small and generally significant wage loss in firms below the 15‐employee threshold relative to larger firms after the 1990 reform, which amounts to a 1.1 percentage point in our preferred specification. To test the validity of the ‘common time effects’ assumption implicit in the DID approach, we adopt a triple‐difference strategy that exploits the different relevance of the constraints imposed by EPL on firms in different sectors. In particular, we look at whether the impact of EPL is greater in industries in which the need for labour reallocation is higher, and find that wages fell more markedly in sectors with greater pre‐reform employment volatility. This suggests that results are not driven by small‐firm wages being on a declining time path with respect to wages in larger firms. We next investigate whether the estimated negative wage effect of EPL is uniform across workers. As suggested by theory, we first check whether the EPL reform has a different impact on insiders and outsiders. To this aim, we identify two groups of workers: a group of incumbent workers, which includes all individuals who are already employed in a firm at the time of the introduction of the reform in 1990 and stay continuously in the same firm over our sample period; and a group of movers, that is, a group of workers who change firm at least once, before or after 1990, for whom we observe at least one entry wage. The evidence indicates that, after the reform, movers suffer a drop in the wage rate of 2.5% in treated firms below the threshold relative to larger firms, while incumbent workers are left unaffected. In addition, the estimates show that the negative effect on movers is concentrated upon entry in the new firm, with a reduction of the entry wage of 6.3% in our preferred specification. Post‐entry wages of movers are unaffected by the introduction of the EPL reform. Thus, on the one hand, firms seem to be able to translate (part of) the cost of EPL onto workers before the match is formed, when they do not incur any severance payment if there is no agreement. On the other hand, incumbent workers and movers in the years following entry in the new firm do not seem to be able to renegotiate their wages upwards (MacLeod and Malcomson, 1993). We then look at whether the impact of EPL on wages depends on individual characteristics presumably correlated with workers bargaining power in the employment relationship, and find that the negative wage effect of the EPL reform is stronger among low‐bargaining power workers, such as young blue‐collar workers (Dolado et al., 2007). Furthermore, but unfortunately only for part of the sample, we have a direct measure of bargaining power, given by the individual wage premium over the sectoral contractual minimum – the wage drift.2 Results from quantile regressions suggest that workers at the 5th percentile of the distribution of the wage drift suffer a wage reduction five times as large as workers at the 90th percentile and three times as large as the average effect. Finally, we exploit the theoretical insight that the bargaining power of workers should also depend on the local labour market conditions that affect workers’ and firms’ relative outside options, through the probabilities of finding a job and filling a vacancy. To test this idea, we look at a sample of workers over the whole Italian territory and proxy the tightness of the local labour markets using the annual regional employment rates of males aged 25–64. We find evidence suggesting that workers in low‐employment regions suffer higher wage reductions in firms below the threshold relative to larger firms after the reform. The rest of this article is organised as follows. Section 1. lays out the theoretical and institutional background of our empirical analysis. Section 2. describes the data set and the sample selection rules. Section 3. explains the identification strategy and Section 4. presents estimates of the average causal effects of stricter EPL on wages. Section 5. investigates the heterogeneity of the wage effects along multiple dimensions: insiders/outsiders, workers with different observable characteristics correlated with their bargaining position and wage effects at different point of the wage drift distribution and in regions with different labour market conditions. Section 6. discusses the results and concludes. 1. Background 1.1. Theoretical Background Under Nash bargaining, firing costs affect firms’ outside option in bilateral wage negotiations with workers because, in the absence of a wage agreement, firms have to pay severance with an associated drop in profits.3 In their standard matching model with a two‐tier wage structure, Mortensen and Pissarides (1999) assume that the firm does not incur any firing costs if there is no agreement on the wage in the first encounter because no employment relationship yet exists. In this framework, workers pre‐pay for higher EPL via lower entry wages and enjoy a subsequent one‐shot increase in post‐entry wages as in Lazear (1990).4 Therefore, the model predicts a negative effect of EPL on workers’ cumulative wage bill (net of firing costs) and a distinction between the effect on entry and post‐entry wages. To better understand the mechanism, consider the choice facing the firm and the worker when they first meet (Pissarides, 2000). If they sign the contract, the pay‐off to the firm is J0 ⁠. Therefore, the initial wage w0 is chosen to maximise the product B0=(W0−U)β(J0−V)1−β ⁠, where V and J0 are the firm’s net worth from a vacancy and from a job paying w0 ⁠, and W0 and U are the worker’s net worth from a job paying w0 and unemployment. After the worker is taken on, if the firm fails to agree on a continuation wage, its loss will be J++F where F is the firing cost. Therefore, the post‐entry wage maximises B+=(W+−U)β(J++F−V)1−β ⁠. Of course, a crucial point is whether workers are able to force a wage renegotiation after entry. MacLeod and Malcomson (1993) argue that they cannot because they have no credible threat if the firm refuses to renegotiate. However, if renegotiation takes place, the model predicts tighter employment protection to increase wages in post‐entry negotiations to reflect the fact that, once the job has started, the firm is locked into the relationship by the firing tax. Anticipating this, employers reduce wages at entry when the worker is still unprotected.5 Notice that while the model described above offers predictions on the effect of the introduction of EPL on the wage level, it is not equally helpful in understanding the effects of EPL on workers’ wage‐tenure profile. An increase in EPL implies a stepwise increase in the wage of incumbent workers (and also of movers’ post‐entry wages) if workers can force a wage renegotiation, but does not change the slope of the wage‐tenure profile. The reason is that, as most studies in this literature (with some exceptions, see e.g. Cozzi et al., 2011), the above model assumes that productivity – and therefore wages – does not vary with tenure. This assumption makes it unsuitable for studying how EPL affects the evolution of workers’ wages with respect to their tenure in the firm. The empirical studies analysing the relationship between EPL and workers’ tenure profile go beyond the standard matching model and are typically based on incentive mechanisms (Autor, 2003; Ichino and Riphahn, 2005; Wasmer, 2006; Belot et al., 2007; Scoppa, 2010). For a more detailed discussion and for empirical results on the effects of EPL on tenure profiles, we refer the reader to the working paper version Leonardi and Pica (2010). 1.2. Institutional Background As a form of worker protection for open‐ended contracts, labour codes specify the causes for fair dismissal, and establish workers’ compensation depending on the reason for termination.6 Over the years, the Italian legislation ruling unfair dismissals has changed several times. Both the magnitude of the firing cost and the coverage of the firms subject to the restrictions have gone through extensive changes. Individual dismissals were first regulated in Italy in 1966 through Law 604, which established that employers could freely dismiss workers either for economic reasons (considered as fair ‘objective’ motives) or in the case of misconduct (considered either as fair ‘subjective’ motive or as just cause). In any case, workers could take employers to court and judges would determine if the dismissals were indeed fair or unfair. In the case of unfair dismissal, employers had the choice of either reinstating the worker or paying severance, which depended on firm size and – loosely – on tenure. Firms with fewer than 60 employees had to pay half the severance paid by firms with more than 60 employees, and firms with fewer than 35 workers were completely exempt.7 In 1970, the Statuto dei Lavoratori (Law 300) established that all firms with more than 15 employees had to reinstate workers and pay their foregone wages in cases of unfair dismissals. Firms with fewer than 15 employees remained exempt. Finally, Law 108 was introduced in July 1990 restricting dismissals for permanent contracts in small firms. This law introduced severance payments of between 2.5 and 6 months pay for unfair dismissals in firms with 15 or fewer employees.8 Firms with more than 15 employees still had to reinstate workers and pay foregone wages in cases of unfair dismissals. This means that the cost of unfair dismissals for firms with fewer than 15 employees increased relative to the cost for firms with more than 15 employees after 1990. For our purposes, this reform has two attractive features. First, it was largely unexpected: the first published news of the intention to change the EPL rules for small firms appeared in the main Italian financial newspaper – Il Sole 24 Ore – at the end of January 1990. Second, it imposed substantial costs on small firms: Kugler and Pica (2008) look at the effect of this reform on job and workers flows and find that accessions and separations decreased by about 13% and 15% in small relative to large firms after the reform. At the end of the article, we will comment on the relative importance of the adjustment through employment and wages. The 15‐employee threshold is not only relevant for EPL provisions but also for the establishment of trade union representatives at firm level. However, our identification is not affected by this rule given that there are no reforms on this matter over our sample period. In addition, in 1992, two other legislative changes were introduced. The first was a pension reform, which changed retirement ages and reference periods for calculating pensions. The second initiative eliminated a wage indexation mechanism (Scala Mobile) that had been in place since 1945 for firms of all sizes. As these reforms do not apply differentially to firms of different sizes, they also do not threaten the validity of our identification strategy. The only reform that may potentially confound our results is the collective dismissals reform that took place in 1991. A special procedure was introduced for firms with more than 15 employees willing to dismiss five or more workers (within 120 days) because of plant closure or restructuring. The collective dismissals’ procedures require a credible risk of bankruptcy and firms are required to engage in negotiations with unions and the government to reach an agreement on the dismissals. However, if public administration officials determine that an agreement cannot be reached, the firm is free to downsize and the employees are not allowed to take the firm to court, that is, collective dismissals do not impose additional firing costs on firms. In Section 4., we will test whether our results are confounded by the effects of this reform. 2. Data Description This study uses the Veneto Workers History (henceforth VWH) data set, which is an employer–employee panel with information on the characteristics of both workers and firms. The longitudinal panel is constructed from the administrative records of the Italian Social Security System (INPS). It refers to the entire population of employers and workers of the private sector in two provinces, Treviso and Vicenza, of the Italian region of Veneto located in the north‐eastern part of the country. The overall population in the two provinces was 1.6 million people (2.7% of the total Italian population) as of the 2001 Population Census. Starting from a relatively backward economic condition after the Second World War, Veneto enjoyed fast growth in the post‐war period first reaching the national average GDP per capita and then outgrowing it: in 2000, GDP per capita in Veneto was 20% higher than the national average. There are two reasons for using these data. The first is that, although limited to two provinces, the data are well suited for studying the effect of the 1990 EPL reform because the Italian North‐East is characterised by a high concentration of small firms and a tight labour market, which makes it similar to many manufacturing regions of France or Germany. Therefore, the results may be relevant for other labour markets outside Veneto.9 The second reason is that we need information on the universe of workers and firms to be able to build suitable instruments for firm size and apply IV techniques. A random sample of the whole Italian working population is available from the same administrative source but it is a representative sample of workers and not of firms. Therefore, it does not allow us to build appropriate instruments for firm size and estimate IV models. For this reason, we only use the nationwide random sample in subsection 5.4. to look at the differential effect of the reform across local labour markets. The VWH data set includes universal information on all firms and employees working at least one day in any firm of the two provinces from 1985 to 1997. In particular, it includes information on employees’ age, gender, occupation (blue collar/white collar), yearly wage, number of paid weeks, type of contract (permanent/temporary) and information on firms’ location, sector and firm size – which is not an integer because it is measured as the average number of employees weighted by the number of worked months.10 No information on education is available. The unit of observation is the employer‐day; such information is used to build a complete history of the working life of each employee. Once they are in the data set, employees are followed, independently of their place of residence, even in their occupational spells (in the private sector) out of Treviso and Vicenza. The original archives only include information on private sector firms in the manufacturing and service sectors, therefore all workers in the public sector, agriculture and self‐employment are excluded. This selection is common for administrative data, which typically include the private sector only. As the individual longitudinal records are generated using social security numbers and collect information on private sector employees for the purpose of computing retirement benefits, employees are only followed through their employment spells. The only reason of dropping out of the data set is exit from the private sector or from the employment status altogether. The data stop following individuals who move into self‐employment, public sector, agricultural sector, underground economy, unemployment or retirement.11 2.1. Sample Selection We select all males between 20 and 55 years of age, hired on an open‐ended contract, with a valid wage between 1989–93. We exclude females because the trade‐off between job security and wages is likely to be affected by fertility decisions on which we have no information.12 We also exclude workers on temporary contracts because employment protection provisions are guaranteed only to workers on open‐ended contracts. To stay as close as possible to the reform year 1990, we focus on the period 1989–93 excluding years 1988 and 1987 to be able to use firm size in those pre‐reform out‐of‐sample years as instruments for current firm size. We also remove year 1990 because the reform occurred in the month of July and the annual wages of year 1990 are likely to be a mixture of pre‐reform and post‐reform wages. However, we test the robustness of our results both to different time periods (see Table C3 in Appendix C) and to the inclusion of 1990 (Table 2). To preserve comparability between treatment and control groups, we further select the sample to firms within the interval 5–25 employees. For robustness, in Appendix C, we experiment with the optimal bandwidth method. In the course of the study, we use weekly wages (annual wages divided by the number of weeks worked) after eliminating the upper and lower 1% of the wage distribution in each year. Where the same individual has multiple employment spells in different firms in the same year, we keep the longest spell. The final sample includes 9,914 firms and 29,177 workers for a total of 96,333 observations. We observe an entry wage for about one‐third of the sample, namely for the 9,667 workers (28,451 observations) who changed firm at least once over our sample period. The remaining 19,510 workers (67,882 observations) stayed with the same firm throughout the sample period. Descriptive statistics for the main variables used in the analysis are shown in Table 1. The number of small firms (5–15) is higher than the number of large firms (16–25), so is the number of workers employed in small firms, both before and after the reform. The real weekly wage of workers in large firms is around 307 (331) euro at 1995 prices per week before (after) the reform versus a significantly lower wage of 293 (313) euro per week in small firms before (after) the reform. The average age of workers is not significantly different across the two groups, while larger firms employ a slightly higher proportion of white‐collar workers and, as expected, have a slightly lower turnover (i.e. they employ a lower proportion of movers). Table 1. Descriptive Statistics . Pre‐reform . Post‐reform . . Small firms . Large firms . Small firms . Large firms . Real weekly wages 293.738 307.454 312.923 331.243 (72.011) (82.479) (78.545) (90.367) Firm size 9.604 19.496 9.541 19.551 (2.953) (2.824) (2.958) (2.830) White‐collar dummy 0.134 0.161 0.133 0.165 (0.340) (0.368) (0.340) (0.371) Movers (proportion) 0.309 0.258 0.313 0.268 (0.462) (0.438) (0.464) (0.443) Age 34.565 34.990 37.489 37.918 (8.556) (8.498) (8.675) (8.623) Sectoral dummies Agriculture 0.007 0.004 0.006 0.005 (0.080) (0.065) (0.077) (0.071) Gas–water–oil 0.001 0.000 0.001 0.000 (0.030) (0.000) (0.030) (0.000) Extraction–minerals–chemical 0.079 0.091 0.077 0.103 (0.270) (0.288) (0.267) (0.305) Metal 0.274 0.330 0.271 0.311 (0.446) (0.470) (0.445) (0.463) Manufacturing 0.244 0.297 0.237 0.292 (0.430) (0.457) (0.425) (0.455) Construction 0.154 0.110 0.163 0.109 (0.361) (0.313) (0.369) (0.312) Wholesale–retail–hotel 0.182 0.108 0.184 0.118 (0.386) (0.311) (0.388) (0.323) Transportation 0.031 0.025 0.034 0.026 (0.173) (0.156) (0.180) (0.158) Banks–insurance 0.012 0.012 0.010 0.014 (0.107) (0.110) (0.099) (0.118) N 15,965 8,342 45,848 26,178 . Pre‐reform . Post‐reform . . Small firms . Large firms . Small firms . Large firms . Real weekly wages 293.738 307.454 312.923 331.243 (72.011) (82.479) (78.545) (90.367) Firm size 9.604 19.496 9.541 19.551 (2.953) (2.824) (2.958) (2.830) White‐collar dummy 0.134 0.161 0.133 0.165 (0.340) (0.368) (0.340) (0.371) Movers (proportion) 0.309 0.258 0.313 0.268 (0.462) (0.438) (0.464) (0.443) Age 34.565 34.990 37.489 37.918 (8.556) (8.498) (8.675) (8.623) Sectoral dummies Agriculture 0.007 0.004 0.006 0.005 (0.080) (0.065) (0.077) (0.071) Gas–water–oil 0.001 0.000 0.001 0.000 (0.030) (0.000) (0.030) (0.000) Extraction–minerals–chemical 0.079 0.091 0.077 0.103 (0.270) (0.288) (0.267) (0.305) Metal 0.274 0.330 0.271 0.311 (0.446) (0.470) (0.445) (0.463) Manufacturing 0.244 0.297 0.237 0.292 (0.430) (0.457) (0.425) (0.455) Construction 0.154 0.110 0.163 0.109 (0.361) (0.313) (0.369) (0.312) Wholesale–retail–hotel 0.182 0.108 0.184 0.118 (0.386) (0.311) (0.388) (0.323) Transportation 0.031 0.025 0.034 0.026 (0.173) (0.156) (0.180) (0.158) Banks–insurance 0.012 0.012 0.010 0.014 (0.107) (0.110) (0.099) (0.118) N 15,965 8,342 45,848 26,178 Notes. Sample of years 1989–93, all males aged 20–55 with an open‐ended contract in firms of between 5 and 25 employees. Real wages are expressed in 1995 euro. Movers are defined as workers who change firm at least once over the period 1989–93. Standard deviations in parentheses. Open in new tab Table 1. Descriptive Statistics . Pre‐reform . Post‐reform . . Small firms . Large firms . Small firms . Large firms . Real weekly wages 293.738 307.454 312.923 331.243 (72.011) (82.479) (78.545) (90.367) Firm size 9.604 19.496 9.541 19.551 (2.953) (2.824) (2.958) (2.830) White‐collar dummy 0.134 0.161 0.133 0.165 (0.340) (0.368) (0.340) (0.371) Movers (proportion) 0.309 0.258 0.313 0.268 (0.462) (0.438) (0.464) (0.443) Age 34.565 34.990 37.489 37.918 (8.556) (8.498) (8.675) (8.623) Sectoral dummies Agriculture 0.007 0.004 0.006 0.005 (0.080) (0.065) (0.077) (0.071) Gas–water–oil 0.001 0.000 0.001 0.000 (0.030) (0.000) (0.030) (0.000) Extraction–minerals–chemical 0.079 0.091 0.077 0.103 (0.270) (0.288) (0.267) (0.305) Metal 0.274 0.330 0.271 0.311 (0.446) (0.470) (0.445) (0.463) Manufacturing 0.244 0.297 0.237 0.292 (0.430) (0.457) (0.425) (0.455) Construction 0.154 0.110 0.163 0.109 (0.361) (0.313) (0.369) (0.312) Wholesale–retail–hotel 0.182 0.108 0.184 0.118 (0.386) (0.311) (0.388) (0.323) Transportation 0.031 0.025 0.034 0.026 (0.173) (0.156) (0.180) (0.158) Banks–insurance 0.012 0.012 0.010 0.014 (0.107) (0.110) (0.099) (0.118) N 15,965 8,342 45,848 26,178 . Pre‐reform . Post‐reform . . Small firms . Large firms . Small firms . Large firms . Real weekly wages 293.738 307.454 312.923 331.243 (72.011) (82.479) (78.545) (90.367) Firm size 9.604 19.496 9.541 19.551 (2.953) (2.824) (2.958) (2.830) White‐collar dummy 0.134 0.161 0.133 0.165 (0.340) (0.368) (0.340) (0.371) Movers (proportion) 0.309 0.258 0.313 0.268 (0.462) (0.438) (0.464) (0.443) Age 34.565 34.990 37.489 37.918 (8.556) (8.498) (8.675) (8.623) Sectoral dummies Agriculture 0.007 0.004 0.006 0.005 (0.080) (0.065) (0.077) (0.071) Gas–water–oil 0.001 0.000 0.001 0.000 (0.030) (0.000) (0.030) (0.000) Extraction–minerals–chemical 0.079 0.091 0.077 0.103 (0.270) (0.288) (0.267) (0.305) Metal 0.274 0.330 0.271 0.311 (0.446) (0.470) (0.445) (0.463) Manufacturing 0.244 0.297 0.237 0.292 (0.430) (0.457) (0.425) (0.455) Construction 0.154 0.110 0.163 0.109 (0.361) (0.313) (0.369) (0.312) Wholesale–retail–hotel 0.182 0.108 0.184 0.118 (0.386) (0.311) (0.388) (0.323) Transportation 0.031 0.025 0.034 0.026 (0.173) (0.156) (0.180) (0.158) Banks–insurance 0.012 0.012 0.010 0.014 (0.107) (0.110) (0.099) (0.118) N 15,965 8,342 45,848 26,178 Notes. Sample of years 1989–93, all males aged 20–55 with an open‐ended contract in firms of between 5 and 25 employees. Real wages are expressed in 1995 euro. Movers are defined as workers who change firm at least once over the period 1989–93. Standard deviations in parentheses. Open in new tab 3. Identification Strategy The estimand of interest is the average treatment effect of EPL on wages. We exploit both the discontinuity in EPL at the 15‐employee threshold and the reform of EPL, which affected only small firms to build an RDD combined with a DID strategy to estimate the causal effect of EPL on wages. To identify the impact of dismissal costs on wages, we compare the change in mean wages paid by firms just below 15 employees before and after the 1990 reform to the change in mean wages paid by firms just above 15 employees. In other words, the assumption that guarantees that the effect of EPL on wages can be interpreted as causal is that any variable that affects wages is either continuous at the threshold (as in standard RDD) or its discontinuity is constant over time (as in standard DID). Another identification assumption is that the average wage of individuals employed in firms marginally below the 15 employees threshold (5–15) is expected to diverge from the wage of the control group employed in firms just above the threshold (16–25) for no other reason than the reform, a reasonable assumption in a neighbourhood of the threshold. If workers and firms were exogenously assigned to the treatment and control groups, ordinary least squares (OLS) estimates of the following model would identify the causal effect of EPL on wages: Yijt=β’Xijt+δ1DjtS+δ2(DjtS×Post)+∑k=13(γkfsizejtk)+eijt(1) −97DjtS=1[firm size≤15in yeart] =1[year≥1991]. The dependent variable is the log of the weekly wage paid to worker i by firm j in year t and is given by the yearly wage divided by the number of paid weeks. The variable Post is a dummy that takes the value of 1 starting from 1991 and zero otherwise; DjtS is a dummy that takes the value of 1 if the worker is employed in year t in a firm with 15 or fewer employees and 0 if the worker is employed in a firm with strictly more than 15 employees (in what follows we will refer to this dummy as the small‐firm dummy). The interaction term DjtS×Post between the small‐firm dummy and the post‐reform dummy is included to capture the effect of the EPL reform. All specifications contain a polynomial of third degree in firm size. Appendix C shows that results are robust to this functional form assumption. The matrix Xijt includes age dummies, an occupation (white collar/blue collar) dummy, nine industry dummies and year dummies which account for macro shocks (and prevent the identification of the post‐reform dummy). The error term eijt is allowed to include, in turn, worker firm and match (worker–firm) fixed effects. The reported standard errors account for possible error correlations at the individual level in all specifications. As remarked above, our differences‐in‐differences strategy relies on the ‘common time effects’ assumption, according to which treated and untreated workers are on the same time path. However, small firms may be on a declining time path with respect to larger firms above the threshold and may also be differentially affected by the business cycle. Violation of the ‘common time effects’ assumption – although unlikely in a small neighbourhood of the 15‐employee threshold – would bias our results. To account for this potential source of bias, we allow for the possibility that the introduction of dismissal costs has stronger effects in more volatile sectors, where these costs are likely to bind (Micco and Pagés, 2006), as follows: Yijt=β’Xijt+γ1DjtS+γ2(DjtS×Post)+γ3VSk+γ4(VSk×DjtS)+γ5(VSk×Post)+γ6(VSk×Post×DjtS)+∑k=13(γkfsizejtk)+eijt.(2) The variable VSk denotes the variance of employment growth in sector k during the pre‐reform period calculated separately for firms above and below the 15‐employee threshold. The coefficient γ6 captures the differential effect of the reform in firms below the threshold relative to larger firms with more than 15 employees in sectors with different pre‐reform employment volatility. Equations (1) and (2) give unbiased estimates only if workers and firms are exogenously assigned to the treatment status. However, the conditional comparison of wages in firms on the two sides of the threshold does not provide an unbiased estimate of the average treatment effect if firms and workers with different unobservable characteristics endogenously choose their treatment or control status: individuals may decide to work in firms below or above the threshold and firms in turn may decide to grow above or shrink below the 15‐employee threshold. Thus, a fundamental concern is the non‐random selection of workers and firms above and below the 15‐employee threshold to which we now turn. 3.1. The Distribution of Firm Size and Firm Sorting Estimates of (1) and (2) using firm fixed effects control for all time‐invariant unobserved factors that may affect the propensity of firms to self‐select into (or out of) treatment. However, they do not account for the selection due to the reform itself. Firms in a neighbourhood of the 15‐employee threshold may change their size in response to the 1990 reform of EPL, thus biasing the estimates. For example, firms which keep their size just below 15 employees before the reform to avoid strict EPL rules, may increase their size because the reform makes the gap in EPL provisions narrower. The sign of the bias is not easy to establish and depends on which type of firms move because of the reform. If firms which move from below to above the threshold are those with bad growth perspectives and lower productivity (thus reducing the distance between wages paid in the treatment and in the control group of firms), then presumably OLS estimates understate the negative effect of the reform on wages. On the other hand, OLS would overestimate the negative effects if firms which move are high‐productivity firms. In this section, we assess the validity of our identification strategy with two different procedures. First, we formally check for the absence of manipulation of the running variable (violated if firms were able to alter their size and sort above or below the threshold) testing the null hypothesis of continuity of the density of firm size at 15 employees as proposed by McCrary (2008). Second, we check whether the probability of firm growth around the 15‐employee threshold changes after the reform. In the left panels of Figure Figure Fig. 1.., we plot the frequency of firms between 5 and 25 employees in year 1989 (before the reform) and in year 1991 (after the reform). Visual inspection does not reveal any clear discontinuity at the 15‐employee threshold, only a small dip in the distribution at 16. In the right panels of Figure Figure Fig. 1.., we formally test for the presence of a density discontinuity at the threshold by running kernel local linear regressions of the log of the density separately on both sides of the threshold (McCrary, 2008). Apparently, there is no evidence of manipulative sorting: the log‐difference between the frequency to the right and to the left of the threshold is not statistically significant, neither in 1989 nor in 1991. The point estimate is −0.071 (0.090) in 1989 and 0.141 (0.087) in 1991. Fig. 1. Open in new tabDownload slide Firm Size Distribution Notes. Frequency of firm size in 1989 and 1991 (left panels). McCrary test of density continuity (right panels): weighted kernel estimation of the log density, performed separately on either side of the threshold. Optimal bin width and bin size as in McCrary (2008). Fig. 1. Open in new tabDownload slide Firm Size Distribution Notes. Frequency of firm size in 1989 and 1991 (left panels). McCrary test of density continuity (right panels): weighted kernel estimation of the log density, performed separately on either side of the threshold. Optimal bin width and bin size as in McCrary (2008). The density tests shown in Figure Figure Fig. 1.. may, however, have low power if manipulation occurs on both sides of the threshold. In that case, non‐random sorting is not detectable looking at the distribution of the running variable. For this reason, in Appendix A.1, we perform a further test to verify whether firms sort around the threshold at the time of the reform: we compare the probability of firm growth before and after the reform conditioning on lagged firm size and pre‐reform conditional average wages. Consistently with Borgarello et al. (2004) and Schivardi and Torrini (2008), results in Table A1 (Appendix A.1) show that firms just below 15 employees are about 3% less likely to grow than larger firms, but the effect is not significantly different before and after the reform and for firms with different average pre‐reform wages. The reader may be puzzled by the apparent inconsistency between a large difference in EPL at the 15‐employee threshold and the continuity of the firm size distribution. The average firm size in Italy is approximately half that of the European Union and expensive EPL for firms with more than 15 employees is often indicated as one of the factors responsible for such a skewed size distribution. This claim is not confirmed by the available empirical evidence. Schivardi and Torrini (2008) explain this finding arguing, first, that firms on a growing (or shrinking) pattern may find themselves temporarily slightly above 15 employees and, second, that firms may adjust other margins to cope with stricter EPL. In this article we investigate the possibility that protected workers pay for the additional EPL with lower wages.13 Overall, this section shows that there is little evidence of sorting according to observables. While this is reassuring, unobservable components may still drive firms’ sorting behaviour. Firm fixed‐effect models do allow the analyst to control for the sorting due to to unobservable time‐invariant characteristics, but leave time‐varying unobservable factors unaccounted for. For this reason, we adopt the IV strategy outlined below. 3.2. The IV Model To control for the sorting induced by time‐varying factors, including the reform itself, we instrument the treatment status with firm size in the pre‐reform period. To reduce the concern that the instrument is affected by the reform, we disregard the immediate pre‐reform year 1989 and use as instruments firm size in years 1987 and 1988, prior to the years considered in the benchmark sample 1989–93. The formal specification of the IV model is: logwijt=β’Xijt+δ1DjtS+δ2(DjtS×Post)+∑k=13(γkfsizejtk)+υijt(2) DjtS=γ0’Xijt+γ2SjpreS+γ3(SjpreS×Post)+∑k=13(γkfsizejtk)+νjt, where SjpreS is a vector that includes firm size in 1988 and in 1987. The term DjtS×Post is also instrumented using as an instrument SjpreS×Post ⁠. The matrix Xijt contains the same controls as in (1). Notice that to build the instruments, it is necessary to follow firms over time. For this reason, it is crucial to have information on the universe of workers and firms, as the VWH data set described in Section 2. does. Figure Figure Fig. 2.. captures the key element of the relationship between the running variable (the dummy DjtS in (1)) and firm size in 1988, and can be thought of as a plot of the first stage of (2).14 The Figure shows that firms with 15 or fewer employees in 1988 are more likely to have fewer than 15 employees in the following years of the sample 1989–93 (the average probability of being below the threshold in 1989–93 across firms between 5 and 15 employees in 1988 is 0.65), while firms above 15 employees in 1988 are more likely to stay larger than 15 in the following years (the average probability of being below the threshold in 1989–93 across firms between 16 and 25 employees in 1988 is less than 0.1). Fig. 2. Open in new tabDownload slide Fraction of Small Firms Notes. The dots represent the probability of being a firm below the 15‐employee threshold in the period 1989–93 averaged by firm size in 1988. The solid line is a fitted regression of the small‐firm dummy on a third‐degree polynomial in the pre‐reform firm size, performed separately on either side of the threshold. Fig. 2. Open in new tabDownload slide Fraction of Small Firms Notes. The dots represent the probability of being a firm below the 15‐employee threshold in the period 1989–93 averaged by firm size in 1988. The solid line is a fitted regression of the small‐firm dummy on a third‐degree polynomial in the pre‐reform firm size, performed separately on either side of the threshold. While there are transitions across the threshold in both directions, Table A1 (Appendix A.1) shows that these transitions are not abnormal in years around 1990. As expected, Figure Figure Fig. 2.. also shows that small firms below the 15‐employee threshold in 1988 are more likely to grow in the following years (1 minus the probability of being small in 1989–93) than are large firms in 1988 to shrink. Overall, Figure Figure Fig. 2.. shows that past firm size does predict current firm size and is in this sense a good instrument. In addition, as discussed in subsection 1.2., the reform was largely unanticipated and was hastily introduced so it is highly unlikely that firms in 1988 and 1987 were determining their size in view of the new regulations, thus allowing us to control for the sorting due to the reform itself. Of course, the validity of the IV estimates rest on the (untestable) assumption that the instruments satisfy the exclusion restrictions, that is, that they do not directly affect wages. 3.3. Worker Sorting Identification of (1) may be also threatened by workers non‐randomly sorting in firms around the 15‐employee threshold and choosing their own EPL regime by selecting the size of the firm they work for. Sorting may bias our results as long the selection process is driven by worker characteristics that we are not able to control for. Suppose, for example, that low‐productivity workers disproportionately apply to (and are subsequently hired in) more protected jobs. In this case, a negative association between wages and job protection cannot be interpreted as the causal effect of EPL on wages, because it rather reflects the different composition of the pool of workers in protected and non‐protected jobs. We run two different tests of workers’ sorting and we show the results in Appendix A.2. We first check whether firms’ observable characteristics, such as industry, age and occupation (white collar/blue collar) composition of the workforce are balanced in the neighbourhood of the 15 employees threshold in the post‐relative to the pre‐reform period. If non‐random worker sorting were to occur, we would expect these characteristics to differ systematically between treated and untreated firms in the post‐relative to the pre‐reform period. Results in Table A2 (Appendix A.2) illustrate that no pre‐treatment characteristics show a significant discontinuity at the 15‐employee threshold after the reform in the third‐degree polynomial specification. A few covariates pop up as significantly different from zero in the second‐degree polynomial specification but the spotty nature of these gaps and the fact that their significance differs according to the polynomial used supports the notion that our controlled comparisons to the left and right of the 15‐employee threshold before and after the reform are indeed a good experiment.15 Second, we run regressions of the probability of workers moving to a firm above or below the threshold on a number of determinants that include a small‐firm dummy interacted with year dummies. Results in Table A3 (Appendix A.2) show some evidence of sorting, as the probability of moving to firms larger than 15 employees coming from a firm below the threshold decreases after the reform. However, reassuringly, the same Table also shows that this effect is apparently not driven by workers’ attributes correlated with their productivity, as measured by the time‐invariant component of the individual’s average pre‐reform wage. Because we cannot rule out entirely the possibility of non‐random sorting of workers, the next section will show results including worker fixed effects and match fixed effects. This helps addressing the concern that workers select their most preferred EPL regime to the extent that it controls for all time‐invariant unobservable worker and match‐specific attributes that affect workers’ behaviour. Of course, workers and match effects do not allow us to control for the time‐varying factors that affect workers’ self‐selection. 4. Results Before turning to the estimates, we provide a visual summary of the relationship between firm size and wages around the threshold. Figure Figure Fig. 3.. draws a scatter plot of the difference between post‐reform log wages (averaged over the years 1991 to 1993) and pre‐reform log wages (year 1989) against firm size in 1988 for firms in the ±10 window around the 15‐employee threshold. Wages are measured at the firm level averaging individual wages by firm size in 1988 separately for the pre and post‐reform period. The figure also reports the fitted values of a regression of log wage differences on firm size in 1988. As firm size is measured in 1988 to minimise endogeneity issues, the picture can be thought of as representing the reduced form of the IV specification (with the same caveat as in footnote 14). Figure Figure Fig. 3.. shows a positive jump in the difference between post‐ and pre‐reform log wages at the 15‐employee threshold, meaning that in the neighbourhood of the threshold wages in small firms decrease after 1990 relative to wages in large firms. The jump appears to be small but significant, suggesting that small firms translate part of the increased cost of EPL onto lower wages. Fig. 3. Open in new tabDownload slide Post Minus Pre‐reform Wages Notes. Wages are measured at the firm level averaging individual wages by firm size in 1988. The dots are the observed differences between log wages post‐reform (averaged in years 1991, 1992 and 1993) minus log wages pre‐reform in the year 1989. The solid line is a fitted regression of log wage differences on firm size in 1988, performed separately on either side of the threshold. Fig. 3. Open in new tabDownload slide Post Minus Pre‐reform Wages Notes. Wages are measured at the firm level averaging individual wages by firm size in 1988. The dots are the observed differences between log wages post‐reform (averaged in years 1991, 1992 and 1993) minus log wages pre‐reform in the year 1989. The solid line is a fitted regression of log wage differences on firm size in 1988, performed separately on either side of the threshold. The general pattern presented in Figure Figure Fig. 3.. is also borne out in the regression results to which we now turn. Differently from the Figures, the regressions are run on individual wages and allow us to control for both workers’ and firms’ characteristics. Table 2 reports regression results from the estimation of (1). In panel (a), the year of the reform, 1990, is excluded. For the sake of space, we only show the coefficient of interest on the interaction term between the small‐firm dummy and the post‐reform dummy. Results in column 1 of panel (a) include worker fixed effects and suggest that individuals employed in firms just below the threshold of 15 employees are paid 0.4% less than workers in firms immediately above the cut‐off after 1990. Columns 2 and 3 show that the result does not survive the inclusion of firm and match effects respectively. The smaller effects found in the firm and match effects regressions, which absorb the cross‐firm and cross‐match variability, suggest that most of the action comes from workers moving across firms. Section 5. will further explore this possibility. Table 2. Average Effects of 1990 EPL Reform . (1) . (2) . (3) . (4) . Panel (a): Excluding the reform year 1990 Small firm × Post 1990 −0.004** −0.002 −0.001 −0.011*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Including the reform year 1990 Small firm × Post 1990 −0.005*** −0.003** −0.002 −0.009*** (0.001) (0.001) (0.001) (0.002) Observations 120,652 120,652 120,652 99,658 R2 0.15 0.22 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Panel (a): Excluding the reform year 1990 Small firm × Post 1990 −0.004** −0.002 −0.001 −0.011*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Including the reform year 1990 Small firm × Post 1990 −0.005*** −0.003** −0.002 −0.009*** (0.001) (0.001) (0.001) (0.002) Observations 120,652 120,652 120,652 99,658 R2 0.15 0.22 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue collar dummy. First‐stage results of the IV specification in panel (a) are shown in Table B1. First‐stage statistics of the IV specification in panel (b) are shown in Table B2. ** Significance at 5% and *** Significance at 1%. Open in new tab Table 2. Average Effects of 1990 EPL Reform . (1) . (2) . (3) . (4) . Panel (a): Excluding the reform year 1990 Small firm × Post 1990 −0.004** −0.002 −0.001 −0.011*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Including the reform year 1990 Small firm × Post 1990 −0.005*** −0.003** −0.002 −0.009*** (0.001) (0.001) (0.001) (0.002) Observations 120,652 120,652 120,652 99,658 R2 0.15 0.22 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Panel (a): Excluding the reform year 1990 Small firm × Post 1990 −0.004** −0.002 −0.001 −0.011*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Including the reform year 1990 Small firm × Post 1990 −0.005*** −0.003** −0.002 −0.009*** (0.001) (0.001) (0.001) (0.002) Observations 120,652 120,652 120,652 99,658 R2 0.15 0.22 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue collar dummy. First‐stage results of the IV specification in panel (a) are shown in Table B1. First‐stage statistics of the IV specification in panel (b) are shown in Table B2. ** Significance at 5% and *** Significance at 1%. Open in new tab Finally, column 4 refers to IV (with worker fixed‐effects) estimates in which we instrument the treatment status using firm size in 1987 and 1988. This is our preferred specification because it controls both for the sorting of workers due to time‐invariant characteristics and for the sorting of firms due to time‐varying factors, including the reform itself. The IV estimates deliver a negative and significant coefficient more than twice as large as the baseline coefficients in column 1. The larger magnitude of the IV coefficient may be due to measurement error in firm size that produces an attenuation bias in non‐instrumented regressions. An alternative interpretation is that the larger size of the IV coefficients confirms the importance of instrumenting to account for the sorting of firms according to unobservable characteristics. In particular, it may suggest that the reform may have induced some firms to cross the threshold, reducing the gap in average wages observed in the treated and control groups after 1990. This can happen, for example, if the reform provided greater incentives to low‐productivity firms – that before the reform were keeping their size below the 15‐employee threshold to avoid strict EPL rules – to move above the threshold. The estimates from the first stage of the IV model are presented and discussed in Appendix B. In panel (b), year 1990 is included as a pre‐reform year (the reform passed in July and wages are unlikely to adjust immediately). It shows that the inclusion of 1990 reinforces the results, as the coefficient of interest is negative and significant in all specifications except for the one with match effects. To be conservative, in what follows, we exclude year 1990.16 Table 3 reports regression results from the estimation of (2), in which we exploit the idea that EPL should matter more in highly volatile sectors (Micco and Pagés, 2006). We measure employment volatility as the pre‐reform within‐sector standard deviation of the firm‐level growth rate of employment computed separately for firms below and above the threshold. Results confirm that the reform bites more in more volatile sectors, thus suggesting that results are not driven by small‐firm wages being on a declining path with respect to wages in larger firms above the 15‐employee threshold. This is also reassuring as it suggests that we are capturing the effect of the 1990 reform rather than the effect of some other contemporaneous shock or legislative change, such as the pension reform or the elimination of the Scala Mobile (see subsection 1.2.), which should not have affected differently sectors with different volatilities. Table 3. Differential Effects of the 1990 Reform by Sectoral Employment Volatility . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004** −0.002 −0.001 −0.008** (0.002) (0.002) (0.002) (0.004) Pre‐reform standard deviation of employment growth −0.009*** −0.009*** −0.005** −0.013 (0.002) (0.003) (0.002) (0.009) Standard deviation of employment growth × Post 1990 0.010*** 0.010*** 0.009*** 0.011*** (0.002) (0.002) (0.001) (0.003) Standard deviation of employment growth × Small firm 0.013*** 0.014*** 0.012*** 0.014 (0.003) (0.004) (0.003) (0.019) Standard deviation of employment growth × Small firm × Post 1990 −0.012*** −0.014*** −0.012*** −0.012*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Worker FE Yes No No Yes Firm FE No Yes No No Match effects No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004** −0.002 −0.001 −0.008** (0.002) (0.002) (0.002) (0.004) Pre‐reform standard deviation of employment growth −0.009*** −0.009*** −0.005** −0.013 (0.002) (0.003) (0.002) (0.009) Standard deviation of employment growth × Post 1990 0.010*** 0.010*** 0.009*** 0.011*** (0.002) (0.002) (0.001) (0.003) Standard deviation of employment growth × Small firm 0.013*** 0.014*** 0.012*** 0.014 (0.003) (0.004) (0.003) (0.019) Standard deviation of employment growth × Small firm × Post 1990 −0.012*** −0.014*** −0.012*** −0.012*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Worker FE Yes No No Yes Firm FE No Yes No No Match effects No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. The standard deviation of firm‐level employment growth (standardised to zero mean and unit variance) is computed in the pre‐reform period within each sector separately for small and large firms. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. IV first‐stage statistics are shown in Table B2. ** Significance at 5% and *** Significance at 1%. Open in new tab Table 3. Differential Effects of the 1990 Reform by Sectoral Employment Volatility . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004** −0.002 −0.001 −0.008** (0.002) (0.002) (0.002) (0.004) Pre‐reform standard deviation of employment growth −0.009*** −0.009*** −0.005** −0.013 (0.002) (0.003) (0.002) (0.009) Standard deviation of employment growth × Post 1990 0.010*** 0.010*** 0.009*** 0.011*** (0.002) (0.002) (0.001) (0.003) Standard deviation of employment growth × Small firm 0.013*** 0.014*** 0.012*** 0.014 (0.003) (0.004) (0.003) (0.019) Standard deviation of employment growth × Small firm × Post 1990 −0.012*** −0.014*** −0.012*** −0.012*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Worker FE Yes No No Yes Firm FE No Yes No No Match effects No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004** −0.002 −0.001 −0.008** (0.002) (0.002) (0.002) (0.004) Pre‐reform standard deviation of employment growth −0.009*** −0.009*** −0.005** −0.013 (0.002) (0.003) (0.002) (0.009) Standard deviation of employment growth × Post 1990 0.010*** 0.010*** 0.009*** 0.011*** (0.002) (0.002) (0.001) (0.003) Standard deviation of employment growth × Small firm 0.013*** 0.014*** 0.012*** 0.014 (0.003) (0.004) (0.003) (0.019) Standard deviation of employment growth × Small firm × Post 1990 −0.012*** −0.014*** −0.012*** −0.012*** (0.002) (0.002) (0.002) (0.004) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Worker FE Yes No No Yes Firm FE No Yes No No Match effects No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. The standard deviation of firm‐level employment growth (standardised to zero mean and unit variance) is computed in the pre‐reform period within each sector separately for small and large firms. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. IV first‐stage statistics are shown in Table B2. ** Significance at 5% and *** Significance at 1%. Open in new tab Extensive robustness checks (with respect to the time span of the sample, the specification of the polynomial in firm size and the size of the bandwidth around the threshold) and placebo tests (fake firm size thresholds and fake reform years) in Appendix C confirm the presence of a robust, negative and generally significant (albeit small) causal effect of the EPL reform on wages. To have a sense of the economic magnitude of the effect, in the concluding section we will assess the extent of the translation of the EPL cost onto wages. Before turning to that, we provide several pieces of evidence that the wage effects of the EPL reform are heterogeneous and depend on the bargaining position of workers. 5. Heterogeneous Effects 5.1. Impact at Entry The theoretical considerations of subsection 1.1. suggest that newly hired workers should be in a weaker bargaining position compared with incumbent workers because firms do not pay severance if there is no agreement on the wage at the first encounter. On the contrary, higher EPL should strengthen incumbent workers’ bargaining position and possibly lead to a wage increase if workers are able to renegotiate their wages. In what follows, we investigate the differential impact of the reform on new entrants’ and incumbents’ wages and (for new entrants only) we distinguish the effect on the entry and post‐entry wages. To this end, we identify the subsample of incumbent workers, which consists of all workers who stayed in the same firm over the sample period, and the complementary subsample of movers, which includes all workers who changed firm at least once over the same period. Obviously, we observe the entry wage only in the sample of movers. Descriptive statistics in Table D1 (which includes year 1990 and for this reason displays the same number of observations as panel (b) of Table 2) show that movers are a little less than one‐third of the sample: 35,690 observations of 120,652 (the proportion remains the same once year 1990 is dropped as shown in Table 1). Column 1 shows that the proportion of job changes is stable over the sample period at around 9% per year.17 The wage of incumbent workers is higher than the wage of movers (columns 2 and 3), plausibly because of tenure effects. For the same reason, movers’ entry wages are lower than movers’ post‐entry wages (columns 4 and 5). Before looking at the differential effect of EPL on the wages of new entrants and incumbents using our regression framework, we display movers’ entry wages, that is, the first observed wage of a mover in the new firm, in Figure Figure Fig. 4.., and the wages of incumbents workers in Figure Figure Fig. 5... Individual wages are averaged by firm size in 1988 in both figures. Fig. 5. Open in new tabDownload slide Post Minus Pre‐reform Wages of Incumbent Workers Notes. The sample of incumbents includes only workers who stayed in the same firm between 1989 and 1993. Wages are measured at the firm level averaging individual log wages by firm size in 1988. The dots are the observed differences between log wages post‐reform (averaged in years 1991, 1992 and 1993) minus log wages pre‐reform in year 1989. The solid line is a fitted regression of log wage differences on firm size in 1988, performed separately on either side of the threshold. Fig. 5. Open in new tabDownload slide Post Minus Pre‐reform Wages of Incumbent Workers Notes. The sample of incumbents includes only workers who stayed in the same firm between 1989 and 1993. Wages are measured at the firm level averaging individual log wages by firm size in 1988. The dots are the observed differences between log wages post‐reform (averaged in years 1991, 1992 and 1993) minus log wages pre‐reform in year 1989. The solid line is a fitted regression of log wage differences on firm size in 1988, performed separately on either side of the threshold. Fig. 4. Open in new tabDownload slide Post Minus Pre‐reform Entry Wages Notes. Entry wages are the first observed wage in a new firm for workers who change firms at least once in the period 1989–93. Wages are measured at the firm level averaging individual log entry wages by firm size in 1988. The dots are the observed differences between log entry wages post‐reform (averaged in years 1991, 1992 and 1993) minus log entry wages pre‐reform in year 1989. The solid line is a fitted regression of log entry wage differences on firm size in 1988, performed separately on either side of the threshold. Fig. 4. Open in new tabDownload slide Post Minus Pre‐reform Entry Wages Notes. Entry wages are the first observed wage in a new firm for workers who change firms at least once in the period 1989–93. Wages are measured at the firm level averaging individual log entry wages by firm size in 1988. The dots are the observed differences between log entry wages post‐reform (averaged in years 1991, 1992 and 1993) minus log entry wages pre‐reform in year 1989. The solid line is a fitted regression of log entry wage differences on firm size in 1988, performed separately on either side of the threshold. Figure Figure Fig. 4.. draws a scatter plot of the difference between log entry wages post‐reform (year 1991–3) and log entry wages pre‐reform (year 1989). The significant jump at 15 implies that after the reform entry, wages are lower in firms below the threshold relative to firms above the threshold. On the contrary, the same relationship plotted for the sample of incumbents (Figure Figure Fig. 5..) shows no jump, meaning that there is no difference between the average wages of incumbents paid in firms below and above the threshold before and after the reform. This visual evidence is consistent with the idea that most of the burden imposed by higher firing costs is translated onto lower entry wages, with incumbents’ wages virtually unaffected. In Table 4, we report the regression results from estimation of (1) augmented with a ‘mover’ dummy equal to one if the individual ever changed firm in the sample period, fully interacted with the small‐firm dummy and the post‐reform dummy. The ‘mover’ dummy is a fixed individual characteristic and therefore is not identified when there are worker fixed effects. The regressions show that movers account for the overall effect that we see in the baseline regressions in Table 2. Movers suffer a 2.5% wage loss in firms below the threshold relative to larger firms after the reform in our preferred IV specification with worker fixed effects. Incumbents experience no significant change in their wages (see the insignificant coefficient on ‘Small firm × Post 1990’). This result is consistent with the idea that incumbents are not able to renegotiate their wages, either because no renegotiation round took place in the post‐reform period or because workers have no credible threat if the firm refuses to renegotiate their wages (MacLeod and Malcomson, 1993). Table 4. Effects of the 1990 Reform on Movers and Incumbents . (1) . (2) . (3) . (4) . Small firm × Post 1990 0.001 −0.001 0.001 −0.007 (0.002) (0.002) (0.002) (0.004) Mover dummy – −0.036*** – – – (0.005) – – Mover dummy × Post 1990 0.013*** −0.019*** 0.009* 0.009 (0.005) (0.005) (0.005) (0.008) Mover dummy × Small firm 0.018*** 0.017*** 0.018*** 0.033 (0.006) (0.005) (0.006) (0.021) Mover dummy × Small firm × Post 1990 −0.019*** −0.003 −0.015** −0.025** (0.006) (0.006) (0.006) (0.011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.23 0.17 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Small firm × Post 1990 0.001 −0.001 0.001 −0.007 (0.002) (0.002) (0.002) (0.004) Mover dummy – −0.036*** – – – (0.005) – – Mover dummy × Post 1990 0.013*** −0.019*** 0.009* 0.009 (0.005) (0.005) (0.005) (0.008) Mover dummy × Small firm 0.018*** 0.017*** 0.018*** 0.033 (0.006) (0.005) (0.006) (0.021) Mover dummy × Small firm × Post 1990 −0.019*** −0.003 −0.015** −0.025** (0.006) (0.006) (0.006) (0.011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.23 0.17 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. Movers are defined as workers who change firm at least once over the period 1989–93. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. IV first‐stage statistics are shown in Table B2. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab Table 4. Effects of the 1990 Reform on Movers and Incumbents . (1) . (2) . (3) . (4) . Small firm × Post 1990 0.001 −0.001 0.001 −0.007 (0.002) (0.002) (0.002) (0.004) Mover dummy – −0.036*** – – – (0.005) – – Mover dummy × Post 1990 0.013*** −0.019*** 0.009* 0.009 (0.005) (0.005) (0.005) (0.008) Mover dummy × Small firm 0.018*** 0.017*** 0.018*** 0.033 (0.006) (0.005) (0.006) (0.021) Mover dummy × Small firm × Post 1990 −0.019*** −0.003 −0.015** −0.025** (0.006) (0.006) (0.006) (0.011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.23 0.17 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Small firm × Post 1990 0.001 −0.001 0.001 −0.007 (0.002) (0.002) (0.002) (0.004) Mover dummy – −0.036*** – – – (0.005) – – Mover dummy × Post 1990 0.013*** −0.019*** 0.009* 0.009 (0.005) (0.005) (0.005) (0.008) Mover dummy × Small firm 0.018*** 0.017*** 0.018*** 0.033 (0.006) (0.005) (0.006) (0.021) Mover dummy × Small firm × Post 1990 −0.019*** −0.003 −0.015** −0.025** (0.006) (0.006) (0.006) (0.011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.23 0.17 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. Movers are defined as workers who change firm at least once over the period 1989–93. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. IV first‐stage statistics are shown in Table B2. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab We next restrict the analysis to the subsample of movers (notice the lower number of observations in Table 5) to analyse whether the EPL reform impacts movers’ wages at entry or afterwards. To do so, we augment our baseline specification in (1) with an entry wage dummy and all relevant interactions. We also add a pre‐entry dummy (a dummy equal to one for the observations prior to the first job change observed) fully interacted with the small‐firm dummy and the post‐reform dummy to be able to interpret the interaction between the small‐firm dummy and the post‐reform dummy as the effect on the post‐entry wages. Table 5 shows that movers experience a wage decline at entry and, consistent with the results on incumbents, no changes in the post‐entry period. The decline at entry is a sizeable 6.3% in our preferred specification. As discussed in Section 4., the IV results are always larger probably signalling either mismeasurement of firm size or sorting of low‐productivity firms above the threshold. This result suggests that workers paid for the introduction of EPL with a lower entry wage and were unable to renegotiate their wages upwards in later years. Table 5. Effects of the 1990 Reform on Movers Entry and Post‐entry Wages . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004 −0.015 0.005 0.002 (0.012) (0.010) (0.012) (0.021) Entry dummy −0.042** −0.037*** −0.053*** −0.064** (0.016) (0.013) (0.016) (0.025) Entry dummy × Post 1990 0.034** 0.026* 0.052*** 0.054** (0.017) (0.013) (0.016) (0.027) Entry dummy × Small firm 0.036* 0.000 0.051*** 0.064** (0.019) (0.016) (0.019) (0.030) Entry dummy × Small firm × Post 1990 −0.034* 0.001 −0.048** −0.063* (0.020) (0.016) (0.019) (0.033) Observations 28,451 28,451 28,451 16,140 R2 0.13 0.17 0.11 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004 −0.015 0.005 0.002 (0.012) (0.010) (0.012) (0.021) Entry dummy −0.042** −0.037*** −0.053*** −0.064** (0.016) (0.013) (0.016) (0.025) Entry dummy × Post 1990 0.034** 0.026* 0.052*** 0.054** (0.017) (0.013) (0.016) (0.027) Entry dummy × Small firm 0.036* 0.000 0.051*** 0.064** (0.019) (0.016) (0.019) (0.030) Entry dummy × Small firm × Post 1990 −0.034* 0.001 −0.048** −0.063* (0.020) (0.016) (0.019) (0.033) Observations 28,451 28,451 28,451 16,140 R2 0.13 0.17 0.11 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. The sample includes only movers. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies, a blue‐collar dummy and a pre‐entry dummy (a dummy equal to one for the observations prior to first job change observed) and all interactions. IV first‐stage statistics are shown in Table B2. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab Table 5. Effects of the 1990 Reform on Movers Entry and Post‐entry Wages . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004 −0.015 0.005 0.002 (0.012) (0.010) (0.012) (0.021) Entry dummy −0.042** −0.037*** −0.053*** −0.064** (0.016) (0.013) (0.016) (0.025) Entry dummy × Post 1990 0.034** 0.026* 0.052*** 0.054** (0.017) (0.013) (0.016) (0.027) Entry dummy × Small firm 0.036* 0.000 0.051*** 0.064** (0.019) (0.016) (0.019) (0.030) Entry dummy × Small firm × Post 1990 −0.034* 0.001 −0.048** −0.063* (0.020) (0.016) (0.019) (0.033) Observations 28,451 28,451 28,451 16,140 R2 0.13 0.17 0.11 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Small firm × Post 1990 −0.004 −0.015 0.005 0.002 (0.012) (0.010) (0.012) (0.021) Entry dummy −0.042** −0.037*** −0.053*** −0.064** (0.016) (0.013) (0.016) (0.025) Entry dummy × Post 1990 0.034** 0.026* 0.052*** 0.054** (0.017) (0.013) (0.016) (0.027) Entry dummy × Small firm 0.036* 0.000 0.051*** 0.064** (0.019) (0.016) (0.019) (0.030) Entry dummy × Small firm × Post 1990 −0.034* 0.001 −0.048** −0.063* (0.020) (0.016) (0.019) (0.033) Observations 28,451 28,451 28,451 16,140 R2 0.13 0.17 0.11 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. The sample includes only movers. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies, a blue‐collar dummy and a pre‐entry dummy (a dummy equal to one for the observations prior to first job change observed) and all interactions. IV first‐stage statistics are shown in Table B2. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab 5.2. Occupation and Age The bargaining power of workers may differ not only across insiders and outsiders. There are other possible dimensions that relate to the individual characteristics along which the bargaining power may be heterogeneous. In what follows, we cut our data set into high (white collar, old) and low‐bargaining power subsamples (blue collar, young). Table 6 reports regression results from the estimation of a version of (2) in which the triple interaction term identifies the differential effect of the reform on the above‐mentioned subgroups. Panel (a) looks at blue collar and finds no significant difference relative to white collars. In panel (b), we find a significant negative effect for young workers aged less than 30, both in the specification with worker fixed effects and in the IV specification with worker fixed effects. Finally, the subgroup of young blue collars in panel (c) displays significant negative effects in all specifications except for the one with match effects. Table 6. Heterogeneous Wage Effects of the 1990 EPL Reform . (1) . (2) . (3) . (4) . Panel (a): Blue/white collar Small firm × Post 1990 0.002 0.004 0.005 0.000 (0.006) (0.006) (0.005) (0.010) Blue collar × Small firm × Post 1990 −0.006 −0.006 −0.006 −0.012 (0.006) (0.007) (0.006) (0.0011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Young (<30)/old (>40) Small firm × Post 1990 0.002 0.002 0.002 −0.009 (0.003) (0.003) (0.003) (0.007) Young × Small firm × Post 1990 −0.012** −0.002 −0.008 −0.020* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.23 0.16 Panel (c): Young blue collar Small firm × Post 1990 0.002 0.005 0.002 −0.008 (0.003) (0.003) (0.003) (0.007) Young blue collar × Small firm × Post 1990 −0.013** −0.009* −0.008 −0.021* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.26 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Panel (a): Blue/white collar Small firm × Post 1990 0.002 0.004 0.005 0.000 (0.006) (0.006) (0.005) (0.010) Blue collar × Small firm × Post 1990 −0.006 −0.006 −0.006 −0.012 (0.006) (0.007) (0.006) (0.0011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Young (<30)/old (>40) Small firm × Post 1990 0.002 0.002 0.002 −0.009 (0.003) (0.003) (0.003) (0.007) Young × Small firm × Post 1990 −0.012** −0.002 −0.008 −0.020* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.23 0.16 Panel (c): Young blue collar Small firm × Post 1990 0.002 0.005 0.002 −0.008 (0.003) (0.003) (0.003) (0.007) Young blue collar × Small firm × Post 1990 −0.013** −0.009* −0.008 −0.021* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.26 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. Young workers are defined as under the age of 30 and old workers over the age of 40. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. IV first‐stage statistics are shown in Table B2. * Significance at 10% and ** Significance at 5%. Open in new tab Table 6. Heterogeneous Wage Effects of the 1990 EPL Reform . (1) . (2) . (3) . (4) . Panel (a): Blue/white collar Small firm × Post 1990 0.002 0.004 0.005 0.000 (0.006) (0.006) (0.005) (0.010) Blue collar × Small firm × Post 1990 −0.006 −0.006 −0.006 −0.012 (0.006) (0.007) (0.006) (0.0011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Young (<30)/old (>40) Small firm × Post 1990 0.002 0.002 0.002 −0.009 (0.003) (0.003) (0.003) (0.007) Young × Small firm × Post 1990 −0.012** −0.002 −0.008 −0.020* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.23 0.16 Panel (c): Young blue collar Small firm × Post 1990 0.002 0.005 0.002 −0.008 (0.003) (0.003) (0.003) (0.007) Young blue collar × Small firm × Post 1990 −0.013** −0.009* −0.008 −0.021* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.26 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes . (1) . (2) . (3) . (4) . Panel (a): Blue/white collar Small firm × Post 1990 0.002 0.004 0.005 0.000 (0.006) (0.006) (0.005) (0.010) Blue collar × Small firm × Post 1990 −0.006 −0.006 −0.006 −0.012 (0.006) (0.007) (0.006) (0.0011) Observations 96,333 96,333 96,333 76,814 R2 0.16 0.22 0.17 Panel (b): Young (<30)/old (>40) Small firm × Post 1990 0.002 0.002 0.002 −0.009 (0.003) (0.003) (0.003) (0.007) Young × Small firm × Post 1990 −0.012** −0.002 −0.008 −0.020* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.23 0.16 Panel (c): Young blue collar Small firm × Post 1990 0.002 0.005 0.002 −0.008 (0.003) (0.003) (0.003) (0.007) Young blue collar × Small firm × Post 1990 −0.013** −0.009* −0.008 −0.021* (0.005) (0.005) (0.005) (0.011) Observations 61,899 61,899 61,899 46,622 R2 0.15 0.26 0.16 Worker effect Yes No No Yes Firm effect No Yes No No Match effect No No Yes No IV No No No Yes Notes. Robust standard errors clustered by individual in parentheses. Young workers are defined as under the age of 30 and old workers over the age of 40. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. IV first‐stage statistics are shown in Table B2. * Significance at 10% and ** Significance at 5%. Open in new tab These results fit the interpretation that the negative wage effects of EPL are inversely related to the bargaining power of workers, indirectly measured with workers’ observable characteristics. We investigate further this issue moving to a subsample of workers for which we have a more direct measure of bargaining power, namely the individual wage premium over the contractual minimum wage. 5.3. Contractual Minimum Wages and Quantile Regression Similarly to many other European countries, Italy has a system of contractual minimum wages bargained every 2 years (with many delays and exceptions) at the industry level, which extends also to non‐signatory workers. Employers can negotiate supplemental wage premiums over and above the contractual minimum wage at the firm level and employees also receive individual premiums and bonuses. In this Section we exploit information on contractual minimum wages to construct a measure of the ‘wage drift’, that is, the difference between the actual wage and the contractual minimum. The contractual minimum wages are defined by industry and occupation category (typically five or more categories according to tasks performed and tenure). Thus, the wage drift in percentage terms is yijzt=(wijt−wjztmin)/wjztmin where wjztmin is the contractual minimum in sector j for a worker of occupation category z. Our data allow us to identify the wage drift only for a subsample of workers. The matching of each worker to her contractual minimum has a cost in terms of observations due to missing information either on the sectoral contract itself (e.g. we miss information on contracts in the chemical industry and in industries covered by narrow sectoral agreements) or on the occupation category of the worker. We can match only around 40% of the observations present in the benchmark sample to their respective contractual minimum wages. We have information on contractual minima in 21 types of contracts in Table D2.18 Notice that collective contracts do not correspond exactly to sectors but also vary within sectors according to firm size and type of firm. The distribution of the characteristics of the workers (proportion of white‐collar workers, average age and wages) in the resulting subsample (13.7%, 38.7 years and 321.2 euro per week at 1995 prices) is similar to the distribution in the overall estimation sample (14.4%, 36.9 years and 314.29 euro per week). This is suggestive that the loss of observations due to missing information is not endogenous to the variables of interest. Table D2 reports the distribution of the wage drift for all available contracts and shows that there is a wide variation across contracts in the incidence of the contractual minimum as a percentage of the full compensation. The table reports the 5th, 10th, 25th, 50th, 75th, 90th and 95th quantile of the wage drift distribution by each contract. The median wage drift differs by sector and goes from 25.2% in textile artisanal firms to 91.8% in the professional services sector. Notice that even at the 5th percentile, the wage drift is on average a sizeable 12.5%, suggesting that wage minima are hardly binding. As long as individual‐specific premia and firm‐wide premia paid above the minimum are a result of bargaining in local contracts, the wage drift can be interpreted as a measure of bargaining power of the workers: the higher the actual wage with respect to the contractual minimum, the higher the bargaining power of the workers (Card et al., 2010). Following this reasoning, we should expect larger wage cuts for low bargaining‐power workers with small wage premia over the minimum. Of course, wages at (or very close to) the minimum should be insensitive to changes in EPL because of the binding contractual (and legal) floor. To investigate these hypotheses, we run a quantile regression at different points of the distribution using as a dependent variable the wage drift yijzt=(wijt−wjztmin)/wjztmin ⁠. For completeness, we also estimate quantile regressions on log wages. Let Qθ(yijzt|Xijt) for θ ∈ (0,1) denote the θth quantile of the distribution of yijzt conditional on individual and firm characteristics included in the matrix Xijt (same controls as in (1)). The model of the conditional quantile is: Qθ(yijzt|Xijt)=βθ’Xijt+δ1θDjtS+δ2θ(DjtS×Post)+∑k=13(γθkfsizejtk).(3) Bootstrapped standard errors are obtained from individual resampling. Table 7 reports the estimates of the coefficient of the interaction term δ2θ obtained at the 5th, 10th, 25th, 50th, 75th, 90th and 95th quantile of the log wage and of the wage drift distributions. Panel (a) shows the results on log wages in the benchmark period 1989–93, panel (b) on the wage drift as defined above in the same sample period. Results show that the negative effect of the reform on the log wages of workers of firms below the 15‐employee threshold is stronger at the bottom of the distribution and weaker at the top.19 Panel (b) exhibits an even stronger pattern using the wage drift as a dependent variable. In particular, the effect at the 5th percentile of the wage drift distribution is more than five times larger than the effect at the 90th of the distribution. These results are in accordance with the interpretation that firms were able to translate the increased EPL costs onto workers with low bargaining power. The fact that we find a strong effect also on wages very close to the minimum (the 5th percentile of the wage drift) is explained by the fact that even at the 5th percentile, as remarked above, there is room for adjustment. Table 7. Heterogeneous Wage Effects of 1990 EPL Reform: Quantile Regression . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Log wages Small firm × Post 1990 −0.014*** −0.009** −0.009*** −0.009*** −0.010*** −0.008 −0.011 (0.006) (0.004) (0.003) (0.003) (0.004) (0.007) (0.008) Observations 96,333 96,333 96,333 96,333 96,333 96,333 96,333 Wage drift Small firm × Post 1990 −0.032*** −0.025*** −0.021*** −0.009 −0.010 −0.006 −0.020 (0.010) (0.008) (0.006) (0.007) (0.011) (0.018) (0.024) Observations 38,895 38,895 38,895 38,895 38,895 38,895 38,895 . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Log wages Small firm × Post 1990 −0.014*** −0.009** −0.009*** −0.009*** −0.010*** −0.008 −0.011 (0.006) (0.004) (0.003) (0.003) (0.004) (0.007) (0.008) Observations 96,333 96,333 96,333 96,333 96,333 96,333 96,333 Wage drift Small firm × Post 1990 −0.032*** −0.025*** −0.021*** −0.009 −0.010 −0.006 −0.020 (0.010) (0.008) (0.006) (0.007) (0.011) (0.018) (0.024) Observations 38,895 38,895 38,895 38,895 38,895 38,895 38,895 Notes. Bootstrapped standard errors (100 replications) clustered by individual. The wage drift is defined as (wage‐contractual wage)/contractual wage. Contractual wages are bargained at the national level by sector and occupation category (typically 5 or more categories according to tasks performed and tenure). All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. ** Significance at 5% and *** Significance at 1%. Open in new tab Table 7. Heterogeneous Wage Effects of 1990 EPL Reform: Quantile Regression . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Log wages Small firm × Post 1990 −0.014*** −0.009** −0.009*** −0.009*** −0.010*** −0.008 −0.011 (0.006) (0.004) (0.003) (0.003) (0.004) (0.007) (0.008) Observations 96,333 96,333 96,333 96,333 96,333 96,333 96,333 Wage drift Small firm × Post 1990 −0.032*** −0.025*** −0.021*** −0.009 −0.010 −0.006 −0.020 (0.010) (0.008) (0.006) (0.007) (0.011) (0.018) (0.024) Observations 38,895 38,895 38,895 38,895 38,895 38,895 38,895 . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Log wages Small firm × Post 1990 −0.014*** −0.009** −0.009*** −0.009*** −0.010*** −0.008 −0.011 (0.006) (0.004) (0.003) (0.003) (0.004) (0.007) (0.008) Observations 96,333 96,333 96,333 96,333 96,333 96,333 96,333 Wage drift Small firm × Post 1990 −0.032*** −0.025*** −0.021*** −0.009 −0.010 −0.006 −0.020 (0.010) (0.008) (0.006) (0.007) (0.011) (0.018) (0.024) Observations 38,895 38,895 38,895 38,895 38,895 38,895 38,895 Notes. Bootstrapped standard errors (100 replications) clustered by individual. The wage drift is defined as (wage‐contractual wage)/contractual wage. Contractual wages are bargained at the national level by sector and occupation category (typically 5 or more categories according to tasks performed and tenure). All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. ** Significance at 5% and *** Significance at 1%. Open in new tab 5.4. Local Labour Markets According to models with labour market frictions, the tightness of the local labour market affects workers’ outside option and eventually their wages. As a final exercise, we therefore test whether the effect of the reform differs across local labour markets. To do so, we exploit a sample of workers which covers the whole of Italy. The data set is drawn from the same administrative source as our VWH data set, namely the Italian Social Security Administration (INPS) archives. The original data are a 1/90 random sample from the stock of employed workers and includes all workers born on the 10th of March, June, September and December of every year. We use a 10% random draw from this orginal data set, as in Kugler and Pica (2006, 2008). Contrary to our main sample, it is a representative sample of workers and not of firms, therefore we cannot use IVs because we do not necessarily follow firms over time. Thus, we only show results using worker, firm and match effects. Before moving to regression results, Table D3 compares the main characteristics of males aged 20–55 in the Italian sample and in the VWH sample. It shows that the average characteristics of workers in the two data sets are similar, except for a higher shares of white‐collar workers in the Italian sample (20% against 14%), due to the fact that Veneto is a predominantly manufacturing region. In particular, in 1990 the Veneto region has the same average wage as the national average (columns 1 and 2). Columns 1 and 3 of Table D3 show that figures for the Veneto region from the two data sources compare fairly well. As a measure of regional labour market tightness, we use the (standardised) annual regional employment rate of males aged 25–64 across 20 Italian regions. Employment rates, rather than unemployment rates, are a better measure of local labour market tightness because of the wide variation in labour force participation across regions in Italy. In 1989–93, the average employment rate among prime age men (aged 25–64) in Italy is 80.22% with a standard deviation of 2.88. Table 8 shows results from worker, firm and match‐effect models (as explained above we cannot use IVs) augmented with the average regional employment rate fully interacted with the small‐firm dummy and the post‐reform dummy. We also control for regional fixed effects and region‐specific trends to capture systematic trends in region‐specific wage pressure. As for the estimates on the VWH sample, along with the baseline estimates, we report a number of robustness tests. Panel (a) focuses on a ±10 window around the 15‐employee threshold, while panel (b) moves closer to the threshold to a ±5 window. Columns (1)–(3) refer to the 1989–93 period, columns (4)–(6) to the 1987–94 period and columns (7)–(9) to the 1986–95 period. Table 8. Heterogeneous Wage Effects of 1990 EPL Reform: Local Labour Markets . 1989–93 . 1987–94 . 1986–95 . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . Panel (a): Firm size 5–25 Small firm × Post 1990 −0.008 −0.008 −0.010 −0.020** −0.012 −0.017** −0.021** −0.013 −0.018** (0.011) (0.010) (0.011) (0.009) (0.008) (0.008) (0.008) (0.008) (0.007) Employment rate × Small firm × Post 1990 −0.004 0.019 0.019 0.013 0.017 0.019* 0.026* 0.017 0.020** (0.013) (0.017) (0.017) (0.011) (0.011) (0.010) (0.013) (0.011) (0.009) Observations 7,323 7,323 7,323 12,894 12,894 12,894 16,637 16,637 16,637 R2 0.55 0.61 0.63 0.63 0.67 0.68 0.66 0.69 0.71 Panel (b): Firm size 10−20 Small firm × Post 1990 −0.009 −0.011 −0.015 −0.017* −0.019** −0.023*** −0.015* −0.017* −0.022** (0.011) (0.012) (0.011) (0.008) (0.007) (0.007) (0.008) (0.009) (0.009) Employment rate × Small firm × Post 1990 0.028* 0.035** 0.036** 0.036** 0.043*** 0.047*** 0.040** 0.037*** 0.038*** (0.016) (0.015) (0.014) (0.013) (0.010) (0.010) (0.016) (0.011) (0.011) Observations 3,727 3,727 3,727 6,502 6,502 6,502 8,362 8,362 8,362 R2 0.63 0.64 0.64 0.67 0.68 0.70 0.70 0.70 0.72 Worker effect Yes No No Yes No No Yes No No Firm effect No Yes No No Yes No No Yes No Match effect No No Yes No No Yes No No Yes . 1989–93 . 1987–94 . 1986–95 . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . Panel (a): Firm size 5–25 Small firm × Post 1990 −0.008 −0.008 −0.010 −0.020** −0.012 −0.017** −0.021** −0.013 −0.018** (0.011) (0.010) (0.011) (0.009) (0.008) (0.008) (0.008) (0.008) (0.007) Employment rate × Small firm × Post 1990 −0.004 0.019 0.019 0.013 0.017 0.019* 0.026* 0.017 0.020** (0.013) (0.017) (0.017) (0.011) (0.011) (0.010) (0.013) (0.011) (0.009) Observations 7,323 7,323 7,323 12,894 12,894 12,894 16,637 16,637 16,637 R2 0.55 0.61 0.63 0.63 0.67 0.68 0.66 0.69 0.71 Panel (b): Firm size 10−20 Small firm × Post 1990 −0.009 −0.011 −0.015 −0.017* −0.019** −0.023*** −0.015* −0.017* −0.022** (0.011) (0.012) (0.011) (0.008) (0.007) (0.007) (0.008) (0.009) (0.009) Employment rate × Small firm × Post 1990 0.028* 0.035** 0.036** 0.036** 0.043*** 0.047*** 0.040** 0.037*** 0.038*** (0.016) (0.015) (0.014) (0.013) (0.010) (0.010) (0.016) (0.011) (0.011) Observations 3,727 3,727 3,727 6,502 6,502 6,502 8,362 8,362 8,362 R2 0.63 0.64 0.64 0.67 0.68 0.70 0.70 0.70 0.72 Worker effect Yes No No Yes No No Yes No No Firm effect No Yes No No Yes No No Yes No Match effect No No Yes No No Yes No No Yes Notes. Robust standard errors clustered by region in parentheses. Estimates are based on a random 10% sample of a data set drawn from the Italian Social Security Administration (INPS) archives. Employment rate is the regional rate of employment of males aged 25–64 (standardised to zero mean and unit variance). All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies, a blue‐collar dummy, the regional employment rate fully interacted with the small‐firm dummy and the post‐reform dummy, regional dummies and regional trends. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab Table 8. Heterogeneous Wage Effects of 1990 EPL Reform: Local Labour Markets . 1989–93 . 1987–94 . 1986–95 . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . Panel (a): Firm size 5–25 Small firm × Post 1990 −0.008 −0.008 −0.010 −0.020** −0.012 −0.017** −0.021** −0.013 −0.018** (0.011) (0.010) (0.011) (0.009) (0.008) (0.008) (0.008) (0.008) (0.007) Employment rate × Small firm × Post 1990 −0.004 0.019 0.019 0.013 0.017 0.019* 0.026* 0.017 0.020** (0.013) (0.017) (0.017) (0.011) (0.011) (0.010) (0.013) (0.011) (0.009) Observations 7,323 7,323 7,323 12,894 12,894 12,894 16,637 16,637 16,637 R2 0.55 0.61 0.63 0.63 0.67 0.68 0.66 0.69 0.71 Panel (b): Firm size 10−20 Small firm × Post 1990 −0.009 −0.011 −0.015 −0.017* −0.019** −0.023*** −0.015* −0.017* −0.022** (0.011) (0.012) (0.011) (0.008) (0.007) (0.007) (0.008) (0.009) (0.009) Employment rate × Small firm × Post 1990 0.028* 0.035** 0.036** 0.036** 0.043*** 0.047*** 0.040** 0.037*** 0.038*** (0.016) (0.015) (0.014) (0.013) (0.010) (0.010) (0.016) (0.011) (0.011) Observations 3,727 3,727 3,727 6,502 6,502 6,502 8,362 8,362 8,362 R2 0.63 0.64 0.64 0.67 0.68 0.70 0.70 0.70 0.72 Worker effect Yes No No Yes No No Yes No No Firm effect No Yes No No Yes No No Yes No Match effect No No Yes No No Yes No No Yes . 1989–93 . 1987–94 . 1986–95 . . (1) . (2) . (3) . (4) . (5) . (6) . (7) . (8) . (9) . Panel (a): Firm size 5–25 Small firm × Post 1990 −0.008 −0.008 −0.010 −0.020** −0.012 −0.017** −0.021** −0.013 −0.018** (0.011) (0.010) (0.011) (0.009) (0.008) (0.008) (0.008) (0.008) (0.007) Employment rate × Small firm × Post 1990 −0.004 0.019 0.019 0.013 0.017 0.019* 0.026* 0.017 0.020** (0.013) (0.017) (0.017) (0.011) (0.011) (0.010) (0.013) (0.011) (0.009) Observations 7,323 7,323 7,323 12,894 12,894 12,894 16,637 16,637 16,637 R2 0.55 0.61 0.63 0.63 0.67 0.68 0.66 0.69 0.71 Panel (b): Firm size 10−20 Small firm × Post 1990 −0.009 −0.011 −0.015 −0.017* −0.019** −0.023*** −0.015* −0.017* −0.022** (0.011) (0.012) (0.011) (0.008) (0.007) (0.007) (0.008) (0.009) (0.009) Employment rate × Small firm × Post 1990 0.028* 0.035** 0.036** 0.036** 0.043*** 0.047*** 0.040** 0.037*** 0.038*** (0.016) (0.015) (0.014) (0.013) (0.010) (0.010) (0.016) (0.011) (0.011) Observations 3,727 3,727 3,727 6,502 6,502 6,502 8,362 8,362 8,362 R2 0.63 0.64 0.64 0.67 0.68 0.70 0.70 0.70 0.72 Worker effect Yes No No Yes No No Yes No No Firm effect No Yes No No Yes No No Yes No Match effect No No Yes No No Yes No No Yes Notes. Robust standard errors clustered by region in parentheses. Estimates are based on a random 10% sample of a data set drawn from the Italian Social Security Administration (INPS) archives. Employment rate is the regional rate of employment of males aged 25–64 (standardised to zero mean and unit variance). All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies, a blue‐collar dummy, the regional employment rate fully interacted with the small‐firm dummy and the post‐reform dummy, regional dummies and regional trends. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab The average wage effect of the reform on the Italian sample (captured by the interaction Small × Post) is negative in all specifications and it is typically larger, although often imprecisely estimated, than the average effects obtained in Table 2 using the same specifications. The coefficient of the triple interaction term, which captures the differential effect of the reform in regions with different employment rates, is positive in all specifications (except one), but it is only sometimes significant in panel (a), where we look at firms in the 5–25 employees range. In panel (b), where we restrict to firms between 10 and 20 employees, the triple interaction term is instead always positive and significant. Moving closer to the threshold, that is, from a ±10 to a ±5 window where firms are presumably more comparable, the estimated effect is also larger in magnitude. This evidence suggests, albeit not forcefully, that workers of firms below the threshold in regions with higher employment rates suffer lower wage losses after 1990. As Veneto is a region with an above‐average labour market tightness, the results in Table 2 can be presumably interpreted as a lower bound. This impression is also reinforced by the fact – remarked above – that the average negative effect of the reform estimated over the whole of Italy in Table 8 is larger, although imprecisely estimated, than the effects obtained on the VWH sample in Table 2 in the same specifications. 6. Discussion and Conclusions This study investigates the effects on wages of an Italian reform, which introduced severance payments for firms with 15 or fewer employees in the case of unfair dismissal, and left larger firms unaffected. On average, we find a small and generally significant negative effect on wages in firms below 15 employees of 1.1% in our preferred specification. These findings complement those in Kugler and Pica (2008) who find a significant reduction in worker flows of around 13–15% induced by the same 1990 reform: we can presume that the substantial effects on worker flows would have been even higher had part of the adjustment not taken place through wages. We document that the effect is highly heterogeneous and argue that such heterogeneity depends on the relative bargaining power of workers versus firms. Consistent with the theoretical predictions of models with labour market frictions and Nash bargaining, we find that the wage effect of EPL is concentrated on the entry wage of newly hired workers who lose up to 6% of their wage upon entry in a small firm after the reform. Furthermore, the negative effect is stronger on young blue‐collar workers, on low‐bargaining power workers at the low end of the wage drift distribution and in regions with low employment rates in which workers have a worse outside option. Results partially diverge from theory on one account: the two‐tier wage model structure à la Mortensen and Pissarides (1999) predicts that higher EPL improves the bargaining position of workers who are already locked in an employment relationship. Differently, we find that the wages of workers already employed when the reform was introduced (who stayed in the same firm afterwards) did not increase after the reform; the same happens to the wages of newly hired workers in the periods following entry in a new firm. These results seem to suggest that workers are not able to renegotiate wages possibly because, if the firm refuses to renegotiate, the workers’ threat point is not credible (MacLeod and Malcomson, 1993). It is important to stress that this empirical exercise – which is local in nature as any RDD – cannot help determining whether any increase in EPL would be (partially) offset by lower wages. However, the Italian EPL reform offers a clean natural experiment and, Veneto being a large and relatively rich region with small‐sized firms not dissimilar to many manufacturing regions in Europe, the estimated effects are unlikely to be peculiar of the area under scrutiny. These results may therefore provide useful insights on the effects of reforms in many countries, which have firm‐level thresholds in the application of EPL. Finally, we use our estimates to try and calculate – albeit roughly – how much of the increase in the firing cost is translated onto lower wages. The Mortensen and Pissarides (1999) model predicts that the wage‐offset of the EPL costs should be total, and pre‐paid at entry. In practice, Lindbeck and Snower (1988) list many reasons why employers may not be able to reduce entry wages by the full extent of the increase in EPL: among them, liquidity constraints, minimum wage laws and social norms. Therefore the extent to which firms can actually translate EPL costs onto lower entry wages is an empirical question. Appendix E produces a back‐of‐the‐envelope calculation, which shows that our results imply that on average 68.8% of the expected increase in firing costs is translated onto lower wages. This percentage is increasing in the estimated wage loss of the worker (which depends on the estimated point coefficient and on the average tenure of the worker) and is decreasing in the expected firing costs borne by the employer (which depend on the probability of firing a worker and on legal expenses). In any case, such an average hides heterogeneous effects across workers with different bargaining positions. Appendix A. Evidence on Firm and Worker Sorting A.1. Firms To verify if firms sort according to pre‐existing characteristics, we first estimate a regression of firms’ average wages paid in 1986–9 (before the reform) on firm size, firm age, year dummies and firm fixed effects. We then use the time‐invariant portion of the residual as one of the determinants of the firm probability of growing. The probit regression is of the form djt=β’Xjt+δ0Post+δ1dummySjt−1+δ2FEj+α0(dummySjt−1×Post)+α1(FEj×Post)+α2(dummySjt−1×Post×FEj)+εjt,(A.1) where djt=1 if firm j in year t has a larger size than in t − 1. The term dummySjt−1 denotes a set of firm size dummies while the variable Post takes the value of one from 1991. The term FEj denotes the estimated firm fixed effects. The matrix Xjt includes a quadratic in firms’ age, year dummies, sector dummies and a polynomial in lagged firm size. Column 1 of Table 7 shows that on average firms just below 15 employees are about 3% less likely to grow of one unit than larger firms. Finally, Column 3 indicates that the effect is similar for firms with different average pre‐reform wages, as the coefficient of the triple interaction Post 1990 × Firms Fixed Effect × Dummy 15 is not significantly different from zero. Table A1. Firm Sorting . (1) . (2) . (3) . Dummy 13 −0.012 0.014 0.005 (0.014) (0.028) (0.028) Dummy 14 −0.026* −0.041 −0.041 (0.014) (0.027) (0.027) Dummy 15 −0.029* −0.005 −0.001 (0.015) (0.030) (0.030) Post 1990 × Dummy 13 −0.034 −0.030 (0.030) (0.031) Post 1990 × Dummy 14 0.021 0.030 (0.033) (0.034) Post 1990 × Dummy 15 −0.031 −0.035 (0.033) (0.033) Firms fixed effect 0.242*** (0.033) Firms fixed effect × Dummy 13 0.348** (0.151) Firms fixed effect × Dummy 14 −0.087 (0.139) Firms fixed effect × Dummy 15 −0.302* (0.165) Post 1990 × Firms fixed effect −0.220*** (0.036) Post 1990 × Firms fixed effect × Dummy 13 −0.254 (0.173) Post 1990 × Firms fixed effect × Dummy 14 0.011 (0.162) Post 1990 × Firms fixed effect × Dummy 15 0.297 (0.183) Observations 29,315 29,315 27,720 . (1) . (2) . (3) . Dummy 13 −0.012 0.014 0.005 (0.014) (0.028) (0.028) Dummy 14 −0.026* −0.041 −0.041 (0.014) (0.027) (0.027) Dummy 15 −0.029* −0.005 −0.001 (0.015) (0.030) (0.030) Post 1990 × Dummy 13 −0.034 −0.030 (0.030) (0.031) Post 1990 × Dummy 14 0.021 0.030 (0.033) (0.034) Post 1990 × Dummy 15 −0.031 −0.035 (0.033) (0.033) Firms fixed effect 0.242*** (0.033) Firms fixed effect × Dummy 13 0.348** (0.151) Firms fixed effect × Dummy 14 −0.087 (0.139) Firms fixed effect × Dummy 15 −0.302* (0.165) Post 1990 × Firms fixed effect −0.220*** (0.036) Post 1990 × Firms fixed effect × Dummy 13 −0.254 (0.173) Post 1990 × Firms fixed effect × Dummy 14 0.011 (0.162) Post 1990 × Firms fixed effect × Dummy 15 0.297 (0.183) Observations 29,315 29,315 27,720 Notes. The dependent variable is a dummy that takes the value of 1 if in firm j employment at time t is larger than employment at time t − 1, and 0 otherwise. Firms between 5 and 25 workers are included. All specifications include a third‐degree polynomial in lagged firm size, a quadratic in firms’ age, sector dummies and year dummies. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab Table A1. Firm Sorting . (1) . (2) . (3) . Dummy 13 −0.012 0.014 0.005 (0.014) (0.028) (0.028) Dummy 14 −0.026* −0.041 −0.041 (0.014) (0.027) (0.027) Dummy 15 −0.029* −0.005 −0.001 (0.015) (0.030) (0.030) Post 1990 × Dummy 13 −0.034 −0.030 (0.030) (0.031) Post 1990 × Dummy 14 0.021 0.030 (0.033) (0.034) Post 1990 × Dummy 15 −0.031 −0.035 (0.033) (0.033) Firms fixed effect 0.242*** (0.033) Firms fixed effect × Dummy 13 0.348** (0.151) Firms fixed effect × Dummy 14 −0.087 (0.139) Firms fixed effect × Dummy 15 −0.302* (0.165) Post 1990 × Firms fixed effect −0.220*** (0.036) Post 1990 × Firms fixed effect × Dummy 13 −0.254 (0.173) Post 1990 × Firms fixed effect × Dummy 14 0.011 (0.162) Post 1990 × Firms fixed effect × Dummy 15 0.297 (0.183) Observations 29,315 29,315 27,720 . (1) . (2) . (3) . Dummy 13 −0.012 0.014 0.005 (0.014) (0.028) (0.028) Dummy 14 −0.026* −0.041 −0.041 (0.014) (0.027) (0.027) Dummy 15 −0.029* −0.005 −0.001 (0.015) (0.030) (0.030) Post 1990 × Dummy 13 −0.034 −0.030 (0.030) (0.031) Post 1990 × Dummy 14 0.021 0.030 (0.033) (0.034) Post 1990 × Dummy 15 −0.031 −0.035 (0.033) (0.033) Firms fixed effect 0.242*** (0.033) Firms fixed effect × Dummy 13 0.348** (0.151) Firms fixed effect × Dummy 14 −0.087 (0.139) Firms fixed effect × Dummy 15 −0.302* (0.165) Post 1990 × Firms fixed effect −0.220*** (0.036) Post 1990 × Firms fixed effect × Dummy 13 −0.254 (0.173) Post 1990 × Firms fixed effect × Dummy 14 0.011 (0.162) Post 1990 × Firms fixed effect × Dummy 15 0.297 (0.183) Observations 29,315 29,315 27,720 Notes. The dependent variable is a dummy that takes the value of 1 if in firm j employment at time t is larger than employment at time t − 1, and 0 otherwise. Firms between 5 and 25 workers are included. All specifications include a third‐degree polynomial in lagged firm size, a quadratic in firms’ age, sector dummies and year dummies. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab A.2. Workers We test whether workers non‐randomly sort into firms above and below the 15‐employee threshold adopting two strategies. First, we check whether firms’ observable characteristics Xjt ⁠, such as industry, age and occupation (white collar/blue collar) composition of the workforce, are balanced in the neighbourhood of the 15‐employee threshold. The balance tests are performed running the firm‐level regression: Xjt=δ0Post+δ1DjtS+δ2(DjtS×Post)+∑k=1n(γkfsizejtk)+ejt.(A.2) Table A2 shows the coefficients and standard errors of δ2 ⁠. No pre‐treatment characteristics show a significant discontinuity at the 15‐employee threshold after the reform in the third‐degree polynomial specification. In particular, the age, occupation and industry composition of firms across the two sides of the threshold is not significantly different after the reform. The only weakly significant coefficients belong to two industry dummies in the case of the second‐degree polynomial specification. Table A2. Balanced Test of Firm Characteristics . Age . White collar . Agriculture . Gas water oil . Extraction minerals chemical . Metal . Manuf‐acturing . Construction . Wholesale retail hotel . Transportation . Second‐degree polynomial Post 1990 × Small firm −3.760 −0.473 −0.112 −0.001 0.101 −0.699 1.218* −0.990* 0.823 0.240 (10.816) (0.515) (0.131) (0.028) (0.441) (0.733) (0.737) (0.535) (0.620) (0.251) Third‐degree polynomial Post 1990 × Small firm −41.268 1.355 0.531 0.002 3.533 1.333 −2.234 −1.770 −1.707 −1.541 (83.991) (3.996) (1.014) (0.216) (3.420) (5.691) (5.721) (4.155) (4.816) (1.952) Obs. 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 . Age . White collar . Agriculture . Gas water oil . Extraction minerals chemical . Metal . Manuf‐acturing . Construction . Wholesale retail hotel . Transportation . Second‐degree polynomial Post 1990 × Small firm −3.760 −0.473 −0.112 −0.001 0.101 −0.699 1.218* −0.990* 0.823 0.240 (10.816) (0.515) (0.131) (0.028) (0.441) (0.733) (0.737) (0.535) (0.620) (0.251) Third‐degree polynomial Post 1990 × Small firm −41.268 1.355 0.531 0.002 3.533 1.333 −2.234 −1.770 −1.707 −1.541 (83.991) (3.996) (1.014) (0.216) (3.420) (5.691) (5.721) (4.155) (4.816) (1.952) Obs. 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 Notes. Data collapsed at the firm‐year level. * Significance at 10%. Open in new tab Table A2. Balanced Test of Firm Characteristics . Age . White collar . Agriculture . Gas water oil . Extraction minerals chemical . Metal . Manuf‐acturing . Construction . Wholesale retail hotel . Transportation . Second‐degree polynomial Post 1990 × Small firm −3.760 −0.473 −0.112 −0.001 0.101 −0.699 1.218* −0.990* 0.823 0.240 (10.816) (0.515) (0.131) (0.028) (0.441) (0.733) (0.737) (0.535) (0.620) (0.251) Third‐degree polynomial Post 1990 × Small firm −41.268 1.355 0.531 0.002 3.533 1.333 −2.234 −1.770 −1.707 −1.541 (83.991) (3.996) (1.014) (0.216) (3.420) (5.691) (5.721) (4.155) (4.816) (1.952) Obs. 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 . Age . White collar . Agriculture . Gas water oil . Extraction minerals chemical . Metal . Manuf‐acturing . Construction . Wholesale retail hotel . Transportation . Second‐degree polynomial Post 1990 × Small firm −3.760 −0.473 −0.112 −0.001 0.101 −0.699 1.218* −0.990* 0.823 0.240 (10.816) (0.515) (0.131) (0.028) (0.441) (0.733) (0.737) (0.535) (0.620) (0.251) Third‐degree polynomial Post 1990 × Small firm −41.268 1.355 0.531 0.002 3.533 1.333 −2.234 −1.770 −1.707 −1.541 (83.991) (3.996) (1.014) (0.216) (3.420) (5.691) (5.721) (4.155) (4.816) (1.952) Obs. 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 28,043 Notes. Data collapsed at the firm‐year level. * Significance at 10%. Open in new tab We further test for non‐random selection of workers by explicitly looking at their flows across firms. If the reform lowers the wage in small firms relative to big firms after the reform, one may expect larger flows of workers from small to big firms and smaller flows from big to small firms after the reform. To assess the extent of worker sorting, we run regressions of the probability of workers moving to a big firm or to a small firm on a number of determinants that include a small‐firm dummy interacted with year dummies. The probit regression is of the form: dij’t=β’Xijt+δ0Djt−1S+δ1Tt+δ2FEi+α0(Tt×Djt−1S)+α1(Tt×FEi)+α2(Tt×Djt−1S×FEi)+εijt,(A.3) where dij’t equals 1 if in year t worker i moves from firm j to a firm j’ which has more than 15 employees (Table A3, columns 1 and 2) or to a firm j’ which has fewer than 15 employees (Table A3, columns 3 and 4). The dummy Djt−1S indicates the size of the firm of origin and it equals 1 if the firm has fewer than 15 employees. The term Tt denotes a set of year dummies. The variable FEi (indicated as Worker Fixed Effect in Table A3) is the time‐invariant component of the individual’s average pre‐reform wage (between 1986 and 1989) purged of age, a third‐degree polynomial in firm size and year dummies. The matrix Xijt includes a quadratic in worker age, sector dummies and a polynomial in the size of the firm of origin. Columns 1 and 2 of Table A.3 show that there is a lower probability of moving to firms larger than 15 coming from a small firm after the reform, that is, in 1990, 1991 and 1992 (negative and significant coefficients on T1990×Djt−1S ⁠, T1991×Djt−1S and T1992×Djt−1S ⁠). However, column 2 of Table A3 shows that the drop in the probability of moving from a small to a large firm is smaller for high‐wage workers in 1991 (positive and significant coefficient on T1991×Djt−1S×FEi ⁠), while it is independent of (the time‐invariant component of) workers wages in 1990 and 1992 (insignificant coefficients on T1990×Djt−1S×FEi and T1992×Djt−1S×FEi ⁠). Thus, except for 1991, the probability of moving from a small to a large firm after the reform is apparently not driven by workers’ attributes correlated with their productivity. Results for the probability of moving from small to small firms (columns 3 and 4) indicate that there are no differential effects around 1990 (insignificant coefficients on both T1990×Djt−1S and T1990×Djt−1S×FEi ⁠). Table A3. Worker Sorting Dependent variable: Mover dummy (probit) . p > 15 . p ≤ 15 . Small‐firm dummy 0.009*** 0.009*** −0.000 0.000 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1990 −0.010*** −0.010*** −0.003 −0.003 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1991 −0.013*** −0.013*** 0.001 0.001 (0.003) (0.003) (0.005) (0.005) Small‐firm dummy × Dummy 1992 −0.014*** −0.014*** 0.024*** 0.023*** (0.003) (0.003) (0.006) (0.006) Small‐firm dummy × Dummy 1993 −0.003 −0.003 0.014*** 0.014*** (0.003) (0.003) (0.005) (0.005) Worker fixed effect −0.010 −0.061*** (0.012) (0.014) Worker fixed effect × Small‐firm dummy 0.001 0.022 (0.015) (0.017) Worker fixed effect × Dummy 1990 −0.008 −0.012 (0.016) (0.019) Worker fixed effect × Dummy 1991 −0.020 −0.001 (0.016) (0.020) Worker fixed effect × Dummy 1992 −0.019 0.044** (0.017) (0.021) Worker fixed effect × Dummy 1993 −0.008 −0.005 (0.015) (0.023) Worker fixed effect × Dummy 1990 × Small‐firm dummy 0.008 0.018 (0.021) (0.024) Worker fixed effect × Dummy 1991 × Small‐firm dummy 0.050** 0.003 (0.021) (0.024) Worker fixed effect × Dummy 1992 × Small‐firm dummy 0.024 −0.033 (0.022) (0.025) Worker fixed effect × Dummy 1993 × Small‐firm dummy 0.016 0.024 (0.018) (0.027) Observations 120,652 120,652 120,583 120,583 Dependent variable: Mover dummy (probit) . p > 15 . p ≤ 15 . Small‐firm dummy 0.009*** 0.009*** −0.000 0.000 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1990 −0.010*** −0.010*** −0.003 −0.003 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1991 −0.013*** −0.013*** 0.001 0.001 (0.003) (0.003) (0.005) (0.005) Small‐firm dummy × Dummy 1992 −0.014*** −0.014*** 0.024*** 0.023*** (0.003) (0.003) (0.006) (0.006) Small‐firm dummy × Dummy 1993 −0.003 −0.003 0.014*** 0.014*** (0.003) (0.003) (0.005) (0.005) Worker fixed effect −0.010 −0.061*** (0.012) (0.014) Worker fixed effect × Small‐firm dummy 0.001 0.022 (0.015) (0.017) Worker fixed effect × Dummy 1990 −0.008 −0.012 (0.016) (0.019) Worker fixed effect × Dummy 1991 −0.020 −0.001 (0.016) (0.020) Worker fixed effect × Dummy 1992 −0.019 0.044** (0.017) (0.021) Worker fixed effect × Dummy 1993 −0.008 −0.005 (0.015) (0.023) Worker fixed effect × Dummy 1990 × Small‐firm dummy 0.008 0.018 (0.021) (0.024) Worker fixed effect × Dummy 1991 × Small‐firm dummy 0.050** 0.003 (0.021) (0.024) Worker fixed effect × Dummy 1992 × Small‐firm dummy 0.024 −0.033 (0.022) (0.025) Worker fixed effect × Dummy 1993 × Small‐firm dummy 0.016 0.024 (0.018) (0.027) Observations 120,652 120,652 120,583 120,583 Notes. In the first (last) two columns, the dependent variable is a dummy that takes the value of 1 if worker i moves to a firm with more (less) than 15 employees and 0 otherwise. Firms between 5 and 25 employees included. All specifications include a quadratic in workers’ age, year dummies, sector dummies and a polynomial in the size of the firm of origin. Standard errors in parentheses. ** Significance at 5% and *** Significance at 1%. Open in new tab Table A3. Worker Sorting Dependent variable: Mover dummy (probit) . p > 15 . p ≤ 15 . Small‐firm dummy 0.009*** 0.009*** −0.000 0.000 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1990 −0.010*** −0.010*** −0.003 −0.003 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1991 −0.013*** −0.013*** 0.001 0.001 (0.003) (0.003) (0.005) (0.005) Small‐firm dummy × Dummy 1992 −0.014*** −0.014*** 0.024*** 0.023*** (0.003) (0.003) (0.006) (0.006) Small‐firm dummy × Dummy 1993 −0.003 −0.003 0.014*** 0.014*** (0.003) (0.003) (0.005) (0.005) Worker fixed effect −0.010 −0.061*** (0.012) (0.014) Worker fixed effect × Small‐firm dummy 0.001 0.022 (0.015) (0.017) Worker fixed effect × Dummy 1990 −0.008 −0.012 (0.016) (0.019) Worker fixed effect × Dummy 1991 −0.020 −0.001 (0.016) (0.020) Worker fixed effect × Dummy 1992 −0.019 0.044** (0.017) (0.021) Worker fixed effect × Dummy 1993 −0.008 −0.005 (0.015) (0.023) Worker fixed effect × Dummy 1990 × Small‐firm dummy 0.008 0.018 (0.021) (0.024) Worker fixed effect × Dummy 1991 × Small‐firm dummy 0.050** 0.003 (0.021) (0.024) Worker fixed effect × Dummy 1992 × Small‐firm dummy 0.024 −0.033 (0.022) (0.025) Worker fixed effect × Dummy 1993 × Small‐firm dummy 0.016 0.024 (0.018) (0.027) Observations 120,652 120,652 120,583 120,583 Dependent variable: Mover dummy (probit) . p > 15 . p ≤ 15 . Small‐firm dummy 0.009*** 0.009*** −0.000 0.000 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1990 −0.010*** −0.010*** −0.003 −0.003 (0.003) (0.003) (0.004) (0.004) Small‐firm dummy × Dummy 1991 −0.013*** −0.013*** 0.001 0.001 (0.003) (0.003) (0.005) (0.005) Small‐firm dummy × Dummy 1992 −0.014*** −0.014*** 0.024*** 0.023*** (0.003) (0.003) (0.006) (0.006) Small‐firm dummy × Dummy 1993 −0.003 −0.003 0.014*** 0.014*** (0.003) (0.003) (0.005) (0.005) Worker fixed effect −0.010 −0.061*** (0.012) (0.014) Worker fixed effect × Small‐firm dummy 0.001 0.022 (0.015) (0.017) Worker fixed effect × Dummy 1990 −0.008 −0.012 (0.016) (0.019) Worker fixed effect × Dummy 1991 −0.020 −0.001 (0.016) (0.020) Worker fixed effect × Dummy 1992 −0.019 0.044** (0.017) (0.021) Worker fixed effect × Dummy 1993 −0.008 −0.005 (0.015) (0.023) Worker fixed effect × Dummy 1990 × Small‐firm dummy 0.008 0.018 (0.021) (0.024) Worker fixed effect × Dummy 1991 × Small‐firm dummy 0.050** 0.003 (0.021) (0.024) Worker fixed effect × Dummy 1992 × Small‐firm dummy 0.024 −0.033 (0.022) (0.025) Worker fixed effect × Dummy 1993 × Small‐firm dummy 0.016 0.024 (0.018) (0.027) Observations 120,652 120,652 120,583 120,583 Notes. In the first (last) two columns, the dependent variable is a dummy that takes the value of 1 if worker i moves to a firm with more (less) than 15 employees and 0 otherwise. Firms between 5 and 25 employees included. All specifications include a quadratic in workers’ age, year dummies, sector dummies and a polynomial in the size of the firm of origin. Standard errors in parentheses. ** Significance at 5% and *** Significance at 1%. Open in new tab Appendix B. IV First Stage Table B1 displays the first stage of the IV model in panel (a) of Table 2, that is, estimates from the regression of the two endogenous variables DjtS and DjtS×Post on the full set of included and excluded instruments (see Table B2 for the first‐stage statistics of the IV model in panel (b)). Column 1 reports results for the small‐firm dummy DjtS and shows a negative coefficient on firm size in 1987: as expected, the larger the firm is in 1987, the lower the probability of being below the 15‐employee threshold over the sample period 1989–93. This coefficient is insignificant plausibly for the presence among the controls of the polynomial in current firm size. The interaction term between firm size in 1987 and post‐reform dummy is negative and significant. Size in 1988 enters positively in the regression showing evidence of mean reversion: controlling for size in 1987 and for current firm size, firms which experience a positive shock in 1988 tend to switch back to their regular size afterwards. The same pattern of alternating signs applies to the results in Column 2 for DjtS×Post ⁠, in which all coefficients are significant. The mean‐reversion effect highlighted by the alternate sign on firm size in 1987 and 1988 suggests that using a single pre‐reform year as an instrument may bias the results. In fact, some firms assigned by the single instrument to the small (large) size category may actually correspond to firms that are typically of a larger (smaller) size but that had had a relatively bad (good) year in that period (Martins, 2009). Finally, the overall power of the instruments is strong – as indicated by the F‐test of the excluded instruments equal to 5.71 and 11031.65 – and Hansen’s J statistic shows that the specification passes the test of overidentifying restrictions. Table B1. First Stage of IV Model in Panel (a) of Table 2 . Small . Small × Post 1990 . Excluded instruments Size in 1987 −0.0015 −0.0185*** (0.0015) (0.0020) Size in 1988 0.0020 0.0840*** (0.0016) (0.0021) Size in 1987 × 1990 −0.0018** 0.0153*** (0.0008) (0.0011) Size in 1988 × 1990 0.0009 −0.0843*** (0.0008) (0.0011) Observations 76,814 76,814 R2 0.55 0.82 F‐test of excluded instruments 5.71 11,031.65 (p‐value) (0.000) (0.000) Hansen’s J statistic 0.53 (p‐value) (0.77) . Small . Small × Post 1990 . Excluded instruments Size in 1987 −0.0015 −0.0185*** (0.0015) (0.0020) Size in 1988 0.0020 0.0840*** (0.0016) (0.0021) Size in 1987 × 1990 −0.0018** 0.0153*** (0.0008) (0.0011) Size in 1988 × 1990 0.0009 −0.0843*** (0.0008) (0.0011) Observations 76,814 76,814 R2 0.55 0.82 F‐test of excluded instruments 5.71 11,031.65 (p‐value) (0.000) (0.000) Hansen’s J statistic 0.53 (p‐value) (0.77) Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. ** Significance at 5% and *** Significance at 1%. Open in new tab Table B1. First Stage of IV Model in Panel (a) of Table 2 . Small . Small × Post 1990 . Excluded instruments Size in 1987 −0.0015 −0.0185*** (0.0015) (0.0020) Size in 1988 0.0020 0.0840*** (0.0016) (0.0021) Size in 1987 × 1990 −0.0018** 0.0153*** (0.0008) (0.0011) Size in 1988 × 1990 0.0009 −0.0843*** (0.0008) (0.0011) Observations 76,814 76,814 R2 0.55 0.82 F‐test of excluded instruments 5.71 11,031.65 (p‐value) (0.000) (0.000) Hansen’s J statistic 0.53 (p‐value) (0.77) . Small . Small × Post 1990 . Excluded instruments Size in 1987 −0.0015 −0.0185*** (0.0015) (0.0020) Size in 1988 0.0020 0.0840*** (0.0016) (0.0021) Size in 1987 × 1990 −0.0018** 0.0153*** (0.0008) (0.0011) Size in 1988 × 1990 0.0009 −0.0843*** (0.0008) (0.0011) Observations 76,814 76,814 R2 0.55 0.82 F‐test of excluded instruments 5.71 11,031.65 (p‐value) (0.000) (0.000) Hansen’s J statistic 0.53 (p‐value) (0.77) Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. ** Significance at 5% and *** Significance at 1%. Open in new tab Table B2. IV First‐Stage Statistics . Table 2 . Table 3 . Table 4 . Table 5 . Table 6 . . Panel (b) . Panel (a) . Panel (b) . Panel (c) . Hansen J test 4.14 1.18 0.04 10.27 0.91 5.95 4.12 (0.13) (0.88) (0.98) (0.11) (0.92) (0.20) (0.39) F‐tests of excluded instruments of the first‐stage equations Small firm 6.75 5.13 4.72 1.71 3.10 2.26 2.18 (0.00) (0.00) (0.00) (0.06) (0.00) (0.02) (0.03) Small firm × Post 1990 9,650.85 5,612.73 7,487.26 563.70 5,548.92 3,017.63 3,021.61 (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) Small firm × var. empl. growth 23.15 (0.00) Small × Post 1990 × var. empl. growth 445.37 (0.00) Small firm × mover 335.60 (0.00) Small firm × Post 1990 × mover 830.15 (0.00) Small firm × Entry dummy 269.54 (0.00) Small firm × Post 1990 × Entry dummy 230.25 (0.00) Small firm × blue collar 4,865.72 (0.00) Small firm × Post 1990 × blue collar 445.37 (0.00) Small firm × young (below 30 above 40) 135.12 (0.00) Small firm × Post 1990 × young 1,198.53 (0.00) Small firm × young blue collar 151.77 (0.00) Small firm × Post 1990 × young blue collar 1,034.74 (0.00) . Table 2 . Table 3 . Table 4 . Table 5 . Table 6 . . Panel (b) . Panel (a) . Panel (b) . Panel (c) . Hansen J test 4.14 1.18 0.04 10.27 0.91 5.95 4.12 (0.13) (0.88) (0.98) (0.11) (0.92) (0.20) (0.39) F‐tests of excluded instruments of the first‐stage equations Small firm 6.75 5.13 4.72 1.71 3.10 2.26 2.18 (0.00) (0.00) (0.00) (0.06) (0.00) (0.02) (0.03) Small firm × Post 1990 9,650.85 5,612.73 7,487.26 563.70 5,548.92 3,017.63 3,021.61 (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) Small firm × var. empl. growth 23.15 (0.00) Small × Post 1990 × var. empl. growth 445.37 (0.00) Small firm × mover 335.60 (0.00) Small firm × Post 1990 × mover 830.15 (0.00) Small firm × Entry dummy 269.54 (0.00) Small firm × Post 1990 × Entry dummy 230.25 (0.00) Small firm × blue collar 4,865.72 (0.00) Small firm × Post 1990 × blue collar 445.37 (0.00) Small firm × young (below 30 above 40) 135.12 (0.00) Small firm × Post 1990 × young 1,198.53 (0.00) Small firm × young blue collar 151.77 (0.00) Small firm × Post 1990 × young blue collar 1,034.74 (0.00) Notes. Each column shows the first‐stage statistics of the IV models presented in Table 2 (panel (b)) and Tables 3–6. First‐stage results of the IV model presented in panel (a) of Table 2 are displayed in Table B1. The first row displays the Hansen J statistic (p‐value in the second row). Subsequent rows present the F‐test of excluded instruments for each first‐stage equation (p‐values in parentheses). Open in new tab Table B2. IV First‐Stage Statistics . Table 2 . Table 3 . Table 4 . Table 5 . Table 6 . . Panel (b) . Panel (a) . Panel (b) . Panel (c) . Hansen J test 4.14 1.18 0.04 10.27 0.91 5.95 4.12 (0.13) (0.88) (0.98) (0.11) (0.92) (0.20) (0.39) F‐tests of excluded instruments of the first‐stage equations Small firm 6.75 5.13 4.72 1.71 3.10 2.26 2.18 (0.00) (0.00) (0.00) (0.06) (0.00) (0.02) (0.03) Small firm × Post 1990 9,650.85 5,612.73 7,487.26 563.70 5,548.92 3,017.63 3,021.61 (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) Small firm × var. empl. growth 23.15 (0.00) Small × Post 1990 × var. empl. growth 445.37 (0.00) Small firm × mover 335.60 (0.00) Small firm × Post 1990 × mover 830.15 (0.00) Small firm × Entry dummy 269.54 (0.00) Small firm × Post 1990 × Entry dummy 230.25 (0.00) Small firm × blue collar 4,865.72 (0.00) Small firm × Post 1990 × blue collar 445.37 (0.00) Small firm × young (below 30 above 40) 135.12 (0.00) Small firm × Post 1990 × young 1,198.53 (0.00) Small firm × young blue collar 151.77 (0.00) Small firm × Post 1990 × young blue collar 1,034.74 (0.00) . Table 2 . Table 3 . Table 4 . Table 5 . Table 6 . . Panel (b) . Panel (a) . Panel (b) . Panel (c) . Hansen J test 4.14 1.18 0.04 10.27 0.91 5.95 4.12 (0.13) (0.88) (0.98) (0.11) (0.92) (0.20) (0.39) F‐tests of excluded instruments of the first‐stage equations Small firm 6.75 5.13 4.72 1.71 3.10 2.26 2.18 (0.00) (0.00) (0.00) (0.06) (0.00) (0.02) (0.03) Small firm × Post 1990 9,650.85 5,612.73 7,487.26 563.70 5,548.92 3,017.63 3,021.61 (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) (0.00) Small firm × var. empl. growth 23.15 (0.00) Small × Post 1990 × var. empl. growth 445.37 (0.00) Small firm × mover 335.60 (0.00) Small firm × Post 1990 × mover 830.15 (0.00) Small firm × Entry dummy 269.54 (0.00) Small firm × Post 1990 × Entry dummy 230.25 (0.00) Small firm × blue collar 4,865.72 (0.00) Small firm × Post 1990 × blue collar 445.37 (0.00) Small firm × young (below 30 above 40) 135.12 (0.00) Small firm × Post 1990 × young 1,198.53 (0.00) Small firm × young blue collar 151.77 (0.00) Small firm × Post 1990 × young blue collar 1,034.74 (0.00) Notes. Each column shows the first‐stage statistics of the IV models presented in Table 2 (panel (b)) and Tables 3–6. First‐stage results of the IV model presented in panel (a) of Table 2 are displayed in Table B1. The first row displays the Hansen J statistic (p‐value in the second row). Subsequent rows present the F‐test of excluded instruments for each first‐stage equation (p‐values in parentheses). Open in new tab Appendix C. Robustness Checks and Placebo Tests In this section, we show that the results presented in Section 4. are robust to a number of checks. We perform our robustness exercises on the model with worker fixed effects and on the IV model with worker fixed effects, which allows to control for both types of sorting. In Tables C1 and C2, we implement placebo tests by estimating the treatment effect at fake firm‐size thresholds and fake reform years, where there should be no effect. We first estimate the treatment effect below and above the fake 6, 10, 20 and 23‐employee thresholds. The coefficients of interests are mostly insignificant. Table C1 shows that the fake firm size threshold is significant only at 20 employees but the significance disappears in the IV specification. In Table C2, we estimate the treatment effect before and after the fake reform years 1991, 1992, 1988 and 1989 (excluding in turn the fake year of the reform as we did with 1990 in Table 2). A significant negative effect appears only in 1991 (i.e. considering 1989 and 1990 as pre‐reform years and 1992 and 1993 as post‐reform years). This is not surprising because 1991 is the year immediately after the reform and we may take this result as an indication that 1990, the year of the actual reform, belongs to the pre rather than the post‐reform period. Finally, the interaction between the small firm and the post‐reform dummy is not significant when considering 1992 and 1989 as reform years and turns positive when we pretend that the reform occurred in 1988. Table C1. Falsification Exercise: Fake Firm‐size Threshold Fake firm‐size threshold . 6 employees . 10 employees . 20 employees . 23 employees . Panel (a): Worker fixed effects Small firm × post 1990 −0.003 −0.003 −0.009*** −0.001 (0.003) (0.002) (0.003) (0.005) Observations 96,333 96,333 96,333 96,333 R2 0.16 0.16 0.16 0.16 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.064 −0.007 0.001 0.043 (0.052) (0.006) (0.015) (0.081) Observations 76,814 76,814 76,814 76,814 Fake firm‐size threshold . 6 employees . 10 employees . 20 employees . 23 employees . Panel (a): Worker fixed effects Small firm × post 1990 −0.003 −0.003 −0.009*** −0.001 (0.003) (0.002) (0.003) (0.005) Observations 96,333 96,333 96,333 96,333 R2 0.16 0.16 0.16 0.16 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.064 −0.007 0.001 0.043 (0.052) (0.006) (0.015) (0.081) Observations 76,814 76,814 76,814 76,814 Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. *** Significance at 1%. Open in new tab Table C1. Falsification Exercise: Fake Firm‐size Threshold Fake firm‐size threshold . 6 employees . 10 employees . 20 employees . 23 employees . Panel (a): Worker fixed effects Small firm × post 1990 −0.003 −0.003 −0.009*** −0.001 (0.003) (0.002) (0.003) (0.005) Observations 96,333 96,333 96,333 96,333 R2 0.16 0.16 0.16 0.16 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.064 −0.007 0.001 0.043 (0.052) (0.006) (0.015) (0.081) Observations 76,814 76,814 76,814 76,814 Fake firm‐size threshold . 6 employees . 10 employees . 20 employees . 23 employees . Panel (a): Worker fixed effects Small firm × post 1990 −0.003 −0.003 −0.009*** −0.001 (0.003) (0.002) (0.003) (0.005) Observations 96,333 96,333 96,333 96,333 R2 0.16 0.16 0.16 0.16 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.064 −0.007 0.001 0.043 (0.052) (0.006) (0.015) (0.081) Observations 76,814 76,814 76,814 76,814 Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. *** Significance at 1%. Open in new tab Table C2. Falsification Exercise: Fake Reform Year Fake reform year . 1991 . 1992 . 1988 . 1989 . Panel (a): Worker fixed effects Small firm × post‐reform year −0.004*** −0.001 0.003* 0.002 (0.001) (0.002) (0.002) (0.001) Observations 96,627 96,458 139,794 136,784 R2 0.15 0.15 0.24 0.28 Panel (b): IV + Worker fixed effects Small firm × post‐reform year −0.004* 0.000 0.006 0.000 (0.003) (0.003) (0.004) (0.004) Observations 75,852 75,852 113,884 113,238 Fake reform year . 1991 . 1992 . 1988 . 1989 . Panel (a): Worker fixed effects Small firm × post‐reform year −0.004*** −0.001 0.003* 0.002 (0.001) (0.002) (0.002) (0.001) Observations 96,627 96,458 139,794 136,784 R2 0.15 0.15 0.24 0.28 Panel (b): IV + Worker fixed effects Small firm × post‐reform year −0.004* 0.000 0.006 0.000 (0.003) (0.003) (0.004) (0.004) Observations 75,852 75,852 113,884 113,238 Notes. The sample of columns 1 and 2 spans over the period 1989–93 excluding the year of the falsified reform. The sample of columns 3 and 4 spans over 1987–93 excluding the year of the falsified reform. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. * Significance at 10% and *** Significance at 1%. Open in new tab Table C2. Falsification Exercise: Fake Reform Year Fake reform year . 1991 . 1992 . 1988 . 1989 . Panel (a): Worker fixed effects Small firm × post‐reform year −0.004*** −0.001 0.003* 0.002 (0.001) (0.002) (0.002) (0.001) Observations 96,627 96,458 139,794 136,784 R2 0.15 0.15 0.24 0.28 Panel (b): IV + Worker fixed effects Small firm × post‐reform year −0.004* 0.000 0.006 0.000 (0.003) (0.003) (0.004) (0.004) Observations 75,852 75,852 113,884 113,238 Fake reform year . 1991 . 1992 . 1988 . 1989 . Panel (a): Worker fixed effects Small firm × post‐reform year −0.004*** −0.001 0.003* 0.002 (0.001) (0.002) (0.002) (0.001) Observations 96,627 96,458 139,794 136,784 R2 0.15 0.15 0.24 0.28 Panel (b): IV + Worker fixed effects Small firm × post‐reform year −0.004* 0.000 0.006 0.000 (0.003) (0.003) (0.004) (0.004) Observations 75,852 75,852 113,884 113,238 Notes. The sample of columns 1 and 2 spans over the period 1989–93 excluding the year of the falsified reform. The sample of columns 3 and 4 spans over 1987–93 excluding the year of the falsified reform. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. * Significance at 10% and *** Significance at 1%. Open in new tab In Table C3, we run robustness checks with respect to the time span of the sample, enlarging it from the benchmark 1989–93 to 1988–93, 1987–94, 1986–96 and 1986–94, and restricting it to 1989–91 and 1989–92. In all cases, the effect is negative and significant, except for the 1988–93 sample in the specification with worker fixed effects and the 1987–94 sample in the specification with worker‐fixed effects plus IV in which significance is not attained. Table C4 shows that the results are robust to alternative specifications of the polynomial in firm size. Results are generally robust to using a first and second‐degree polynomial, except for two cases where the IV estimates are still negative but insignificant. Finally, in Table C5 we fit a linear regression function to the observations distributed within a distance Δ on both sides of the threshold: logwijt=β’Xijt+δ1DjtS+δ2(DjtS×Post)+εijtfor firm size∈[15−Δ,15+Δ],(C.1) where Xijt contains the same controls as in (1). We choose Δ with the cross‐validation method of Imbens and Lemieux (2008). The cross‐validation method consists in choosing Δ so as to minimise the loss function: L(Δ)=(1/N)∑i=1N[logwi−logw^Δ(fsizej)]2 where, for every fsizej to the left (right) of the threshold 15, we predict logw^Δ(fsizej) as if it were at the boundary of the estimation using only observations in the interval fsizej∈[15−Δ,15+Δ] ⁠. The optimal Δ chosen between 1 and 15 is Δ*=12 with L(12) = 0.03762235. Table C5 shows that the results are robust to the specification change: the local linear regression estimator yields a negative significant coefficient on samples taken over different years, except for the IV model in the 1989–93 sample. Table C3. Robustness to Different Time Periods Time periods . 1989–93 . 1989–91 . 1989–92 . 1988–93 . 1987–94 . 1986–96 . 1986–94 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.002 −0.003* −0.005*** −0.003** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 117,630 158,116 211,267 175,835 R2 0.16 0.25 0.2 0.24 0.26 0.29 0.3 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.011*** −0.015*** −0.015*** −0.006** −0.008 −0.018** −0.012* (0.004) (0.004) (0.005) (0.003) (0.005) (0.008) (0.006) Observations 76,814 36,320 57,593 98,840 134,191 176,648 151,189 Time periods . 1989–93 . 1989–91 . 1989–92 . 1988–93 . 1987–94 . 1986–96 . 1986–94 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.002 −0.003* −0.005*** −0.003** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 117,630 158,116 211,267 175,835 R2 0.16 0.25 0.2 0.24 0.26 0.29 0.3 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.011*** −0.015*** −0.015*** −0.006** −0.008 −0.018** −0.012* (0.004) (0.004) (0.005) (0.003) (0.005) (0.008) (0.006) Observations 76,814 36,320 57,593 98,840 134,191 176,648 151,189 Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab Table C3. Robustness to Different Time Periods Time periods . 1989–93 . 1989–91 . 1989–92 . 1988–93 . 1987–94 . 1986–96 . 1986–94 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.002 −0.003* −0.005*** −0.003** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 117,630 158,116 211,267 175,835 R2 0.16 0.25 0.2 0.24 0.26 0.29 0.3 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.011*** −0.015*** −0.015*** −0.006** −0.008 −0.018** −0.012* (0.004) (0.004) (0.005) (0.003) (0.005) (0.008) (0.006) Observations 76,814 36,320 57,593 98,840 134,191 176,648 151,189 Time periods . 1989–93 . 1989–91 . 1989–92 . 1988–93 . 1987–94 . 1986–96 . 1986–94 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.002 −0.003* −0.005*** −0.003** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 117,630 158,116 211,267 175,835 R2 0.16 0.25 0.2 0.24 0.26 0.29 0.3 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.011*** −0.015*** −0.015*** −0.006** −0.008 −0.018** −0.012* (0.004) (0.004) (0.005) (0.003) (0.005) (0.008) (0.006) Observations 76,814 36,320 57,593 98,840 134,191 176,648 151,189 Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. * Significance at 10%; ** Significance at 5% and *** Significance at 1%. Open in new tab Table C4. Robustness to Polynomials of Different Degrees . 1989–93 . 1989–91 . 1989–92 . 1989–93 . 1989–91 . 1989–92 . Time periods Polynomial of degree 1 Polynomial of degree 2 Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 96,333 48,332 72,526 R2 0.16 0.25 0.2 0.16 0.25 0.2 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.005 −0.015*** −0.005 −0.008** −0.021** −0.01*** (0.003) (0.004) (0.006) (0.003) (0.009) (0.003) Observations 76,814 36,320 57,593 76,814 36,320 57,593 . 1989–93 . 1989–91 . 1989–92 . 1989–93 . 1989–91 . 1989–92 . Time periods Polynomial of degree 1 Polynomial of degree 2 Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 96,333 48,332 72,526 R2 0.16 0.25 0.2 0.16 0.25 0.2 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.005 −0.015*** −0.005 −0.008** −0.021** −0.01*** (0.003) (0.004) (0.006) (0.003) (0.009) (0.003) Observations 76,814 36,320 57,593 76,814 36,320 57,593 Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. ** Significance at 5% and *** Significance at 1%. Open in new tab Table C4. Robustness to Polynomials of Different Degrees . 1989–93 . 1989–91 . 1989–92 . 1989–93 . 1989–91 . 1989–92 . Time periods Polynomial of degree 1 Polynomial of degree 2 Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 96,333 48,332 72,526 R2 0.16 0.25 0.2 0.16 0.25 0.2 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.005 −0.015*** −0.005 −0.008** −0.021** −0.01*** (0.003) (0.004) (0.006) (0.003) (0.009) (0.003) Observations 76,814 36,320 57,593 76,814 36,320 57,593 . 1989–93 . 1989–91 . 1989–92 . 1989–93 . 1989–91 . 1989–92 . Time periods Polynomial of degree 1 Polynomial of degree 2 Panel (a): Worker fixed effects Small firm × post 1990 −0.004** −0.006*** −0.005*** −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) Observations 96,333 48,332 72,526 96,333 48,332 72,526 R2 0.16 0.25 0.2 0.16 0.25 0.2 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.005 −0.015*** −0.005 −0.008** −0.021** −0.01*** (0.003) (0.004) (0.006) (0.003) (0.009) (0.003) Observations 76,814 36,320 57,593 76,814 36,320 57,593 Notes. Robust standard errors clustered by individual in parentheses. All specifications include a third‐degree polynomial in the size of the firm, age dummies, sectoral dummies, year dummies and a blue‐collar dummy. ** Significance at 5% and *** Significance at 1%. Open in new tab Table C5. Local Linear Regression with Optimal Bandwidth Time periods . 1989–93 . 1989–91 . 1989–92 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) Observations 118,308 59,450 89,030 R2 0.15 0.24 0.19 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.004 −0.011*** −0.008*** (0.003) (0.003) (0.002) Observations 94,396 46,160 71,347 Time periods . 1989–93 . 1989–91 . 1989–92 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) Observations 118,308 59,450 89,030 R2 0.15 0.24 0.19 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.004 −0.011*** −0.008*** (0.003) (0.003) (0.002) Observations 94,396 46,160 71,347 Notes. Robust standard errors clustered by individual in parentheses. Local Linear Regression (LLR) with optimal symmetric bandwidth Δ = 12. All specifications include age dummies, sectoral dummies, year dummies and a blue‐collar dummy. *** Significance at 1%. Open in new tab Table C5. Local Linear Regression with Optimal Bandwidth Time periods . 1989–93 . 1989–91 . 1989–92 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) Observations 118,308 59,450 89,030 R2 0.15 0.24 0.19 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.004 −0.011*** −0.008*** (0.003) (0.003) (0.002) Observations 94,396 46,160 71,347 Time periods . 1989–93 . 1989–91 . 1989–92 . Panel (a): Worker fixed effects Small firm × post 1990 −0.004*** −0.006*** −0.005*** (0.002) (0.002) (0.002) Observations 118,308 59,450 89,030 R2 0.15 0.24 0.19 Panel (b): IV + Worker fixed effects Small firm × post 1990 −0.004 −0.011*** −0.008*** (0.003) (0.003) (0.002) Observations 94,396 46,160 71,347 Notes. Robust standard errors clustered by individual in parentheses. Local Linear Regression (LLR) with optimal symmetric bandwidth Δ = 12. All specifications include age dummies, sectoral dummies, year dummies and a blue‐collar dummy. *** Significance at 1%. Open in new tab C.1. Firm Entry and Exit One additional concern is that the negative effect of the EPL reform on wages found in Table 2 may be driven by either lower entry or higher exit of firms below the threshold after the reform (or both). The argument is that in the absence of the reform, there would be a larger number of small firms and therefore higher labour demand and higher wages in the treatment group of firms. Table C6 shows that the probability of entry decreases in firms below the threshold relative to larger firms after the reform, although not significantly so. Also the probability of exit is not significantly different in firms below the threshold relative to larger firms after the reform. Thus, our results are unlikely to be driven by differential entry or exit.20 Table C6. Effects of the Reform on Entry and Exit . Entry . Exit . . LPM . Probit . LPM . Probit . Small‐firm dummy −0.004 −0.087 −0.008*** −0.401* (0.009) (0.079) (0.002) (0.241) Small‐firm dummy × post 1990 −0.010 −0.012 0.001 −0.070 (0.008) (0.066) (0.002) (0.209) Observations 28,043 28,043 28,043 28,043 R2 0.01 0.00 . Entry . Exit . . LPM . Probit . LPM . Probit . Small‐firm dummy −0.004 −0.087 −0.008*** −0.401* (0.009) (0.079) (0.002) (0.241) Small‐firm dummy × post 1990 −0.010 −0.012 0.001 −0.070 (0.008) (0.066) (0.002) (0.209) Observations 28,043 28,043 28,043 28,043 R2 0.01 0.00 Notes. Columns 1 and 3 report results from Linear Probability Models and columns 2 and 4 from Probit models. Entry models include a third‐degree polynomial in firm size, sectoral dummies and year dummies. Exit models additionally include a second‐degree polynomial in firm age. Robust standard errors clustered by firm in parentheses. * Significance at 10% and *** Significance at 1%. Open in new tab Table C6. Effects of the Reform on Entry and Exit . Entry . Exit . . LPM . Probit . LPM . Probit . Small‐firm dummy −0.004 −0.087 −0.008*** −0.401* (0.009) (0.079) (0.002) (0.241) Small‐firm dummy × post 1990 −0.010 −0.012 0.001 −0.070 (0.008) (0.066) (0.002) (0.209) Observations 28,043 28,043 28,043 28,043 R2 0.01 0.00 . Entry . Exit . . LPM . Probit . LPM . Probit . Small‐firm dummy −0.004 −0.087 −0.008*** −0.401* (0.009) (0.079) (0.002) (0.241) Small‐firm dummy × post 1990 −0.010 −0.012 0.001 −0.070 (0.008) (0.066) (0.002) (0.209) Observations 28,043 28,043 28,043 28,043 R2 0.01 0.00 Notes. Columns 1 and 3 report results from Linear Probability Models and columns 2 and 4 from Probit models. Entry models include a third‐degree polynomial in firm size, sectoral dummies and year dummies. Exit models additionally include a second‐degree polynomial in firm age. Robust standard errors clustered by firm in parentheses. * Significance at 10% and *** Significance at 1%. Open in new tab Appendix D. Additional Tables Table D1. Movers’ and Incumbents’ Characteristics Year . Proportion of job changes . Incumbents’ wages . Movers’ wages . Movers’ entry wages . Movers’ post‐entry wages . 1989 0.0863 302 290 284 291 (0.281) (78) (70.3) (70.2) (70.3) 1990 0.105 310 297 295 298 (0.307) (80.7) (70.7) (69.8) (71.2) 1991 0.0999 322 309 305 311 (0.3) (83.6) (74.6) (72.1) (75.7) 1992 0.0927 324 310 307 312 (0.29) (85.2) (78.1) (79.4) (77.4) 1993 0.0934 325 310 305 312 (0.291) (88.2) (78.9) (74.3) (80.9) Observations 120,652 84,962 35,690 10,414 25,276 Year . Proportion of job changes . Incumbents’ wages . Movers’ wages . Movers’ entry wages . Movers’ post‐entry wages . 1989 0.0863 302 290 284 291 (0.281) (78) (70.3) (70.2) (70.3) 1990 0.105 310 297 295 298 (0.307) (80.7) (70.7) (69.8) (71.2) 1991 0.0999 322 309 305 311 (0.3) (83.6) (74.6) (72.1) (75.7) 1992 0.0927 324 310 307 312 (0.29) (85.2) (78.1) (79.4) (77.4) 1993 0.0934 325 310 305 312 (0.291) (88.2) (78.9) (74.3) (80.9) Observations 120,652 84,962 35,690 10,414 25,276 Notes. Movers are defined as workers who change firm at least once over the period 1989–93. The sample period is 1989–93, including year 1990. Real wages expressed in 1995 euro. Standard deviations in parentheses. Open in new tab Table D1. Movers’ and Incumbents’ Characteristics Year . Proportion of job changes . Incumbents’ wages . Movers’ wages . Movers’ entry wages . Movers’ post‐entry wages . 1989 0.0863 302 290 284 291 (0.281) (78) (70.3) (70.2) (70.3) 1990 0.105 310 297 295 298 (0.307) (80.7) (70.7) (69.8) (71.2) 1991 0.0999 322 309 305 311 (0.3) (83.6) (74.6) (72.1) (75.7) 1992 0.0927 324 310 307 312 (0.29) (85.2) (78.1) (79.4) (77.4) 1993 0.0934 325 310 305 312 (0.291) (88.2) (78.9) (74.3) (80.9) Observations 120,652 84,962 35,690 10,414 25,276 Year . Proportion of job changes . Incumbents’ wages . Movers’ wages . Movers’ entry wages . Movers’ post‐entry wages . 1989 0.0863 302 290 284 291 (0.281) (78) (70.3) (70.2) (70.3) 1990 0.105 310 297 295 298 (0.307) (80.7) (70.7) (69.8) (71.2) 1991 0.0999 322 309 305 311 (0.3) (83.6) (74.6) (72.1) (75.7) 1992 0.0927 324 310 307 312 (0.29) (85.2) (78.1) (79.4) (77.4) 1993 0.0934 325 310 305 312 (0.291) (88.2) (78.9) (74.3) (80.9) Observations 120,652 84,962 35,690 10,414 25,276 Notes. Movers are defined as workers who change firm at least once over the period 1989–93. The sample period is 1989–93, including year 1990. Real wages expressed in 1995 euro. Standard deviations in parentheses. Open in new tab Table D2. Distribution of Wage Drift by Type of Contract National contract for employees of . N . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Non‐specified manufacturing firms 276 0.106 0.140 0.203 0.324 0.561 0.815 1.102 Small‐size manufacturing firms 180 0.116 0.146 0.194 0.290 0.509 0.715 0.833 Textile artisanal firms 972 0.090 0.112 0.168 0.252 0.427 0.649 0.805 Firms of the food industry 876 0.143 0.217 0.307 0.407 0.545 0.741 1.012 Firms of the shoe industry 333 0.101 0.149 0.214 0.351 0.565 0.801 1.082 Firms of the service sector 6,470 0.228 0.281 0.369 0.503 0.705 0.964 1.156 Co‐operative firms of the service sector 57 0.232 0.308 0.422 0.480 0.531 0.751 0.841 Firms of the leather industry 1,857 0.131 0.186 0.274 0.415 0.645 0.963 1.205 Firms of the construction sector 3,111 0.005 0.114 0.223 0.315 0.422 0.579 0.740 Small firms of the construction sector 706 0.061 0.130 0.262 0.381 0.490 0.603 0.706 Construction‐related artisanal firms 2,184 0.036 0.116 0.216 0.291 0.364 0.478 0.565 Firms of the toys and personal articles sector 144 0.124 0.144 0.217 0.319 0.431 0.699 0.868 Firms of the wood and furniture sector 1,595 0.113 0.151 0.201 0.267 0.362 0.519 0.673 Metal‐manufacturing and installation firms 6,311 0.175 0.232 0.327 0.463 0.663 0.929 1.212 Small metal‐manufacturing and installation firms 3,191 0.183 0.231 0.332 0.461 0.622 0.868 1.055 Artisanal metal‐manufacturing and installation firms 8,871 0.116 0.161 0.239 0.365 0.530 0.726 0.879 Firms providing environmental health services 68 0.198 0.218 0.350 0.591 0.852 1.021 1.196 Firms of the transportation sector 649 0.196 0.303 0.431 0.576 0.757 0.951 1.097 Firms providing professional services 160 0.226 0.342 0.544 0.918 1.216 1.647 2.180 Firms of the textile sector 322 0.136 0.159 0.218 0.330 0.463 0.796 1.058 Firms of the tourism sector 562 0.172 0.217 0.284 0.392 0.545 0.772 1.168 Total 38,895 0.125 0.179 0.271 0.397 0.579 0.822 1.028 National contract for employees of . N . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Non‐specified manufacturing firms 276 0.106 0.140 0.203 0.324 0.561 0.815 1.102 Small‐size manufacturing firms 180 0.116 0.146 0.194 0.290 0.509 0.715 0.833 Textile artisanal firms 972 0.090 0.112 0.168 0.252 0.427 0.649 0.805 Firms of the food industry 876 0.143 0.217 0.307 0.407 0.545 0.741 1.012 Firms of the shoe industry 333 0.101 0.149 0.214 0.351 0.565 0.801 1.082 Firms of the service sector 6,470 0.228 0.281 0.369 0.503 0.705 0.964 1.156 Co‐operative firms of the service sector 57 0.232 0.308 0.422 0.480 0.531 0.751 0.841 Firms of the leather industry 1,857 0.131 0.186 0.274 0.415 0.645 0.963 1.205 Firms of the construction sector 3,111 0.005 0.114 0.223 0.315 0.422 0.579 0.740 Small firms of the construction sector 706 0.061 0.130 0.262 0.381 0.490 0.603 0.706 Construction‐related artisanal firms 2,184 0.036 0.116 0.216 0.291 0.364 0.478 0.565 Firms of the toys and personal articles sector 144 0.124 0.144 0.217 0.319 0.431 0.699 0.868 Firms of the wood and furniture sector 1,595 0.113 0.151 0.201 0.267 0.362 0.519 0.673 Metal‐manufacturing and installation firms 6,311 0.175 0.232 0.327 0.463 0.663 0.929 1.212 Small metal‐manufacturing and installation firms 3,191 0.183 0.231 0.332 0.461 0.622 0.868 1.055 Artisanal metal‐manufacturing and installation firms 8,871 0.116 0.161 0.239 0.365 0.530 0.726 0.879 Firms providing environmental health services 68 0.198 0.218 0.350 0.591 0.852 1.021 1.196 Firms of the transportation sector 649 0.196 0.303 0.431 0.576 0.757 0.951 1.097 Firms providing professional services 160 0.226 0.342 0.544 0.918 1.216 1.647 2.180 Firms of the textile sector 322 0.136 0.159 0.218 0.330 0.463 0.796 1.058 Firms of the tourism sector 562 0.172 0.217 0.284 0.392 0.545 0.772 1.168 Total 38,895 0.125 0.179 0.271 0.397 0.579 0.822 1.028 Notes. The wage drift is defined as (wage‐contractual wage)/contractual wage. Contractual wages are bargained at the national level by sector and occupation category (typically five or more categories according to tasks performed and tenure). Open in new tab Table D2. Distribution of Wage Drift by Type of Contract National contract for employees of . N . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Non‐specified manufacturing firms 276 0.106 0.140 0.203 0.324 0.561 0.815 1.102 Small‐size manufacturing firms 180 0.116 0.146 0.194 0.290 0.509 0.715 0.833 Textile artisanal firms 972 0.090 0.112 0.168 0.252 0.427 0.649 0.805 Firms of the food industry 876 0.143 0.217 0.307 0.407 0.545 0.741 1.012 Firms of the shoe industry 333 0.101 0.149 0.214 0.351 0.565 0.801 1.082 Firms of the service sector 6,470 0.228 0.281 0.369 0.503 0.705 0.964 1.156 Co‐operative firms of the service sector 57 0.232 0.308 0.422 0.480 0.531 0.751 0.841 Firms of the leather industry 1,857 0.131 0.186 0.274 0.415 0.645 0.963 1.205 Firms of the construction sector 3,111 0.005 0.114 0.223 0.315 0.422 0.579 0.740 Small firms of the construction sector 706 0.061 0.130 0.262 0.381 0.490 0.603 0.706 Construction‐related artisanal firms 2,184 0.036 0.116 0.216 0.291 0.364 0.478 0.565 Firms of the toys and personal articles sector 144 0.124 0.144 0.217 0.319 0.431 0.699 0.868 Firms of the wood and furniture sector 1,595 0.113 0.151 0.201 0.267 0.362 0.519 0.673 Metal‐manufacturing and installation firms 6,311 0.175 0.232 0.327 0.463 0.663 0.929 1.212 Small metal‐manufacturing and installation firms 3,191 0.183 0.231 0.332 0.461 0.622 0.868 1.055 Artisanal metal‐manufacturing and installation firms 8,871 0.116 0.161 0.239 0.365 0.530 0.726 0.879 Firms providing environmental health services 68 0.198 0.218 0.350 0.591 0.852 1.021 1.196 Firms of the transportation sector 649 0.196 0.303 0.431 0.576 0.757 0.951 1.097 Firms providing professional services 160 0.226 0.342 0.544 0.918 1.216 1.647 2.180 Firms of the textile sector 322 0.136 0.159 0.218 0.330 0.463 0.796 1.058 Firms of the tourism sector 562 0.172 0.217 0.284 0.392 0.545 0.772 1.168 Total 38,895 0.125 0.179 0.271 0.397 0.579 0.822 1.028 National contract for employees of . N . Q05 . Q10 . Q25 . Q50 . Q75 . Q90 . Q95 . Non‐specified manufacturing firms 276 0.106 0.140 0.203 0.324 0.561 0.815 1.102 Small‐size manufacturing firms 180 0.116 0.146 0.194 0.290 0.509 0.715 0.833 Textile artisanal firms 972 0.090 0.112 0.168 0.252 0.427 0.649 0.805 Firms of the food industry 876 0.143 0.217 0.307 0.407 0.545 0.741 1.012 Firms of the shoe industry 333 0.101 0.149 0.214 0.351 0.565 0.801 1.082 Firms of the service sector 6,470 0.228 0.281 0.369 0.503 0.705 0.964 1.156 Co‐operative firms of the service sector 57 0.232 0.308 0.422 0.480 0.531 0.751 0.841 Firms of the leather industry 1,857 0.131 0.186 0.274 0.415 0.645 0.963 1.205 Firms of the construction sector 3,111 0.005 0.114 0.223 0.315 0.422 0.579 0.740 Small firms of the construction sector 706 0.061 0.130 0.262 0.381 0.490 0.603 0.706 Construction‐related artisanal firms 2,184 0.036 0.116 0.216 0.291 0.364 0.478 0.565 Firms of the toys and personal articles sector 144 0.124 0.144 0.217 0.319 0.431 0.699 0.868 Firms of the wood and furniture sector 1,595 0.113 0.151 0.201 0.267 0.362 0.519 0.673 Metal‐manufacturing and installation firms 6,311 0.175 0.232 0.327 0.463 0.663 0.929 1.212 Small metal‐manufacturing and installation firms 3,191 0.183 0.231 0.332 0.461 0.622 0.868 1.055 Artisanal metal‐manufacturing and installation firms 8,871 0.116 0.161 0.239 0.365 0.530 0.726 0.879 Firms providing environmental health services 68 0.198 0.218 0.350 0.591 0.852 1.021 1.196 Firms of the transportation sector 649 0.196 0.303 0.431 0.576 0.757 0.951 1.097 Firms providing professional services 160 0.226 0.342 0.544 0.918 1.216 1.647 2.180 Firms of the textile sector 322 0.136 0.159 0.218 0.330 0.463 0.796 1.058 Firms of the tourism sector 562 0.172 0.217 0.284 0.392 0.545 0.772 1.168 Total 38,895 0.125 0.179 0.271 0.397 0.579 0.822 1.028 Notes. The wage drift is defined as (wage‐contractual wage)/contractual wage. Contractual wages are bargained at the national level by sector and occupation category (typically five or more categories according to tasks performed and tenure). Open in new tab Appendix E. Basic Calculations of the Translation of EPL Costs on Wages We start by considering the situation of a employer‐initiated dismissal of a worker of average tenure in a small firm after the reform. If the dismissal is ruled unfair by the judge, the firing cost will range between 2.5 and 6 months (on average 16 weeks) of the last wage. On the basis of our data, the post‐reform average weekly wage amounts to approximately 313 euro. Therefore, the severance pay transferred to the worker amounts to 313 × 16 weeks = 5,008 euro, excluding the legal expenses that can be roughly calculated to be as much as 5,000 euro. The above computation results in a very high firing cost, but we should keep in mind that this is the worst possible scenario for the firm. Ex ante, the firm does not know with certainty whether the separation will be ruled unfair by the court. Furthermore, firms and workers may find a settlement out of court. Galdón‐Sánchez and Güell (2000), using data based on actual Italian court sentences, estimate both the probability of reaching an out‐of‐court agreement and the probability that the dismissal is ruled unfair to be around 0.5. If we assume that in case of an out‐of‐court agreement the employer pays approximately the same sum that would be paid in the form of severance pay, firms below 15 employees can expect a firing cost equal to 5,008 × 0.5 = 2,504 euro excluding legal expenses. If we assume a probability of 10% of the occurrence of individual firing for economic reasons during a typical employment relationship, the total expected cost ex ante for the employer is (5,000 + 2,504)/10 = 750.4 euro. Table D3. Veneto Workers History (VWH) and (Random 10%) Italian Social Security Administration (INPS) Archives . VWH . Italian sample . Veneto in the Italian sample . Real weekly wages 314.248 315.37 306.97 (82.199) (121.40) (98.76) Small‐firm dummy 0.642 0.69 0.66 (0.480) (0.46) (0.47) Age 36.904 35.99 34.86 (8.722) (9.50) (9.52) Firm size 13.133 12.76 13.09 (5.602) (5.70) (5.62) White‐collar dummy 0.144 0.20 0.14 (0.352) (0.40) (0.35) N 96,333 7,323 907 ISTAT Regional employment rate (males 25–64) 80.22 (2.88) . VWH . Italian sample . Veneto in the Italian sample . Real weekly wages 314.248 315.37 306.97 (82.199) (121.40) (98.76) Small‐firm dummy 0.642 0.69 0.66 (0.480) (0.46) (0.47) Age 36.904 35.99 34.86 (8.722) (9.50) (9.52) Firm size 13.133 12.76 13.09 (5.602) (5.70) (5.62) White‐collar dummy 0.144 0.20 0.14 (0.352) (0.40) (0.35) N 96,333 7,323 907 ISTAT Regional employment rate (males 25–64) 80.22 (2.88) Notes. The Italian sample is a random 10% sample of a data set drawn from the Italian Social Security Administration (INPS) archives. Employment rate is the average regional rate of employment of males aged 25–64 across 20 Italian regions over the period 1989–93 (ISTAT Regional accounts). Real wages expressed in 1995 euro. Standard deviations in parentheses. Open in new tab Table D3. Veneto Workers History (VWH) and (Random 10%) Italian Social Security Administration (INPS) Archives . VWH . Italian sample . Veneto in the Italian sample . Real weekly wages 314.248 315.37 306.97 (82.199) (121.40) (98.76) Small‐firm dummy 0.642 0.69 0.66 (0.480) (0.46) (0.47) Age 36.904 35.99 34.86 (8.722) (9.50) (9.52) Firm size 13.133 12.76 13.09 (5.602) (5.70) (5.62) White‐collar dummy 0.144 0.20 0.14 (0.352) (0.40) (0.35) N 96,333 7,323 907 ISTAT Regional employment rate (males 25–64) 80.22 (2.88) . VWH . Italian sample . Veneto in the Italian sample . Real weekly wages 314.248 315.37 306.97 (82.199) (121.40) (98.76) Small‐firm dummy 0.642 0.69 0.66 (0.480) (0.46) (0.47) Age 36.904 35.99 34.86 (8.722) (9.50) (9.52) Firm size 13.133 12.76 13.09 (5.602) (5.70) (5.62) White‐collar dummy 0.144 0.20 0.14 (0.352) (0.40) (0.35) N 96,333 7,323 907 ISTAT Regional employment rate (males 25–64) 80.22 (2.88) Notes. The Italian sample is a random 10% sample of a data set drawn from the Italian Social Security Administration (INPS) archives. Employment rate is the average regional rate of employment of males aged 25–64 across 20 Italian regions over the period 1989–93 (ISTAT Regional accounts). Real wages expressed in 1995 euro. Standard deviations in parentheses. Open in new tab Heckman and Pagés (2004) develop a measure of the expected present discounted cost to the firm, at the time a worker is hired, associated with severance payments to that worker in the future (they also take into account notice period, which is not of interest here). Adopting an analogous approach, we use the estimates in the study to compute the effect of severance payments on the expected present discounted value of wages calculated at the time of hiring. On the basis of our estimates in Table 2 (Column 4), the wage loss for an average worker (with average tenure 3.5 years) in a firm below the threshold of 15 employees after the reform (⁠ δ2^=−0.011 ⁠) amounts to about 3.4 euro per week (313 × 0.011) or approximately 179 euro per year. We use an annual discount rate of 8%, that is, a discount factor of β = 0.92. To match an average tenure of 3.5 years, we use an annual survival probability of ρ = 0.71. Let W be the present discounted value of the wage loss due to the reform W(δ2^|β,ρ)=179×∑t=0∞(βρ)t=516.1 ⁠. This implies that around 68.8% (516/750 = 0.688) of the expected firing cost is translated to lower wages. Footnotes 1 " Among the many articles in the literature on EPL and employment flows, only a few exploit the discontinuities in firing‐costs regimes that apply to firms of different sizes within countries: Boeri and Jimeno (2005) and Kugler and Pica (2008) on Italy; Bauer et al. (2007) on Germany. 2 " Although at the time of the reform, wages in Italy were set through a highly centralised bargaining process, there was still room left for firms to react to the law change because contractual minimum wages were in most cases hardly binding and an important component of workers’ compensation was determined at the firm and individual level in the form of company‐level wage increments, production bonuses and other variable benefits. Between one sixth and one quarter of the compensation was firm specific and half of Italian workers were involved in firm‐level negotiations in the period covered by our sample (Guiso et al., 2005). See Erikson and Ichino (1995) for further details on wage formation in Italy for the period covered by our data. 3 " Recent theory has highlighted the crucial role of wage‐determination mechanisms for the analysis of the employment effects of firing costs in matching models. On this, see especially Ljungqvist (2002), but also Garibaldi and Violante (2005) and Cahuc and Koeniger (2007) in this Journal’s Feature on EPL. 4 " Ljungqvist (2002) shows that this formulation is formally equivalent to assuming that the relative split of the surplus of the match is left unaffected by firing costs throughout the employment relationship. The equivalence arises because the wage profile under the Mortensen and Pissarides (1999) set‐up is homomorphic to new workers posting a bond equal to their share of any future expected firing costs, leaving unchanged the expected present value of workers’ total compensation. Alternatively, firing costs may be assumed to weaken the firm’s threat point from the first negotiation with a newly hired worker, thereby increasing the worker’s relative share of the surplus of the match. In this case, workers become insiders – and extract the associated rents – since the first encounter with the firm and suffer no wage losses. 5 " Lindbeck and Snower (1988) reject the plausibility that firms can make outsiders fully pre‐pay the EPL cost via a lower wage for a number of reasons that limit the downward flexibility of wages, such as the presence of minimum wages. This implies that firms will fail to translate the entire costs of EPL on workers. We will return to this issue in Section 6.. 6 " Labour codes also limit trial periods – that is, the period of time during which a firm can test and dismiss a worker at no cost (in Italy 3 months) – and mandate a minimum advance notice period prior to termination (1 month). Differently from open‐ended contracts, temporary contracts can be terminated at no cost provided that the duration of the contract has expired. 7 " Severance pay for unfair dismissals ranged between 5 and 8 months for workers with less than two and a half years of tenure, between 5 and 12 months for those between two and a half and 20 years of tenure and between 5 and 14 months for workers with more than 20 years of tenure in firms with more than 60 employees. 8 " The law prescribes that the 15‐employee threshold should refer to establishments rather than firms. Although in our data we only have information at the firm level, this is unlikely to be a concern because in the empirical analysis we focus on firms with between 5 and 25 employees that are plausibly single‐plant firms. 9 " The average establishment size in Veneto is 13 employees. Half of the employment stock is not subject to protection against dismissal as stated by art. 18 of the Statuto dei Lavoratori. Typical manufacturing activities are garments, mechanical goods, goldsmiths, leather, textile, furniture and plastics. The stock of manufacturing workers in the two Veneto provinces of Treviso and Vicenza has varied between 194,000 employees in the early 1980s and 233,000 employees in 1996, with a yearly positive average rate of variation of 1.4%. The average rate of growth in employment is the result of a marked increase in white collar and women (Tattara and Valentini, 2005). 10 " The labour code computes the 15‐employee threshold in terms of full‐time equivalents rather than in terms of heads. In particular, it excludes from the threshold’s calculation apprentices and temporary workers below 9 months, and includes part‐time workers and all other temporary contracts in proportion to their actual time worked during the week. For this reason, firm size is computed as the average number of employees weighted by the number of worked months in the firm during the year. 11 " Bank of Italy survey data (SHIW) indicate that in 1989 the private sector constituted 52% of total employment of males aged 20–55; agriculture represented only 2% while public employment and self‐employment represented 23% each. The vast majority of private sector workers do not move out of private sector employment: after 2 years, 83% of males aged between 20 and 55 employed in the private sector in 1989 were still private sector workers; 6.7% move to the public sector, only 2.3% to self‐employment and to agriculture and 5.7% become unemployed or retire early. These figures are stable over time and transition rates for different years are very similar. 12 " Selection issues make the analysis on Italian women difficult. The female employment rate in Italy over our sample period (1989–93) was a very low 35%. Olivetti and Petrongolo (2008) document that in countries in which female employment rates are low, only high‐productivity females self‐select into employment. A further and more serious selection problem may be induced by the reform itself. Prifti and Vuri (2011) find large effects of the 1990 EPL reform on fertility and female labour market participation after childbearing in small firms below the 15‐employee threshold. Adserá (2004) documents that unstable employment relationships depress fertility and Bratti et al. (2005) find that Italian women who enjoy a greater amount of employment protection have a higher incentive to return to work in the three years following childbirth. 13 " Another possible adjustment margin is through hours, which we partially address by looking at weekly wages. Yet another margin – outside the scope and the data availability of this study – is investment (Cingano et al., 2010): stricter EPL may induce firms to substitute rigid labour with capital and raise the capital‐labour ratio. It is noteworthy that EPL seems to have small or no threshold effects on the firm size distribution also in Germany, where a 10‐employee threshold applies (Wagner et al., 2001; Bauer et al., 2007). 14 " For clarity reasons, the Figure uses only the pre‐reform year 1988, while the actual first stage in (1) uses both 1988 and 1987. The corresponding first‐stage equations – one for the main effect DjtS and one for the interaction DjtS×Post – are presented in Table B1 and discussed in Appendix B. 15 " Notice that this test also gives insights on whether other (unobserved) policies differentially affect small and large firms since 1990. Although we cannot directly test this identifying assumption, we can investigate whether firms’ observable characteristics have discontinuities at the threshold after 1990. Results in Table A2 (Appendix A.2) are also suggestive that the effect of the change in EPL is unlikely to be confounded with the effect of another policy that depends on firm size and shares the same threshold. 16 " In addition, to check whether the reform of collective dismissals of 1991 (which is a potential confounder of our results, as explained in Section 1.2.) is behind the negative coefficients on wages estimated in Table 2, we augment the baseline specification of (1) with a post‐1991 reform dummy and its interaction with the small‐firm dummy. Contrary to what one would expect if the 1991 reform was driving our findings, results show that the interaction term with the post‐1991 reform dummy is not significant, while the interaction term between the post‐1990 reform dummy and the small‐firm dummy remains negative and significant. Kugler and Pica (2008) also empirically distinguish the 1990 and the 1991 reforms and conclude that the latter reform has no differential effect over and above that of the 1990 reform. Paggiaro et al. (2009) examine aspects of the 1991 law concerning active labour market policies and find limited effects only on workers aged 50+. 17 " Notice that in Appendix A.2 we analyse the probability of workers moving from firms below the threshold to larger firms above the threshold (and vice versa) conditional on moving, while Table D1 reports the unconditional proportion of job changes. 18 " The contracts for firms in the insurance sector and in co‐operative firms in the construction sector cover only a very small number of workers in the sample (10 and 17 observations) and have been dropped. 19 " The magnitude of the effect on log wages is, at the median, of the same order of magnitude as the average effect found in the IV model with worker fixed effects (Table 2, column 4). As a further check, we estimate the benchmark fixed effects (1) augmented with a pre‐reform low‐wage dummy and all relevant interactions. 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Comments from seminar participants at the University of California at Berkeley, Boston College, Georgetown University, Queen Mary University of London, University of Milan, University of Salerno, University of Padova, University of Venezia, the Fifth IZA/SOLE Transatlantic Meeting, the 7th ECB/CEPR Labour Market Workshop are also gratefully acknowledged. We thank Giuseppe Tattara and Marco Valentini for providing us with the VWH (Veneto Workers History) data set (Miur Projects 1999–2001 #9913193479 and 2001–2003 #2001134473) and Bruno Contini of the LABORatorio Riccardo Revelli for providing us with a sample of the INPS data set. Giovanni Pica gratefully acknowledges support from the University of Salerno grant programme ‘High Performance Computing – HPC – prot. ASSA098434, 2009’ and from the Europlace Institut of Finance (Project: Finance and Labour, 2011). The usual disclaimer applies. © 2013 The Author(s). 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Who Pays for it? The Heterogeneous Wage Effects of Employment Protection Legislation

The Economic Journal , Volume 123 (573) – Dec 1, 2013