TY - JOUR
AU - Leonardi,, Marco
AB - Abstract In this paper, we estimate the causal effects of the 2003 reforms to the Italian apprenticeship contract that increased its legal length, allowed on-the-job training and introduced a minimum floor to apprentices’ wages. Using administrative data, we implement a covariate balancing propensity score and a difference-in-differences estimator. We find that the new contract improves the chances of an apprentice obtaining a permanent job in the same firm five years after hiring; however, this occurs more frequently in large firms. We also find sizeable, long-run wage effects that extend well beyond the legal duration of the apprenticeship contract. These effects are compatible with increased human capital accumulation, possibly due to the reformed training provisions. 1. Introduction Many countries facing high youth unemployment seek to improve their vocational education and training (VET) systems to ease the transition between school and work (Quintini and Martin, 2006). An apprenticeship contract is one of the most popular features of many VET systems: apprentices receive vocational training to enhance their professional skills, while employers are compensated with reduced payroll taxes and lower wage costs. The apprenticeship regime is heavily regulated by governments and social partners, and its implementation has taken different forms across Europe (Eichhorst et al., 2015). In some countries, such as France, the apprenticeship is integrated into the education system, and consists of theoretical training in schools and certified institutions. Several German-speaking countries (Germany, Austria, Switzerland, and Denmark) implement a ‘dual system’ that not only integrates the apprenticeship contract into the education system, but also emphasizes on-the-job training. In other countries, including Italy, the apprenticeship regime is contiguous with formal education; it is not considered an extension of the education system but, rather, an employment contract with a strong training requirement, which is set by collective agreements and regional governments. In international comparisons, the dual system seems more effective than its counterparts at helping youth transition into employment, as it supports more rapid integration into the labour market. The dual system ensures a high level of on-the-job training and requires significant employer involvement. Apprentices in the dual system are also paid. Finally, all training curricula in the dual system are accredited by a central body, ensuring transparency and acceptance of the training among employers (Fersterer et al., 2008; Pischke and von Wachter, 2008; Dustmann and Schönberg, 2009; Parey, 2009). Many countries have therefore tried to revise their apprenticeship regimes by modelling the successful dual systems of German-speaking countries (Woessmann, 2008; Hogarth et al., 2009).1 This paper analyses the effects of important reforms made to the apprenticeship system in Italy in 2003. Law 30/2003 revised the training component of the apprenticeship. Before the reforms, all training (typically 40 annual hours in basic competencies and 80 annual hours in technical competencies) was formal and to be undertaken in specific regional schools. Following the reforms, technical training could also be undertaken on the job. This on-the-job training provision was inspired by the dual system, in which training is divided between school and work. Its goals were twofold: to foster a connection between employers and apprentices, and to reduce the bureaucratic requirements faced by the firms that administer external training. The reforms also introduced other changes, including a minimum wage and an extension of the apprenticeship contract’s legal length. In this paper, we explore the effects of these reforms on labour market outcomes for apprentices. The existing research studies these effects by comparing apprenticeship outcomes with those of students or other temporary workers. We contribute to the literature by, instead, basing our estimates on a comparison between apprenticeship systems: the ‘old’ and the ‘new’ apprenticeship contracts. This method reduces the problems associated with the issue of selection into treatment. The empirical literature on Italy’s transition to open-ended apprenticeship contracts is scarce and shows ambiguous effects. Berton et al. (2011) found that other temporary contracts outperformed the apprenticeship contract in terms of transformation rates (i.e. the conversion of the contracts into open-ended contracts) between 1998–2004. Conversely, Picchio and Staffolani (2019) found the opposite result for workers aged 30 (the age threshold for the apprenticeship contract) between 2009–12. The effects of the 2003 reforms on apprentices’ employment prospects have not yet been studied. We contribute to the literature by providing evidence of these effects.2 For identification, we exploit the contemporaneous presence of two different apprenticeship contracts, which came about as a result of the staggered implementation of the reforms across regions and industries. The reforms were gradually introduced because specific regulations and collective bargaining agreements were required to define the training component of apprenticeship before the law could come into effect. To estimate the average treatment on the treated (ATT), we compare (across regions and industries) employment and wage trajectories of apprentices hired under the two different regimes in 2007. Thanks to rich administrative panel data, we can trace the effects of the reforms for a seven-year period, which extends well beyond the legal duration of apprenticeship contracts (usually between three and five years). In order to identify the causal effects of the reforms, we deploy two analytical strategies that hinge on different sets of assumptions. Our main estimating approach relies on a covariate balancing propensity score estimator (CBPS) and the conditional independence assumption (CIA) to control for differences in composition among the apprentices under the two regimes. We address the validity of this strategy via a sensitivity analysis of confounders (Rosenbaum, 2002), which highlights the relatively large magnitude required of any potential confounder that could invalidate the results. To assess the robustness of findings from the CBPS analysis, we resort to a difference-in-differences estimator, which is robust to selection bias under the parallel trend assumption. We find that the reforms reduced the apprentice dropout rate during the first year and increased the rate of transformation into open-ended contracts. We estimate substantial effects in firms with more than 10 employees: during the first year of apprenticeship, the dropout rate decreased by 21.1% and the transformation rate to open-ended jobs within the same firm after four years increased by 39.7%. Consistent with a pattern of higher job stability, we also find positive long-term effects on wages. While we are, in general, unable to disentangle which of the various elements of the reforms were the most effective, we argue that on-the-job training is an important driver of the results. The paper is structured as follows: Section 2 describes the apprenticeship contract and the changes introduced by Law 30/2003. In Section 3, we describe the dataset, and Section 4 presents the identification strategy. Results and robustness tests are shown in Section 5, and Section 6 provides concluding remarks. 2. Institutional background In this section, we describe the Italian apprenticeship regime. We first detail the main characteristics of the apprenticeship contract during the period of analysis, after which we highlight the changes introduced by Law 30/2003. Traditionally in southern European countries, the role of apprenticeships (and vocational training, in general) in the education-to-labour market transition of youth has been marginal, both because employers prefer to hire workers on fixed-term contracts, for which there is no need for formal vocational training, and because families have a strong preference in favour of academic education (e.g. Eichhorst et al., 2015). Apprenticeship contracts were introduced in Italy in the 1950s, with eligibility requirements based solely on the worker’s age. They are recognized as full employment contracts that are completely separate from schooling.3 Only private sector firms may use apprenticeship contracts, and the maximum number of apprentices in a firm must be fewer than the number of employees. However, firms with fewer than three employees may hire up to three apprentices. The probationary period is two months at most, after which apprentices may only be laid off for just cause. From 2009, apprentices dismissed for economic reasons with three months’ seniority have been entitled to unemployment insurance for 90 days (Law 2/2009). Through the apprenticeship contract, employers provide training to employees in exchange for the receipt of payroll tax rebates and the ability to pay lower wages. Employers’ Social Security contributions (SSCs) are reduced to 10% of the apprentices’ gross earnings, instead of the standard 27% for regular employees. There are further incentives for firms with fewer than 10 employees, including an almost complete exemption of social security contributions for the first two years of the apprenticeship.4 Furthermore, the payroll tax rebates are extended for a further year in the event that an apprenticeship transforms into an open-ended contract (Law 56/1987). Lower wage costs are defined by collective bargaining agreements (CBAs), which are typically industry-specific at the national level. Employers must appoint an internal advisor as a mentor (and, sometimes, a trainer) for the apprentice; this mentor may counsel up to five apprentices. Firms choose the training courses that apprentices will follow from a region-specific list. In the period of our analysis, the training component of the contract amounted to 120 hours per annum, of which 40 hours of training, usually financed by the regional government, were spent on basic skills, including labour laws, work organization, and safety regulations. The remaining hours covered job-specific technical competencies and were paid for by the employers. 2.1 Differences introduced by Law 30/2003 Before the 2003 reforms, the eligibility at hiring was 16–24 years,5 the possible duration of the apprenticeship contract was between 18 months to four years (five in the craft sector), and training could be provided only by external authorities certified by the regional governments. Law 30/2003 introduced several changes to the regime, which was then labelled ‘Vocational Apprenticeship’ (see Table 1). First, the Law liberalized the training component; firms who were able to provide specific training competencies, infrastructures, and tutors to their apprentices could now deliver on-the-job training. Usually, on-the-job training covered the technical–professional competencies; however, some regions and CBAs permitted basic training to be performed on-the-job as well, albeit under stricter rules (ISFOL, 2010).6 Second, the Law introduced a minimum wage for apprentices, establishing that their compensation could not be lower than two grades on the pay scale of the occupation for which the apprentices were qualifying. Third, the reforms set the contract duration between two and six years, although the CBAs usually remained at the lower end of the range.7 Finally, the Law raised the upper age limit at hiring to 29, to incentivize the use of the contracts.8 Table 1 Changes in the apprenticeship regime introduced by the 2003 reform Pre-reform Post-reform Maximum age at hiring ≤24 (29 in some exceptions) ≤29 Training External authorities External but also internal if the firm has training capabilities Maximum and minimum contract length 1.5–4 years (5 years in craft sector) 2–6 years (De facto 33–56 months) Wage Set by the collective bargain agreements Minimum wage to the remuneration the collective bargain agreements could set Pre-reform Post-reform Maximum age at hiring ≤24 (29 in some exceptions) ≤29 Training External authorities External but also internal if the firm has training capabilities Maximum and minimum contract length 1.5–4 years (5 years in craft sector) 2–6 years (De facto 33–56 months) Wage Set by the collective bargain agreements Minimum wage to the remuneration the collective bargain agreements could set Source: Law 30/2003. Open in new tab Table 1 Changes in the apprenticeship regime introduced by the 2003 reform Pre-reform Post-reform Maximum age at hiring ≤24 (29 in some exceptions) ≤29 Training External authorities External but also internal if the firm has training capabilities Maximum and minimum contract length 1.5–4 years (5 years in craft sector) 2–6 years (De facto 33–56 months) Wage Set by the collective bargain agreements Minimum wage to the remuneration the collective bargain agreements could set Pre-reform Post-reform Maximum age at hiring ≤24 (29 in some exceptions) ≤29 Training External authorities External but also internal if the firm has training capabilities Maximum and minimum contract length 1.5–4 years (5 years in craft sector) 2–6 years (De facto 33–56 months) Wage Set by the collective bargain agreements Minimum wage to the remuneration the collective bargain agreements could set Source: Law 30/2003. Open in new tab The reforms were not immediately effective. The Law was enacted by Legislative Decree 276/2003 of 10 September 2003. However, since Italian regions were given exclusive jurisdiction of vocational training, regional governments retained a high degree of autonomy in the implementation of the Law. Regional governments only began implementing the law through specific regional regulations in 2005, as they were not immediately ready to revise the menu of training courses offered. Several regions preferred to implement pilot tests in specific sectors before fully implementing the reforms; these sectors included tourism in Lazio and retail trade in Lazio, Lombardy, Umbria, and Marche. As shown in Fig. 1, the regions that enacted regulations to enable the official implementation of the reforms were Tuscany, Emilia, Marche, Friuli Venetia Giulia, and Sardinia in 2005; Lazio, Trentino Alto Adige, Puglia, and Basilicata in 2006; Piedmont, Umbria, and Lombardy in 2007; Molise in 2008 and Campania, Veneto, Liguria, and Abruzzi in 2009. Fig. 1 Open in new tabDownload slide Timing of regional implementation of the reform until the 1st quarter of 2011 Source: ISFOL (2006, 2007, 2010, 2013). Fig. 1 Open in new tabDownload slide Timing of regional implementation of the reform until the 1st quarter of 2011 Source: ISFOL (2006, 2007, 2010, 2013). However, the implementation of the reforms often happened through CBAs rather than regional laws because, in practice, the new regime was effective only after a CBA also updated the sector’s training programmes (ISFOL, 2007). Furthermore, to speed up the implementation process, the government also allowed the CBAs to enact the new regime officially in the absence of a regional regulation (Law 80/2005). The most important CBAs to have renewed apprenticeship training since 2005 have been in the following sectors: retail and wholesale trade, chemicals, construction, tourism, transport, financial services, energy, rubber, textile, and metal manufacturing and metallurgy. The implementation of the reforms varied by region, sector, and time (see Table 3A of online Appendix A). Due to this staggered implementation, two different apprenticeship contracts co-existed between 2005 and 2011.9 Furthermore, firms could not freely decide which contract to use; the contract was determined by the specific regulations of the sector and region of activity at the time of hiring.10 Importantly, the reforms applied only to newly-signed contracts; converting old contracts into new ones was not allowed. These limitations were explicitly set to prevent firms from dismissing an old-regime apprentice and replacing them with a new one. Although the rules were clear in principle, there was still a degree of uncertainty among employers as to which of the two apprenticeship contracts should be applied (for instance, many firms operated in different regions or under different CBAs). This confusion resulted in an incomplete overlap between firm eligibility and apprentice assignments under the new regime. 3. Data and descriptive statistics To estimate the effect of the reforms on apprenticeship outcomes, we use administrative data derived from social security registers made available by the Italian Social Security Institute (INPS). The overall administrative sample available for research purposes has a longitudinal structure covering 6.5% of all individuals registered with the INPS. The data report individual employment histories in the salaried private sector (e.g. remuneration, working days, contract type, starting and ending dates), as well as the receipt of unemployment benefits. The data contain information about the firm (e.g. its size, sector), as well as individual characteristics of its employees (e.g. age, gender, region of work), but does not include information about the individuals’ education. As of 2007, the INPS data also record the regime under which new apprentices were hired: the ‘old’ contract or the ‘new’ one introduced by Law 30/2003. We select an inflow sample of individuals who began a period of apprenticeship in 2007 and follow them at a monthly frequency for the subsequent seven years, until the end of 2014. We choose only individuals aged 19–24 at the beginning of the apprenticeship contract, because younger individuals were not eligible for the new apprenticeship and older persons were eligible for the old regime only in special cases. This allows us to exclude the channel of higher age eligibility in the interpretation of our results. The selection rule generates a sample of 17,948 individuals. Of those, 7,204 apprentices were hired under the old regime, and 10,744 were hired under the new regime.11 Since apprenticeships usually have a maximum duration of five years, we observe individual trajectories for at least an additional two years after the end of the contract. Of course, not all apprentices complete the maximum duration; many terminate the contract earlier and move to other forms of employment (or non-employment). Figure 2 plots the rate at which our 2007 inflow sample remain in the apprenticeship contract. We observe that 19% of apprentices exit the contract within the first two months of the probationary period; 51% terminate the contract after the third month and before the contract’s second year; and 30% remain longer. All apprenticeship contracts are terminated at the end of our observation period and, as shown in Fig. 2, the hazard rate displays two spikes, at month 36 and month 48 (which are both normal contract durations, according to most CBAs). Fig. 2 Open in new tabDownload slide Survivor function in the initial apprenticeship Note: Inflow sample of 17,948 apprentices hired in 2007 aged 19–24. Fig. 2 Open in new tabDownload slide Survivor function in the initial apprenticeship Note: Inflow sample of 17,948 apprentices hired in 2007 aged 19–24. Table 2 displays employment transitions differentiated by year and destination for the apprentices hired in 2007. The statuses we consider are the share of youth: (1) remaining in the apprenticeship in the initial firm; those transiting to (2) an apprenticeship in another firm, (3) a permanent job in the initial firm, or (4) another firm, (5) a temporary contract, (6) a collaborator contract, or (7) insured unemployment; and, finally, those (8) exiting our database (i.e. neither in salaried employment in the private sector, nor in insured unemployment). The proportion of youth remaining employed in the salaried private sector decreases over time; at the end of the seventh year, 56% are still employed (the sum of the last row of columns 1–6). At the end of the seventh year, about 39% of apprentices have an open-ended contract (14% within the same firm and 25% in another firm), 5% have a different apprenticeship contract in another firm, 11% have a temporary contract, and 1% are external collaborators. Finally, 4% of the individuals earn unemployment benefits and almost 40% are no longer in our database.12 Table 2 Labour market status over time (%) Year (end) (1) Appr. initial firm (2) Other appr. (3) Open-ended same firm (4) Open-ended other firms (5) Temporary (6) Collaborator (7) Unemployed (8) Out-of-database 1 48.7 9.9 1.5 4.1 8.4 1.0 0.1 26.2 2 32.3 13.3 3.8 7.5 9.0 1.2 0.6 32.2 3 20.3 13.3 7.9 11.3 10.3 1.3 1.2 34.3 4 8.4 11.2 14.0 16.4 11.6 1.4 1.8 35.1 5 1.9 8.5 16.6 20.7 11.2 1.4 2.4 37.2 6 0.5 6.5 15.6 23.5 9.9 1.1 3.5 39.4 7 0.3 5.4 14.0 25.0 10.1 1.2 4.4 39.7 Year (end) (1) Appr. initial firm (2) Other appr. (3) Open-ended same firm (4) Open-ended other firms (5) Temporary (6) Collaborator (7) Unemployed (8) Out-of-database 1 48.7 9.9 1.5 4.1 8.4 1.0 0.1 26.2 2 32.3 13.3 3.8 7.5 9.0 1.2 0.6 32.2 3 20.3 13.3 7.9 11.3 10.3 1.3 1.2 34.3 4 8.4 11.2 14.0 16.4 11.6 1.4 1.8 35.1 5 1.9 8.5 16.6 20.7 11.2 1.4 2.4 37.2 6 0.5 6.5 15.6 23.5 9.9 1.1 3.5 39.4 7 0.3 5.4 14.0 25.0 10.1 1.2 4.4 39.7 Notes: Inflow sample of 17,948 apprentices hired in 2007 aged 19–24. Status at the end of the year after hiring in %: (1) apprenticeship in the first firm, (2) other apprenticeship, (3) open-ended contract in the same firm, (4) open-ended contract in another firm, (5) other temporary contract, (6) collaborator, (7) insured unemployed, (8) not in salaried employment in the private sector. Individuals with more jobs are considered only in one position following the order of the columns. Source: Authors’ calculations. Open in new tab Table 2 Labour market status over time (%) Year (end) (1) Appr. initial firm (2) Other appr. (3) Open-ended same firm (4) Open-ended other firms (5) Temporary (6) Collaborator (7) Unemployed (8) Out-of-database 1 48.7 9.9 1.5 4.1 8.4 1.0 0.1 26.2 2 32.3 13.3 3.8 7.5 9.0 1.2 0.6 32.2 3 20.3 13.3 7.9 11.3 10.3 1.3 1.2 34.3 4 8.4 11.2 14.0 16.4 11.6 1.4 1.8 35.1 5 1.9 8.5 16.6 20.7 11.2 1.4 2.4 37.2 6 0.5 6.5 15.6 23.5 9.9 1.1 3.5 39.4 7 0.3 5.4 14.0 25.0 10.1 1.2 4.4 39.7 Year (end) (1) Appr. initial firm (2) Other appr. (3) Open-ended same firm (4) Open-ended other firms (5) Temporary (6) Collaborator (7) Unemployed (8) Out-of-database 1 48.7 9.9 1.5 4.1 8.4 1.0 0.1 26.2 2 32.3 13.3 3.8 7.5 9.0 1.2 0.6 32.2 3 20.3 13.3 7.9 11.3 10.3 1.3 1.2 34.3 4 8.4 11.2 14.0 16.4 11.6 1.4 1.8 35.1 5 1.9 8.5 16.6 20.7 11.2 1.4 2.4 37.2 6 0.5 6.5 15.6 23.5 9.9 1.1 3.5 39.4 7 0.3 5.4 14.0 25.0 10.1 1.2 4.4 39.7 Notes: Inflow sample of 17,948 apprentices hired in 2007 aged 19–24. Status at the end of the year after hiring in %: (1) apprenticeship in the first firm, (2) other apprenticeship, (3) open-ended contract in the same firm, (4) open-ended contract in another firm, (5) other temporary contract, (6) collaborator, (7) insured unemployed, (8) not in salaried employment in the private sector. Individuals with more jobs are considered only in one position following the order of the columns. Source: Authors’ calculations. Open in new tab If we split the sample by apprenticeship regime, we observe noteworthy differences. As shown in Figure 1A in online Appendix A, apprentices in the new regime tend to transit to open-ended contracts from the fourth year onwards, especially within the same firm. Apprentices in the old regime more often move to temporary contracts and other apprenticeships. An important share of apprentices in the old regime moves out of our database in the first few months. For these youths, we observe cyclical patterns for both the share of out-of-database youth and the share of temporary contracts, indicating some sort of seasonal work. This phenomenon is probably caused by the implementation of the reforms by CBAs, which saw some sectors, such as tourism, postponing the reforms. 4. Analytical framework 4.1 Expected effects of the reforms on contract transformation We use basic economic intuition to outline the expected effects of the reforms on the transformation rate of apprentice contracts. Employers hire apprentices if the reduction in labour costs is larger than the combined training costs, both direct (e.g. trainer fees, organization of classes, materials) and indirect (e.g. opportunity cost in terms of production for apprentices and internal tutors). In this calculation, firms also take into account the degree of increase in apprentice productivity by the end of training. We expect that firms transform an expiring apprenticeship contract into a permanent contract if the apprentice’s productivity gain is greater than the increased costs of their permanent employment; namely, an increase in labour costs and the (potential and discounted) firing cost which could result from the presence of stringent employment protection legislation (EPL). If the firm determines that the productivity gain does not outweigh the additional costs, the apprenticeship contract could encourage a churning behaviour (i.e. the consistent substitution of one apprentice with another without promoting the first to a permanent job). In these cases, firms prefer hiring apprentices merely as a form of cheap and flexible labour.13 By setting a minimum wage for apprentices, the 2003 reforms should increase contract transformations by reducing the cost-saving advantage of churning. The reforms allow on-the-job training in lieu of external training, creating uncertain effects on firms’ training costs. On one hand, it introduces organizational costs for employers willing to deliver on-the-job training; on the other hand, organizing internal training may be cheaper than the external training fees and may also reduce the bureaucracy of external training administration. Finally, on-the-job training could positively affect the productivity gain of youth at the end of the apprenticeship due to more firm-specific human capital accumulation. Thus, we expect more transformations of apprenticeship contracts under the new regime. 4.2 Empirical strategy We are interested in the effects of the new apprenticeship contract on the labour market outcomes of individuals who started a new apprenticeship regime in 2007 relative to the counterfactual case in which they would have been hired under the old regime. We estimate the average treatment effect on the treated in a specific month, t, after hiring to be: ATTt=E[Yit1−Yit0|Di=1] (1) where Di is a binary treatment dummy indicating whether, at t = 0, the apprentice, i, is hired under the new apprenticeship contract (⁠ Di = 1) or under the old contract (⁠ Di = 0). The potential outcomes of apprentice i at time t in case of treatment (i.e. the new regime) is Yit1 ⁠, while Yit0 is the potential outcome without treatment (i.e. the old regime). 4.3 Covariate balancing propensity score As mentioned in the Introduction, comparing two different apprenticeship regimes reduces the selection problem relative to most of the literature, which compares the employment outcomes of apprentices with a control group of students (those on the academic education track or other VET tracks) or workers in other contracts. However, as shown in Table 1A in online Appendix A, the apprentices hired under the two regimes still differ in several characteristics. Because of the implementation by means of CBAs, the most noticeable difference is their concentration in certain sectors and firms of a particular size; those with new contracts gravitate towards wholesale, retail trade, business services, construction, and larger firms, while those with old contracts are concentrated in food, tourism, personal services, and smaller firms. To limit these remaining selectivity issues, we rely on the CIA; we overcome the problem of selection into treatment by replacing counterfactuals with the outcomes of an appropriate control group. The control group’s members are identical to the treated units in all relevant characteristics that affect the outcome in the absence of the treatment. We use the apprentices hired under the old scheme to form the control group, and implement an estimator on the observables to ensure that the treated units and controls are comparable. More specifically, we apply the inverse probability weighting estimator (IPW; see, e.g., Hirano et al., 2003), which weights control units based on the odds of receiving treatment given their observable characteristics. This is represented as: ATTtIPW=∑iDiYitN1-∑i1-DiwiYitN0 (2) where N1 is the number of treated units and N0 is the number of control units in our sample; wi=π(Xi)∑iπ(Xi)(1-Di)/N0 is the (normalized) weight for control units; πXi=p(Xi)1-p(Xi) is the odds ratio of the treatment given the covariates Xi ⁠; and p(Xi) is the propensity score. The IPW uses the outcomes of controls in place of the unobservable outcomes of the treated in the counterfactual scenario of no treatment; it also gives more weight to control units that, based on their characteristics, have a higher predicted odds ratio of being treated. To mitigate potential consistency issues arising from model misspecification in the estimation of the propensity score (which is common when the number of X covariates is large), p(Xi) is estimated by implementing the CBPS proposed by Imai and Ratkovic (2014). According to the empirical simulations of Frölich et al. (2017), the CBPS estimator was, overall, the best-performing semi-parametric estimator on the observables. This estimator works in a similar way to the IPW but, instead of estimating p(Xi) by using a logit or probit model, it uses a generalized method of moments (GMM) estimator the objective function of which consists of the first-order conditions (i.e. expected score equal to zero) and the balancing of the covariates. More details on the CBPS estimator are available in online Appendix B. The validity of identification rests on the CIA. In other words, after controlling for the propensity score, the potential outcome in the absence of treatment (⁠ Yt0) should be orthogonal to the treatment assignment:14 Yt0⊥D|p(X) (3) with the set of covariates Xi ⁠, which are used to predict the propensity score, being key in this respect. We include in the model a long list of covariates related to labour market outcomes. First, because the availability of the new apprenticeship regime depended on a firm’s characteristics, we control for detailed information such as region, industry, size, belonging to a corporate group, and calendar quarter of hiring. Second, new rules for the apprenticeship about the minimum wage, minimum duration, and training could induce firms to change the type of individuals hired for an apprenticeship. This could make the treated and the controls different in terms of potential outcome Yt0 ⁠. To ensure a similar composition between the two groups, we control for demographic characteristics (age and gender) and for a long list of labour market characteristics related to individual productivity. Therefore, we include information about each individual’s entire employment history in the salaried private sector (experience; age at first hire; average full-time remuneration; share of working time by occupation, contract, and firm size; part-time experience; number of jobs; length of non-employment before the apprenticeship; a dummy equal to 1 if the individual had experienced a period of insured unemployment); and further details for an individual’s most recent job (type of contract, gross remuneration, reason for ending the contract, part-time status, length of contract, and industry).15 While we cannot exclude the possibility that the composition of the two groups may differ in other dimensions, we argue that remaining differences are of a second order. For example, our administrative data have no information on educational attainment; however, previous salaries, qualification (blue- or white-collar), experience, and age in their first job provide a good approximation of the apprentices’ stock of human capital. Furthermore, since we condition on detailed labour market histories, which in our setting can be considered lagged dependent variables, our covariates can account for time-invariant, unobserved heterogeneity related to the outcomes of interest (Imbens and Wooldridge, 2009). 5. Results 5.1 Covariate balancing propensity score Estimates of the propensity score show that the likelihood of being hired under a new apprenticeship contract varies according to the characteristics of the firm (industry and size), but varies less so according to the characteristics of the worker (e.g. type of last job and past employment history), suggesting that the composition of individuals hired under an apprenticeship did not significantly change after the implementation of the reforms (Table 2A in online Appendix A). The regional dummies’ lack of significance confirms that the main implementation channels for the reforms were CBAs, rather than regional regulations. Since lack of overlap of the propensity score can also bias the estimates and increase the variance (e.g. Lechner and Strittmatter, 2019), we trim the treated units with a propensity score above the 99.9 percentile of the control units, leaving us with about 98% of the treated units. As shown in Figure 2A in online Appendix A, the trimming removes the thinnest part of the distribution.16 Diagnostic tests show that the estimator behaves well in balancing covariates across treated and control units. Despite the many covariates, the CBPS performs remarkably well in balancing their distribution. The median standardized bias (SB) is as low as 0.7% and the highest SB is 3.2%; the pseudo R-squared of the reweighted sample is 0.001, and the log-likelihood ratio test for the joint significance of the variables after the reweighting produces a p-value of 1.17 The balancing tests are better than those obtained by the standard logit model (IPW). IPW weights generate a median SB of 2.2%; the highest SB is 11.3%, the pseudo-R2 of the reweighted sample is 0.012, and the p-value of the log-likelihood ratio test is 0. We show the full list of balancing tests by CBPS weights in Table 1A in online Appendix A.18 5.1.1 Effects of the new apprenticeship on employment Our results are generated by estimating, at a monthly frequency, the effects of the new apprenticeship policy on labour market trajectories in the seven years after the apprentice was hired. We consider nine non-mutually exclusive19 labour market statuses in each month (⁠ Yit ⁠) for the apprentices hired in 2007: employee, apprentice with the initial firm, apprentice with another firm, permanent employee, permanent employee with the initial firm, permanent employee with another firm, temporary employee, unemployment benefits recipient, and not in the database (which includes self-employment, participation in the public sector, enrolment in education, uninsured unemployment, and inactivity). We show the estimated effects graphically in Fig. 3.20 Fig. 3 Open in new tabDownload slide ATT on the apprentices in the seven-year period 2007–14 Note: ATT estimated by CBPS estimator of the reformed apprenticeship versus the old apprenticeship on a sample of 16,805 apprentices hired in 2007 aged 19–24 (after trimming). Status is as at the end of each month after hiring. Bootstrapped standard errors (199 repetitions) clustered by individual to take into account serial correlation. Fig. 3 Open in new tabDownload slide ATT on the apprentices in the seven-year period 2007–14 Note: ATT estimated by CBPS estimator of the reformed apprenticeship versus the old apprenticeship on a sample of 16,805 apprentices hired in 2007 aged 19–24 (after trimming). Status is as at the end of each month after hiring. Bootstrapped standard errors (199 repetitions) clustered by individual to take into account serial correlation. Overall, the new apprenticeship has a positive effect on employment of about 2 percentage points (p.p.) throughout the seven-year time frame considered. Results show that the policy has been very successful in curbing the likelihood of apprentices dropping out early; the share of individuals continuing the apprenticeship increases in the first year by 6.0 p.p. (or 13.8% of the stock of apprentices in that time window), reaching a maximum of 6.8 p.p. at the end of the third year (corresponding to 43.4% of those still in an apprenticeship at that time). The effect becomes moderately negative in the fourth year because, while many apprenticeships of the new regime reach their natural termination date, some contracts in the old regime are still effective (e.g. craft sector apprenticeships had a duration of five years under the old regime). The effect eventually converges to zero after five years. It is important to note that the reduction of the dropout rate was already achieved within the first year of the apprenticeship period; therefore, the estimated effect is unlikely to come from the extended minimum duration of the reformed apprenticeship (the pre-reform apprenticeship had a minimum duration of 1.5 years, and the ‘new’ contract has a minimum duration of 2 years). The dropout reduction probably results from the combined effect of the minimum wage and new on-the-job training provisions. If on-the-job training enhanced the firm-specific human capital of the trained youth, substituting a new apprentice for the trained youth implies not only a larger loss in terms of production, but also lower wage cost gains, due to the higher wage cost of apprentices. In other words, the provisions may have encouraged firms to see apprenticeships as long-term investments. The higher retention of apprentices suggests that firms’ churning behaviour is reduced. This change becomes evident when looking at the transition to permanent employment, which follows a time pattern very similar to that of the initial attachment to the apprenticeship, but with an opposite sign. The new policy reduces transitions to permanent employment in the first four years after hiring, consistent with the positive effect on attachment to the apprenticeship that has already been observed. Subsequently, there is a positive impact of 4 p.p. over the fifth year, which also carries over to the sixth and seventh years after the initial hiring, though at a slightly lower level (+3 p.p.). The shape of the effect is typical of training programmes, where positive employment effects are preceded by a negative impact at the beginning of the treatment (the ‘lock-in effect’; e.g. Wunsch, 2016). Distinguishing job transitions within the same firm from those that occur between different firms, the bulk of the effect on permanent employment occurs through promotions, particularly during the fifth year after initial hiring. The remaining panels in Fig. 3 show a slightly negative effect on transitions into another apprenticeship and on exits from the sample, but no significant effect on transitions to temporary employment or to unemployment benefits. The negative effect on attrition from the administrative panel is approximately constant throughout the time window, suggesting that the time patterns of the effects on dropout from apprenticeship or transitions to permanent employment are not an artefact of selective attrition. 5.1.2 Heterogeneous effects on employment by gender and firm size Results obtained by considering men and women separately are presented in Fig. 4. In general, the effects are similar in both cases, but there are exceptions. Most notably, there is a differential effect on transitions to stable employment at the end of the apprenticeship. While the effects for transformation within the same firm are similar, women show a significantly larger positive effect on transitions to open-ended contracts with other firms. Fig. 4 Open in new tabDownload slide Heterogeneous effects: ATT on female and male apprentices Note: This figure is described as in the note for Fig. 3. Results refer to men (dashed lines) or women (solid lines). Fig. 4 Open in new tabDownload slide Heterogeneous effects: ATT on female and male apprentices Note: This figure is described as in the note for Fig. 3. Results refer to men (dashed lines) or women (solid lines). To consider the effects of the reforms by firm size, we split the sample of apprentices according to the number of employees at the firms of their initial hire: fewer than 10, or more than 10. Firms with fewer than 10 employees are eligible for the higher tax rebate. Figure 5 shows that the positive effects that we have estimated on the overall treated sample seem to come mostly from those apprentices hired in firms with more than 10 employees. The positive effect on attachment to the apprenticeship is much smaller in firms with fewer than 10 employees. At the beginning of the sixth year, the different lock-in effect translates into very different results in terms of transition to permanent employment. In particular, the effect on permanent employment in the same firm is zero in small firms, while in larger firms the impact is +6.3 p.p., corresponding to a 39.7% increase relative to those in open-ended contracts in the same firms at that time. In the subsequent two years the effect remains relatively constant for the apprentices hired in larger firms, while for the smaller firms it decreases, becoming slightly negative at the end of the seventh year (−1.4 p.p.). ‘New’ apprentices hired by firms above the 10 employee threshold also have a larger effect on the number of apprentices working in permanent jobs in other firms at the end of the seventh year (+3.2 p.p.), while there is no such effect in small firms. Overall, for small firms the policy seems to have a limited effect on employment in the salaried private sector. Fig. 5 Open in new tabDownload slide ATT on the apprentices hired in small-sized and other firms This figure is described as in the note of Fig. 3. Results refer to firms below 10 employees (dashed lines) or other firms (solid lines). Fig. 5 Open in new tabDownload slide ATT on the apprentices hired in small-sized and other firms This figure is described as in the note of Fig. 3. Results refer to firms below 10 employees (dashed lines) or other firms (solid lines). The most likely explanation for the worse performance of the reforms in small firms is their lack of capability to deliver on-the-job training, which may have reduced the overall training opportunities for apprentices. Furthermore, smaller firms have a higher incentive to churn and an incentive to keep the size of their permanent staff below 10 employees to enable access to the higher SSC rebate. Apprentices do not contribute to determining firm size for legal purposes, but if they are transformed into regular employees (either permanent or temporary), they could affect the 10 employee threshold and trigger loss of eligibility for lower payroll taxes. 5.1.3 Effects on wages The INPS data contain information on apprentices’ gross pay and the total number of full-time equivalent working days, from which we obtain the full-time equivalent gross daily wage for each month in the seven-year window starting from t = 0. To account for earnings attrition over the period, we perform the analysis both including and excluding zero wages; when zero wages are included, the outcome can be seen as an overall measure of compensation that includes non-employment periods.21 Results are reported in Fig. 6. Including zero wages increases the month-to-month volatility of the estimated effects and reduces the precision of the estimates, but the overall pattern is similar. There is an initial sizeable effect of the new apprentice contract on wages, which are almost 20% higher for apprentices hired under the new regime than under the old. This increase is in line with the higher minimum wage introduced by the reforms. Interestingly, the wage gap between apprentices under the different regime shrinks over time, especially during the first two years after hiring; this suggests that paying higher wages in compliance with the law may come at the cost of reduced wage growth. However, there is a significant long-run wage effect from the reforms (about +3%, and roughly stable after the fifth year), which possibly reflects the increase of apprentices’ human capital thanks to increased opportunity for training under the new regime. Fig. 6 Open in new tabDownload slide ATT on the full-time daily remuneration: maintaining (left) and removing (right) zero outcomes Notes: ATT estimated by CBPS estimator of the reformed apprenticeship versus the old apprenticeship on a sample of 16,805 apprentices hired in 2007 aged 19-24 (after trimming). Effect in %. Left panel outcome: full-time daily remuneration (zero if the individual does not work in t). Right panel outcome: full-time daily salary (missing if not working). Bootstrapped standard errors (199 repetitions) clustered by individual to take into account serial correlation. Fig. 6 Open in new tabDownload slide ATT on the full-time daily remuneration: maintaining (left) and removing (right) zero outcomes Notes: ATT estimated by CBPS estimator of the reformed apprenticeship versus the old apprenticeship on a sample of 16,805 apprentices hired in 2007 aged 19-24 (after trimming). Effect in %. Left panel outcome: full-time daily remuneration (zero if the individual does not work in t). Right panel outcome: full-time daily salary (missing if not working). Bootstrapped standard errors (199 repetitions) clustered by individual to take into account serial correlation. It is also interesting to consider heterogeneity of remuneration effects by gender. There is a distinctive gender difference in entry salary in terms of ATT, with women showing an effect that is half that of men. For both men and women, there is a decline of the effect during the first two years of the contract and a long-term effect of about +7%. Looking at heterogeneity by firm size, firms below the 10 employee threshold show no significant remuneration effect in the long run, which is in line with the insignificant effect on the employment rate.22 5.2 Robustness We perform several robustness tests on the estimates. In a first set of tests, we check whether the estimates are sensitive to the type of semiparametric estimator on the observables implemented. First, we estimate the ATT by the standard inverse probability weighting. Second, we estimate the ATT using the maximum trimming rule, and, third, on the untrimmed sample. Fourth, we use the shrinkage method of Pohlmeier et al. (2016) on the IPW estimator by the cross-validation method. This method shrinks the estimated propensity score toward the estimated unconditional mean (i.e. the share of treated) to avoid giving some units excessive weights. Finally, we replace the covariates observed at hiring (i.e. sector, dimension, firm position) with analogous variables measured during the last job (at least 30 days before the hiring). As shown in Figure 6A in online Appendix A, the results are not significantly different from the benchmark estimates, apart from the last specification, which shows larger effects for transformations and apprenticeship retention. In the second test, we check whether the estimates are robust to the presence of potential unobservable confounders. The CBPS estimates rely on the credibility of the CIA. Although we control for a large number of variables that refer to the past employment history of apprentices, we cannot control for all unobservable factors that may drive a different selection of apprentices in the two regimes.23 However, we can dispel many doubts on correct identification of the results by implementing the sensitivity analysis proposed by Rosenbaum (2002). The analysis assumes that the estimates may actually be driven by an unobserved confounding factor, u, affecting the likelihood of treatment D and the outcome Y. The odds ratio of differential treatment assignment due to X and u can be defined as Γ: Γ=piXi,ui*(1-pjXj,uj)pjXj,uj*(1-piXi,ui= exp βXi+γui exp βXj+γuj (4) with i the treated unit and j the control unit; p is the propensity score estimated by a logit model, X and u are the observed and unobserved confounding factors, and β and γ are their relative effects on the probability of treatment. It can be shown that for matched unit (⁠ Xj= Xi ⁠), we obtain Γ=exp⁡(γui-uj) ⁠, which is equal to 1 if there is no difference in unobserved factor (⁠ ui=uj ⁠) or if ui does not affect the probability of treatment (⁠ γ=0) ⁠. The goal of this sensitivity analysis is to determine the magnitude of the bias Γ ⁠, which would make the treatment effect insignificant. For example, Γ = 2 means that, in order to undermine the analysis, we would need a confounding factor u that makes treated individuals twice as likely to receive the treatment despite having the same X. Note that this bias is a worst case scenario, as the relation between u and Y is assumed to determine perfectly whether Y of the treated would be larger or smaller than Y of the matched control. Finally, we follow DiPrete and Gangl (2004) and relate Γ to an equivalent bias introduced by varying an observed X. We consider the outcomes where we found the largest effect; that is, the lock-in of the initial apprenticeship and the transformation to an open-ended job in the same firm during the third, fifth, and seventh years. The Rosenbaum (2002) sensitivity test indicates that, to reverse the conclusion, we would need a sizable worst-case confounding factor on top of our covariates. For the lock-in of the initial apprenticeship, the odds of receiving the treatment have to be increased by 54% (100% for apprentices in larger firms). Instead, the transformation to a permanent contract requires an increase of at least 30% in the fifth year and 15% in the seventh year (35% in both years for larger firms). Results are reported in Table 4A of online Appendix A. An equivalent bias of 54% required to reverse the lock-in effects (or of 15%, for the effect on transformations) would be obtained if we increased the total weeks of experience of the treated units by 3.5 times (2.4 for the transformations) or the past full-time salary by 5.5 times (or 2.4 times). In the case of larger firms, the induced bias for the lock-in of 100% (or of 35%, for transformations) would be reached if we increased these covariates by 5 (2.7) or 8.1 (2.4) times. In addition, let us keep in mind that this is a worst-case confounding factor, as it should also perfectly determine whether the Y of the treated is larger or smaller than the Y of the matched control. Overall, the evidence points to the robustness of our results. 5.3 A DiD analysis In this section, to provide further evidence of the robustness of our analysis, we estimate the effects of the reforms relying on a set of assumptions different from those behind the CBPS. The policy adoption occurred in a staggered fashion across regions and sectors, which allows us to implement a DiD estimator with multiple groups and time periods.24 This estimator does not directly control for the sources of selection, but removes time-invariant unobserved heterogeneity by taking the double differences in the outcomes between the two groups before and after the reforms; this assumes that counterfactual trends in outcomes in the absence of the treatment Yt0 are the same for the treated and control groups. The DiD estimator is implemented by the following regression model: Yit=∑t=1T-1(ϑtdTit)+∑r=1R-1ηr*dREGIONir +∑c=1C-1ηc*CBAic +∑s=184(βs * His) +∑s=184(δs * TREATMENTit * His)+ϵit (5) where dTit are monthly time dummies for the moment of hiring, dREGIONir are regional dummies for the place of work in the apprenticeship, CBAic is the industrial collective bargain agreement where the apprentice worked, and His are dummies for each s month since the start of the apprenticeship. Finally, TREATMENTi takes a value of 1 if the apprentice should be hired under the new regime. The coefficient of the interaction between TREATMENTi and His (⁠ δs) represents the treatment effect for each s month after hiring. As mentioned in Section 2, eligibility for the treatment did not automatically translate in its actual take-up. For example, in 2007, the variable TREATMENTi (constructed by using the CBA) and the observed treatment status of the apprentice show a correlation coefficient for binary variables of 0.794.25 In this setting of imperfect compliance, δa represents the reforms’ intention to treat (ITT). This is a downward estimate of the true ATT estimated by the CBPS estimator exploiting the actual treatment status. If we are willing to assume that the effect of the treatment is stable over calendar time and is the same for the treated and control groups, we can retrieve the local average treatment effect (LATE) on the compliers by implementing a fuzzy difference-in-differences estimator (e.g. De Chaisemartin and D’Haultfœuille, 2018). As in a Wald estimator, the LATE can be estimated by dividing the ITT by the effect of the reforms on the actual take-up of the treatment. The latter effect is estimated as in equation 5, but Y is replaced with the actual treatment status D.26 Standard errors are cluster robust and calculated by bootstrapping. The DiD estimator finds similar results to those of the CBPS estimator (Fig. 7). The effect is again insignificant in small firms and of a larger magnitude in other firms. The Wald estimator also confirms the finding of the CBPS estimator. The DiD estimator is unbiased if the potential outcome in the absence of the treatment follows a parallel path across different industries. We therefore implement a placebo test estimating the ITT on the apprentices hired four months before the actual implementation of the reforms. Estimates are small and not significantly different from zero, which confirms the estimates’ credibility (Fig. 7A in online Appendix A).27 Fig. 7 Open in new tabDownload slide Event study on the apprentices: (A) ITT, (B) LATE (Wald estimator) Notes: ITT (Panel A) and LATE (Panel B) of the reformed apprenticeship versus the old apprenticeship on a sample of 69,584 apprentices hired in 2005–08 and aged 19–24. Panel A is estimated by difference-in-differences estimator, while Panel B is estimated by the Wald estimator. Treatment status defined as being hired in a sector implementing the reform. Outcomes: status at the end of each month after hiring. The effect on full-time daily remuneration is in absolute terms (and maintaining the zeros). Panel A: robust standard errors, Panel B: bootstrapped standard errors with 199 repetitions. Standard errors clustered by collective bargain agreements. Fig. 7 Open in new tabDownload slide Event study on the apprentices: (A) ITT, (B) LATE (Wald estimator) Notes: ITT (Panel A) and LATE (Panel B) of the reformed apprenticeship versus the old apprenticeship on a sample of 69,584 apprentices hired in 2005–08 and aged 19–24. Panel A is estimated by difference-in-differences estimator, while Panel B is estimated by the Wald estimator. Treatment status defined as being hired in a sector implementing the reform. Outcomes: status at the end of each month after hiring. The effect on full-time daily remuneration is in absolute terms (and maintaining the zeros). Panel A: robust standard errors, Panel B: bootstrapped standard errors with 199 repetitions. Standard errors clustered by collective bargain agreements. A potential threat to identification comes from endogenous migration, which is the migration of future apprentices to adopting regions on the basis of expected employment returns. To dispel these doubts about potential threats to identification, we use data from the Labour Force Survey between 2004 and 2008, and estimate a similar difference-in-differences regression to equation 5, which exploits the regional implementation of the Law. The outcome is an individual indicator for either regional migration or daily commuting across regional borders. We run these regressions using different age groups and allowing for lags in the effects of the policy changes. None of these exercises produced statistically significant estimated effects of the policy change on migration or commuting flows (see online Appendix C), which rules out endogenous migration and commuting as sources of bias in our estimates. 6. Conclusion We found significant positive effects of the 2003 apprenticeship contract reform on wages and transformations to permanent contracts. The reform introduced a minimum pay for apprentices, extended the maximum legal length of the contract, and allowed firms to provide part of the training on-site rather than only externally. The training feature of this reform was introduced with the dual purpose of encouraging apprentices’ learning-by-doing and simplifying firms’ administrative burden regarding external training. To estimate the average treatment effect on the treated, we exploited the contemporaneous presence of two different apprenticeship regimes, which was possible due to the staggered implementation of the reforms across regions and sectors. We found robust evidence that, in comparison with the old apprenticeship regime, the new contract improved the chances of moving to a permanent job in the same firm five years after hiring. However, this happened mostly in large firms. There are also sizeable long-run wage effects of the reforms that extend well beyond the legal duration of these apprenticeships. It is hard to say which of the many changes may explain these results; however, it is probable that the possibility of doing training on-site rather than externally may have increased the accumulation of firm-specific human capital, which induced more firms to promote their apprentices into permanent contracts. The new regime allowed firms to specify training competencies, tutoring, and the place of training, but we cannot be entirely sure that the estimated treatment effects reflect differential effectiveness of (the same amount of) training. It could also be the case that under the new regime employers obtained more information regarding the skill development of the apprentices, which eventually facilitated the transformations of the apprenticeships into permanent jobs (an asymmetric information type of argument). Or it could be that the reforms fostered higher investment in technical–professional competences/firm-specific human capital, which may have come at the expenses of less basic training. This is also potentially evidenced by the fact that apprentices under the new contract are more likely to receive open-ended contracts in the same, and not alternative, firms. This last feature is not necessarily a good one and, in the long run, may cause a ‘lock-in’ effect of apprentices that would not be in a position to benefit from greater adaptability and labour market mobility.28 The possibility of delivering internal training was inspired by the German dual system, in which training is done partly at school and partly on-the-job. The Italian and German systems, however, remain very different: in contrast to Germany, apprenticeships in Italy are full employment contracts and do not originate at school. Furthermore, the accreditation of any training curricula in Italy is a regional competence, rather than a centralized feature; thus, it has limited acceptance among employers. In addition, German apprentices often find work in firms other than their training firms, suggesting a strong emphasis on general human capital skills in addition to job-specific skills in the German apprenticeship system (Parey, 2009). Yet, in the Italian system, where the apprenticeships are entry contracts into the labour market, implementing the idea of on-the-job training has significantly improved the chances of an apprentice transforming into a permanent employee. Supplementary material Supplementary material is available on the OUP website. This comprises the data and replication files, and the online Appendixes. Footnotes 1 For example, the 2009 UK reforms tightened the link between apprenticeships and employers by offering large incentives for employers to increase training activities. In the USA, both the National Youth Apprenticeship Act of 1992 and the School-to-Work Opportunities Act of 1994 were (failed) attempts to implement the dual system (Krueger and Kumar, 2004; Lerman and Rauner, 2012). 2 Cappellari et al. (2012) estimated a positive effect of the reforms on job reallocation (the year-to-year job turnover defined as in Autor et al., 2007) and productivity on firm-level data. 3 This paper looks at the so-called ‘second-level apprenticeship’, which is a labour contract, of which there were approximately 400,000 in 2011 (constituting 14% of the employed population aged 15–29; see ISFOL, 2015). In Italy, there is a different ‘first-level apprenticeship’ that partly involves schools, but its numbers are small. (Even less popular is the ‘third-level apprenticeship’ targeted at secondary school graduates.) 4 Between 2007 and 2011, SSCs were 1.5% (3%) of the gross remuneration for the first (second) year; since 2012, employers have received a full exemption for the first three years. 5 With the exception of Abruzzo, the age limit was 26 in regions entitled to support from European Union funds, which were known as Objective 1 regions. The limit was 29 in small firms. 6 Although the policymakers created a system of administrative sanctions, it was difficult for authorities to verify firms’ compliance with training requirements. Employers not complying with the training requirements had to pay back twice the tax exemption they had received, and potentially transform the apprenticeship into an open-ended contract. 7 Some CBAs even set a minimum length under the two years (e.g. specific CBAs in the retail trade and banking sectors). Compared with the pre-reform regime, the average range of duration increased marginally; at the end of 2008, the average minimum and maximum durations under CBAs was 33 and 56 months, respectively (ISFOL, 2010). 8 Underage individuals were excluded from the ‘vocational apprenticeship’ and could only participate in the old regime or in the marginal ‘first-level apprenticeship’, the implementation of which was postponed until 2011 (ISFOL, 2013). In the evaluation, we isolate this channel of reform by focusing on individuals aged between 19 and 24 years. 9 Legislative Decree 167/2011 reformed the contract for the new jobs. As shown in Figure 3A of online Appendix A, the diffusion of new contracts under the old regime dropped at the end of 2011. In June 2012, Law 92/2012 reformed the apprenticeship regime to reflect differently on firms with fewer than 15 employees or more than 15 employees. These changes are unlikely to affect our sample as, at that date, only 1% were still serving under the initial apprenticeship. 10 While in our identification strategy we do not require random assignment to treatment, in online Appendix C we check whether the labour market of the regions that engaged in early implementation was different before the reforms. The only significant difference is the higher diffusion of apprenticeships, which probably incentivized these regions to adopt the reforms more rapidly. 11 According to IPNS population registries, 277,000 individuals aged between 19 and 24 started an apprenticeship in 2007. Of those, 40% were hired under the old apprenticeship regime and 60% under the new apprenticeship regime. 12 The database does not include periods in self-employment, public employment, inactivity, and uninsured unemployment. Similar descriptive statistics are found in ISFOL (2013), where it is also shown that the share of apprentices ending up in self-employment (including external collaborators) or in the public sector seven years after hiring is 9.4% (in the time period 2005–12). According to Italian Labour Force Survey data, the vast majority of apprentices who leave employment enter into periods of unemployment (60%) or inactivity (29%), while only 11% of them go into self-employment. 13 This is more likely to occur in firms: (1) in which human capital is a secondary factor and the productivity gain at the end of the training is low; (2) with a high probability of job destruction, which decreases the expected return of a trained worker and increases the expected cost of EPL; and (3) in which the financial incentives for using an apprenticeship contract are higher (e.g. in Italian firms with fewer than 10 employees). 14 Another key assumption is the stable unit treatment value assumption (SUTVA). Since the intervention target group is quite small (apprenticeships constitute a small part of all contracts) and the apprentices under the two regimes do not directly compete in the same labour market, as they tend to work in different regions or sectors, the magnitude of the bias coming from a failure of the SUTVA is probably small. 15 We exclude the 30 days before starting the apprenticeship in order to isolate possible anticipation effects on the covariates. 16 Huber et al. (2013) also proposed removing the control units with a weight higher than 4% of the total. However, this additional trimming is not required in our sample, as the highest relative weight is only 0.2% of the total sample. 17 If we trim by the maximum rule, or do not trim, the balancing tests are slightly worse (the highest SBs are 5.0% or 6.1%, respectively). 18 As for the covariate ‘apprentices hired in firms with more than 500 employees’, we do not have a sufficient number of units under the old regime to balance the treated group (47 versus 891 units); so, we remove these individuals before estimating the propensity score (i.e. trimming on covariates), which leaves us with 17,010 units. 19 This explains why the sum of all the effects is not 1. 20 Compared with a duration analysis, where the focus is on the moment of transition, our setting has the advantage of including also indirect effects, such as the persistence of the status. Analyses on the hazard rate using semiparametric estimators are also related to more complex implementation due to changes in composition over the apprenticeship period. 21 The propensity score is estimated on the full sample and used throughout the observation window irrespective of the availability of wage information at any given point in time. As a robustness test, we compared treatment effects on wages in the last month of observation, re-estimating the propensity score only for cases observed with a valid wage in that month, finding no substantive change in results. Alternatively, we estimated treatment effects on wages, limiting the sample to the balanced panel with valid wage information, finding again that results are robust. 22 Results on heterogeneous ATT on remuneration are reported in Figures 4A and 5A in online Appendix A. 23 For example, our data do not contain level of education. Using the Italian Labour Force Survey, we test whether the level of education of the apprentices had increased during the period of reform (2004–11). As the new apprenticeship has been progressively rolled out in Italy, we may expect to observe an increase in the level of education of apprentices if firms started hiring more educated individuals under the terms of this contract. We do not find evidence of a compositional change in the education of the apprentices (Figure 8A in online Appendix A). Furthermore, using the same data we implement a DiD estimator as proposed in Section 5.3 to test whether the average level of education has been changing in the sectors and regions implementing reform. Estimates are not statistically significant (see Table 5A in online Appendix A). 24 To have sufficient variation in the introduction of the reforms over time, we enlarge the time window of the inflow sample from 2005 to 2008. The final sample is composed of 69,584 fresh periods of apprenticeship. 25 If we also consider the regional laws, the correlation coefficient decreases to 0.546, which confirms that the reforms were implemented only in renewed CBAs, even in regions implementing regional law. We therefore only use the CBAs to construct the TREATMENT dummy. 26 Note that as we have the actual take-up only from 2007, we can only estimate the effect on the actual take-up in 2007 and 2008. Therefore, our LATE relies also on the assumption of constant effect on the take-up in the period 2005–08. 27 Unlike the CBPS estimator, the long-run effect on full-time daily remuneration is insignificant in the DiD. However, as shown in Figure 7A in online Appendix A, a placebo test on the longer-run effect of this outcome is rejected. 28 We owe this interpretation of the results to an anonymous referee. 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TI - The effects of youth labour market reforms: evidence from Italian apprenticeships
JF - Oxford Economic Papers
DO - 10.1093/oep/gpz053
DA - 2007-04-01
UR - https://www.deepdyve.com/lp/oxford-university-press/the-effects-of-youth-labour-market-reforms-evidence-from-italian-xN7y62y4zp
DP - DeepDyve
ER -