No extension without representation? Evidence from a natural experiment in collective bargaining
Pubblicato online: 20 ago 2020
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DOI: https://doi.org/10.2478/izajole-2020-0005
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© 2020 Alexander Hijzen, Pedro S. Martins, published by Sciendo
This work is licensed under the Creative Commons Attribution 4.0 International License.
Following the global financial crisis and the large increase in unemployment that ensued, there has been a renewed interest in the role of collective bargaining for economic performance. This interest may increase again during the ongoing pandemic crisis. Well-functioning collective bargaining systems can promote high and stable employment by increasing the responsiveness of working conditions—such as wages and working hours—to economic shocks. This is achieved either through effective coordination that allows working conditions to be aligned with macro-economic conditions or through decentralization that facilitates greater consistency between wages and firm-level conditions (Blanchard et al., 2014; Dustmann et al., 2014; OECD, 2018).
One may also argue that, when fostering wage growth, collective bargaining has the potential of promoting consumption and hence aggregate demand. This may be of particular relevance where there is economic slack, inflation is low, and the room for macroeconomic policy stimulus is limited. However, if not functioning optimally, collective bargaining systems run the risk of reducing the responsiveness of working conditions to negative aggregate shocks. As a result, collective bargaining may increase the social costs of economic downturns by increasing the reliance on labor shedding and slowing down labor market adjustment.
In many countries, particularly but not only in Europe, collective bargaining coverage is determined to an important extent by extensions issued by governments. These administrative extensions widen the reach of collective agreements over and beyond their signatory parties—typically firms affiliated with subscribing employer associations and workers affiliated with subscribing trade unions—to
Extensions have been motivated by the goal of creating a level-playing field and, in doing so, limiting the scope of competition because of the less generous working conditions while enhancing inclusiveness and reducing wage inequality. Extensions can also reduce the transaction costs of setting working conditions, which may be particularly important for small firms that lack the resources to engage in firm-level bargaining and in contexts in which general labor law is limited.
A first quantitative indication of the importance of extensions for collective bargaining coverage can be obtained by contrasting trade union density—the share of workers affiliated to a union—with collective bargaining coverage—the percentage of workers whose working conditions are subject to a collective agreement (Figure 1). In countries where the difference between union density and bargaining coverage is large, such as France, extensions tend to be important. However, (administrative) extensions are not the only factor behind the difference. In many countries, agreements apply
Figure 1
Collective bargaining coverage and trade union density.
Early theoretical work has highlighted potential concerns about the role of extensions for employment, particularly when the social partners are unrepresentative of the sector. Moll (1996) presents a model of administrative extensions with heterogeneous firms in which only some fraction of the largest and most productive firms is engaged in collective bargaining. He shows that these firms benefit from extensions because it reduces competition from less productive firms and allows paying lower wages. By contrast, nonunionized low productivity firms need to pay higher wages, reducing the scope for low-wage competition. In the same spirit, Haucap et al. (2001) show that employer associations can use extensions as an anticompetitive device by raising the labor cost of potential entrants. For both reasons, nonrepresentative extensions could reduce employment opportunities for low-productivity workers.
Empirical papers that analyze the role of administrative extensions do not yield a uniform picture. Murtin et al. (2014) show, using country-level panel data, that excess coverage—the difference between bargaining coverage and union density—is not systematically correlated with (higher) unemployment. However, they also present evidence that suggests that the effects are more adverse in countries where the tax wedge—the difference between labor costs and take-home pay for employees—is higher. See also Martins et al. (2017), who also consider the case of Portugal, and Diéz-Catalán and Villanueva (2015), who explore the contrast in collective bargaining in Spain before and after the emergence of the 2008 financial crisis and find evidence of increased job loss from more generous contracts. De Ridder and Euwals (2016) provide suggestive evidence that extensions increase wages in the Netherlands, but do not consider the role of extensions for employment.
Taking these findings at face value, one possible explanation is that the results differ because extensions operate differently in different countries. Indeed, the Netherlands subjects extension requests to strict criteria to ensure that collective agreements are representative of the entire sector (Hijzen et al., 2019), while this is not the case or applies only to a more limited extent in most other countries where extensions are important. If more representative employer associations negotiate more representative agreements that suit most firms in their sector, this could explain the absence of adverse employment effects in the Netherlands. Importantly, no previous studies have directly examined the role of representativeness by taking account of the membership of firms to employer associations.
This paper contributes to the literature on collective bargaining by providing new insights on the causal impact of extensions. More specifically, this paper analyzes the impact of administrative extensions of collective agreements on employment in affiliated versus nonaffiliated firms. Importantly, it sheds light on the extent to which concerns about representativeness are warranted in practice. Our paper is also related to a broader literature about the role of firms in explaining wage inequality and the contrasting outlooks across countries, possibly depending on their evolving collective bargaining models (Card et al., 2013; Devicienti et al., 2019).
The analysis is based on a natural experiment that resulted from the immediate suspension of extensions by the new government in Portugal that took office in June 2011. We employ a regression discontinuity design (RDD) that exploits the standard administrative delay between the time an agreement is concluded until the time it is extended in combination with the suspension of extensions in June 2011. Importantly, this resulted in a sharp and unanticipated decline in the probability that an extension was issued several months prior to the change in government and the change in policy regarding extensions. This approach offers important advantages over the difference-in-differences method adopted in Martins (2019), which also draws on a different dataset and covers a different period.
Our main result is that extensions had a negative effect on employment growth during the period 2010–2011, amounting to five percentage points or more depending on the specification. Moreover, the negative impact of extensions tends to be concentrated among nonaffiliated firms. This suggests that the limited representativeness of employer associations is a potentially important factor behind the adverse effect of extensions on employment. These large effects are likely to reflect to some extent the specific context of recession during which the natural experiment took place. The adverse effects of extensions are also larger if the administrative delay in processing extensions is longer. The latter reflects the role of retroactivity, which refers to the requirement in place until the 2012 labor reform for nonaffiliated firms to pay wage arrears over the period from the entry-into-force of the original collective agreement to the time when the extension is issued. Finally, we present evidence that suggests that the adverse effect of extensions on employment growth comes about through their impact on wages in the bottom part of the distribution. This hints at a potential trade-off between the wage and employment effects of extensions.
The remainder of this paper is structured as follows. Section 2 provides the economic and institutional context at the time of the experiment. Section 3 describes the experiment, explains how this is exploited using an RDD, and discusses the validity of this approach in the present context. Section 4 discusses our matched employer–employee dataset complemented with information on collective agreements and extensions (including their timings). Section 5 presents the evidence on the impact of administrative extensions across the board as well as separately for firms that are affiliated to an employers’ association and those that are not and at the level of occupations. It also analyzes how the impact of extensions depends on the degree of representativeness of employer associations and the role of retroactivity in combination with the administrative delay in processing extensions. Section 6 presents some additional results in relation to wage inequality. Finally, Section 7 concludes.
During the 2000s, Portugal experienced low growth, declining international competitiveness, and deepening macroeconomic imbalances (Blanchard, 2007). As a result, the country had to face up to the global financial crisis in an already fragile situation. The global financial crisis prompted large increases in public deficits and loss of market access amid a sudden stop in capital flows, leading to a request for financial assistance, in April 2011, directed toward the European Union, the European Central Bank, and the IMF. Financial support was made available, conditional on several structural reforms and adjustment measures. Given the potential importance of real wage adjustment to minimize employment losses and concerns about the role of collective bargaining, structural reforms also included measures on the extension of collective agreement to nonaffiliated firms.
Until mid-2011, collective bargaining in Portugal—as in many other European countries—took place almost exclusively at the sectoral level, being driven by negotiations between employer associations and trade unions. Firm-level bargaining was essentially limited to state-owned and former state-owned companies and a small number of other very large firms or holdings. Moreover, coverage of (sectoral) collective agreements was very high, despite the low union and employers’ association density rate (estimated at 11% and 25% in 2009 of workers and firms, respectively), due to administrative extensions that widened the reach of collective agreements beyond the signatory parties to all firms and workers in each sector. In the absence of extensions, the “double affiliation principle” applies. See footnote 2 for details. Collective agreements and their revisions were also focused on the increase of the minimum wages per occupation, as most nonwage provisions simply replicated the contents of the Labour Code (Martins and Saraiva, 2020).
For an extension of a collective agreement to be issued, a request is needed to be made to the government by either the subscribing employers’ association or the trade union (or both), with respect to a new or a revised collective agreement (both of which were typically about the updating of the minimum wages for workers of different occupations and job levels (Martins, 2019). The government would then assess the economic and social desirability of a potential extension, partly based on an empirical analysis of the number of workers potentially affected (in terms of increased salaries), while allowing other firms or unions to present arguments against the potential extension. Though this administrative procedure would delay the issuance of extensions by several months, the positive outcome of this procedure was virtually never in doubt, resulting in the extension of almost all collective agreements. To fully promote a level-playing field, extensions entered into force retroactively, so that they would have legal effect at the same time as the underlying collective agreements for the signatory parties, even if the extensions were issued (much) later. This forced firms to pay wage increases to workers not initially covered in the collective agreements, i.e. workers employed by nonaffiliated firms and nonunionized workers in affiliated firms (the latter if their firms had not already extended internally and unilaterally the collective agreement). These wage increases had to be paid not only from the time the extension was issued but also from the time the underpinning agreement was signed.
Due to the low levels of membership of the social partners (in particular the unions), extensions played a key role in supporting high and stable collective bargaining coverage in Portugal and effectively removed the scope for low-wage competition between affiliated and nonaffiliated firms in each sector. Given the high level of unemployment and the need for restoring international competitiveness, extensions were increasingly seen as a source of downward wage rigidity, particularly in smaller, younger, and typically less productive firms, who were generally not affiliated and not represented in the collective bargaining process. The low affiliation rates of the social partners thus not only increased the economic importance of coverage extensions, but also raised concerns that collectively agreed wage floors did not reflect appropriate working conditions for nonaffiliated firms.
To address questions about the role of administrative extensions for wage adjustment, the government that took office in June 2011 temporarily suspended the issuance of extensions with immediate effect while preparing a reform about the procedures governing extensions. This decision was made in the context of the structural reform package agreed between Portugal and the “troika” (EU, ECB, and IMF). This package included a provision about collective bargaining (“define clear criteria to be followed for the extension of collective agreements,” including “the representativeness of the negotiating organisations and the implications of the extension for the competitive position of non-affiliated firms”). The full passage reads “Define clear criteria to be followed for the extension of collective agreements and commit to them. The representativeness of the negotiating organisations and the implications of the extension for the competitive position of nonaffiliated firms will have to be among these criteria. The representativeness of negotiating organisations will be assessed on the basis of both quantitative and qualitative indicators. To that purpose, the Government will charge the national statistical authority to do a survey to collect data on the representativeness of social partners on both sides of industry. Draft legislation defining criteria for extension and modalities for their implementation will be prepared by Q2-2012.” See the full text of the memorandum in
Given the low density of employers’ association membership, this led to concerns that the 50% representativeness criteria were too strict. Figure 2 documents the degree of representativeness of sectoral collective agreements signed between September 2010 and August 2011. Representativity is measured by share of the workforce in firms that are affiliated to an employers’ association with respect to the total workforce of the sector. The figure shows that, in most collective agreements, such share in affiliated firms fell well short of the 50% threshold adopted.
Figure 2
The representativeness of collective agreements.
Number of sectoral collective agreements signed between September 2010 and August 2011 by the share of workers in firms affiliated to an employers’ association
Consequently, the reintroduction of extensions in 2012 only led to a modest pickup in the number of administrative extensions as shown in Figure 3. This largely reflected the persistently low number of new or revised collective agreements concluded at the sectoral level. Apart from the period 2011–2012, the figure also reveals a sharp but temporary decline in the number agreements signed and extended in 2004. This reflects the role of the 2003 labor reform that delayed the conclusion of new or revised agreements until the reform was completed. This change therefore does not reflect an unanticipated change in the extension regime as was the case in the period under study in this paper and is therefore not amenable to the same evaluation as the one conducted in the present paper.
Figure 3
Number of sectoral collective agreements and extensions, 2000–2015.
Lingering concerns about the stringency of representativeness criteria in relation to extensions resulted in another reform in extension criteria in July 2014, after the end of the adjustment program, which introduced an alternative representativeness criterion, met if more than 30% of firms affiliated to a signatory employers’ association consisted of small or medium-sized enterprises (firms employing less than 250 employees). As this is likely to be the case for the large majority of employer associations, this largely represented a return to the pre-2011 situation. This has resulted in a modest pickup of the number of extensions issued in 2015 (Figure 3). More recently, in June 2017, representativeness criteria were dropped altogether, making extensions virtually automatic again, even in the current context of the COVID-19 pandemic and its very negative labor market effects.
In order to analyze the causal effects of coverage extensions, this paper makes use of the natural experiment that resulted from the decision of the government that took office in 2011 to immediately suspend the extension of collective agreements, as described above. Importantly, due to the usual administrative delay associated with the extension of collective agreements, a substantial number of collective agreements had been signed before the new government took office, on June 21, 2011, but were not extended or, in a limited number of cases, had their extension considerably delayed (to the second half of 2012 or later).
As shown in Figure 4, this created a sharp discontinuity around February/March 2011 in the probability that a collective agreement was extended in the 12 months following the conclusion of a collective agreement. More specifically, the figure displays the probability that collective agreements
Figure 4
The probability that a collective agreement is extended.
Moreover, the decision of the new government to suspend the extension of collective agreements was unexpected and hence could not be anticipated by trade unions and employer associations conducting the collective bargaining (a process that can last six months or more). In fact, in February or even in March 2011, there was no public information regarding the April 6th bailout request, the May 17th bailout package, and the June 5th elections (unexpected as a full legislature would come to an end only in 2013) nor the new policy on extensions introduced by the government that took office on June 21st.
This means that insofar as one focuses on a short window around March 1, 2011, it is unlikely that there are systematic differences in the characteristics of workers and firms covered by collective agreements in the period just before the new government took office—and that were extended—and the characteristics of workers and firms covered by collective agreements in the period just after the new government took office—and that were not extended.
While this is uncontroversial in Portugal, it is important for the present paper as it determines the validity of the “natural” experiment for analyzing the causal impact of extensions.
The sharp and unanticipated decline in the probability that a collective agreement is extended in early 2011 is used to analyze the impact of extensions by means of an RDD. The intuition of RDD is that the outcomes of firms and workers covered by collective agreements signed just before March 1, 2011, provide a good counterfactual for those of firms and workers where a collective agreement had been signed just after 1st March but was not extended. The main advantage of RDD compared to other quasi-experimental estimators is that it relies on relatively weak assumptions and that these are testable in the same way as in a randomized experiment (Hahn et al., 2001; Lee and Lemieux, 2010).
As there is some variation in the administrative delay associated with the extension of agreements, the probability of extension does not fall from one to zero from one week to the next (see Figure 4). In order to use a strict sharp design, we drop the two agreements signed between January 24, 2011, and February 28, 2011, that were not extended. In this case, all agreements signed before March 1, 2011, were extended and all those signed after were not. An alternative option would be to focus on agreements signed just before January 24, 2011, and those signed just after February 28, 2011. However, this would unduly restrict the size of the sample.
Formally, the sharp RDD can be described by the following model:
where In other words, in our RDD we make use of a cross-sectional comparison of annual outcomes within the same year between firms in sectors covered by collective agreements that were extended and firms in sectors covered by collective agreements that were not extended. Therefore, we do not conduct an RDD over time: our outcome variables focus on changes between October of one year (say 2011) and October of the previous year (2010).
An alternative possibility is to make use of a fuzzy RDD that explicitly takes account of the non-fully sharp decline in the probability of extension during the period January 24, 2011, to February 28, 2011, given the two data points mentioned above. Formally, the fuzzy RDD can be described by an outcome equation and a treatment equation. The treatment equation models the probability that a collective agreement is extended conditional on relative time as a function of a constant (
The outcome equation, in turn, models the outcome variable of interest (
The outcome and treatment equations are estimated with two-stage least squares (2SLS) using the same estimation sample for the treatment and outcome equations.
In practice, we pool the data (described below) across affiliated and nonaffiliated firms, that is, we stack them up for each collective agreement. We then perform two exercises. First, we estimate the impact of extensions on total employment growth between October 2010 and October 2011 across firms while controlling for affiliation status. Second, in order to analyze the differential effects of extensions on firms that are affiliated to an employers’ association versus those that are not, we add an interaction between the treatment dummy and the dummy for affiliation status, while also allowing for different relative time effects across affiliation-status groups, and, as before, controlling for the independent effect of affiliation status. Standard errors correct for heteroscedasticity and are clustered by agreement date and agreement to take account of the discrete nature of our data as suggested by Card and Lee (2008) as well as the fact that we split and then pool the data between affiliated and nonaffiliated firms. Note that we draw on a limited number of agreements and that it would be desirable to have a larger sample size, particularly around the cutoff.
Controlling for relative time effects is key in the present context for two main reasons. First, as the dependent variables are measured in October 2010 and October 2011, the part of the year to which firms are exposed to extensions depends on the timing of the extensions. An agreement that is extended later necessarily has a smaller time period to generate effects than one that is extended earlier. Second, economic conditions may affect the timing of agreements as well as their actual contents. For these reasons, outcomes are likely to depend on relative time. In our analysis, relative time effects are assumed to be either linear or quadratic and are allowed to differ between the two sides of the threshold. Given the small number of collective agreements, we will mainly focus on (potentially asymmetric) linear relative time effects.
An important feature of RDD is that, as long as the treatment is randomized around the threshold, controlling for any characteristics should not affect the estimated size of the discontinuity at the threshold. Controlling for observed or unobserved characteristics in our context may nevertheless be helpful, to take account of the potential effects of any other differences across sectors that concluded their bargaining just before or after the threshold for extension.
The validity of our natural experiment hinges on the assumption that the decision of the new government to suspend the extension of collective agreements was unexpected and hence could not be anticipated by the social partners. If, on the contrary, the suspension of extensions had been anticipated, this could have affected the incentives for concluding an agreement and hence the frequency of observing new or revised collective agreements. Figure 5 plots the number of agreements in each week during the period September 2010 to June 2011. It does not indicate that the average number of collective agreements published in each week declined after March 1, 2011. The average number of agreements per week is even slightly higher after March 1, 2011, than in the period that preceded it. Given the limited number of collective agreements in each week, a formal test on the continuity of the density of agreements around the threshold would not be informative.
Figure 5
The number of collective agreements over time.
Weeks from March 1, 2011 (September 2010–June 2011)
Anticipation effects may also be reflected in the contents of the agreements and their composition across different types of firms and workers. In order to check whether there are any systematic differences between agreements signed just before and after March 1, 2011, we conducted a series of balancing tests that assess whether there are discontinuities along a variety of different dimensions across the threshold (Table 1). In practical terms, this involves estimating equations (1) and (2) using several predetermined variables in our dataset as the dependent variable (see the next section for more information on our data). These are, respectively, the degree of representativeness (the share of the sector workforce in affiliated firms), pre-reform employment growth (2009–2010), the size of the agreement in terms of the log number of employees potentially covered, log average firm size (in terms of employment), log average hourly wage, log median hourly wage, export intensity (exports as share of total revenue), and log labor productivity (revenue per worker). The balancing tests control for linear or quadratic relative time effects and are conducted for the pooled sample as well as separately by affiliation status.
Balancing tests
| All | Non-affiliated | Affiliated | ||||
|---|---|---|---|---|---|---|
| (1) | (2) | (3) | (4) | (3) | (4) | |
| Balancing variables | linear | quadratic | linear | quadratic | linear | quadratic |
| Representativeness, 2010 | 0.0815 | −0.0080 | 0.0923 | −0.0183 | 0.0220 | 0.0303 |
| - share of workforce in afffiliated firms | (0.1143) | (0.0574) | (0.1422) | (0.0617) | (0.0695) | (0.0510) |
| Employment growth, 2009-2010 | 0.0865 | 0.0975 | 0.0953 | 0.1045 | 0.0813 | 0.0844 |
| (0.0155) | (0.0080) | (0.0195) | (0.0106) | (0.0099) | (0.0076) | |
| *** | *** | *** | *** | *** | *** | |
| Log employment, 2010 | −0.2195 | −0.1584 | −0.4327 | −0.3626 | 0.5093 | 0.1547 |
| (0.6026) | (0.6073) | (0.6009) | (0.6273) | (0.7890) | (0.5082) | |
| Log average firm size, 2010 | −1.2418 | −1.4115 | −1.2439 | −1.3098 | −1.5805 | −1.6135 |
| - number of workers per firm | (0.3004) | (0.1840) | (0.2429) | (0.2017) | (0.2265) | (0.1765) |
| *** | *** | *** | *** | *** | *** | |
| Log average wage, 2010 | −0.0510 | −0.0812 | −0.0530 | −0.0603 | −0.1147 | −0.1120 |
| - within job title and year | (0.0870) | (0.0956) | (0.0852) | (0.0875) | (0.0901) | (0.0758) |
| Log median wage, 2010 | 0.0040 | −0.0092 | −0.0127 | −0.0059 | −0.0243 | −0.0035 |
| - within job title and year | (0.0764) | (0.0828) | (0.0775) | (0.0781) | (0.0824) | (0.0605) |
| Export intensity, 2010 | −0.4642 | −0.4553 | −0.4072 | −0.3808 | −0.5818 | −0.6151 |
| (0.0523) | (0.0494) | (0.0579) | (0.0583) | (0.0466) | (0.0264) | |
| *** | *** | *** | *** | *** | *** | |
| Log labour productivity, 2010 | 0.1753 | −0.0735 | 0.2313 | 0.0320 | −0.2217 | −0.1636 |
| (0.4604) | (0.5252) | (0.4727) | (0.5360) | (0.3814) | (0.2627) | |
*, **, *** refer to statistical significance levels of 10%, 5%, and 1%, respectively.
The results in Table 1 suggest that for some variables there are statistically significant differences between the treatment and control groups. Given the relatively small number of agreements used in the present context and the large number of variables considered in these balancing tests, this should not be surprising. It suggests, however, that the natural experiment that we are exploiting does not provide the full equivalent of a randomized experiment. To address this, we make the treatment and control groups more comparable by explicitly allowing for differential pretreatment trends in employment (in practical terms this is done by transforming the dependent variable into the change in the growth rate) as well as by including all variables as controls for which systematic differences are observed in our balancing analysis (average firm size and average export intensity).
The main data for this paper are Personnel Records (
Information on collective agreements and their possible extensions is publicly available from the Ministry of Labour (DGERT) website.
The dataset used for the empirical analysis consists of 36 collective agreements signed over the period October 2010 to August 2011 (see Appendix for details). Together these account for approximately 20% of the workforce in the private sector. In the empirical analysis, we mainly focus on the 31 agreements that were signed between October 8, 2010, and June 20, 2011. The reason for limiting the scope to agreements signed before June 20, 2011, is that the extension procedure was suspended when the new government took office in June 21, 2011. Though this decision was not publicized and is unlikely to have had a major impact on collective bargaining in the following weeks, we feel it is more prudent to limit ourselves to agreements that were signed before the new government took place. However, as will be shown below, the analysis is robust to adding these agreements to the analysis. Note also that two agreements had unclear information regarding affiliation membership and are dropped in some analysis.
The period from October 8, 2010, to June 20, 2011, can be divided into three subperiods. First, a 25-week period from September 2010 to January 24, 2011, during which all nine new or revised agreements were subsequently extended. Second, a 5-week transition period during which three agreements were signed and two were not (January 24, 2011–February 28, 2011). Third, a 15-week period from March 1, 2011, to June 20, 2011, during which 18 new or revised agreements were signed that were not extended during the subsequent 12 months.
For the present purposes, we construct a dataset with information on employment and wages (as well as sales, exports and productivity) by agreement, year, and membership status. This dataset follows from combining information from the
In an extension, we also create a different version of our dataset, for analysis not at the collective-agreement and affiliation-status level but instead at the more detailed occupation/ agreement/affiliation level. In this second case, each observation corresponds to the number of workers in an occupation of an agreement in (October) of a year. The advantage of this approach is that the same occupation can be present in different agreements, including agreements that were subject to extensions and agreements that were not subject to extensions. However, as there is a change in the occupational classification codes between 2009 and 2010, the occupation-level analysis can be conducted for employment growth (between 2011 and 2010) but not for the change in employment growth (which would also require data for 2009).
The results on the impact of extensions on employment growth (ΔE2011) and the change in employment growth (ΔE2011–ΔE2010) on all covered firms, irrespective of membership status, are reported in Table 2. It shows the results based on both the fuzzy and the sharp RDD under the assumption of either linear or quadratic relative time effects. The results based on the sharp RDD using a linear specification are visualized in Figure 6. For ease of presentation, the results presented in Figure 6 do not include any controls apart from affiliation status and relative time effects.
Figure 6
The overall effects of extensions on employment growth.
The effects of extensions, all firms
| Panel A. Employment growth (ΔE2011) | ||||
|---|---|---|---|---|
| Fuzzy | Sharp | |||
| (1) | (2) | (1) | (2) | |
| Treatment dummy | −0.0953 | −0.0500 | −0.0578 | −0.0420 |
| (0.0446) | (0.0591) | (0.0262) | (0.0262) | |
| ** | ** | |||
| Constant | −0.1042 | −0.1358 | −0.1226 | −0.1293 |
| (0.0388) | (0.0274) | (0.0313) | (0.0236) | |
| ** | *** | *** | *** | |
| Relative time effects | Linear | Quadratic | Linear | Quadratic |
| Observations | 62 | 62 | 62 | 62 |
| R-squared | 0.3976 | 0.4037 | 0.4290 | 0.4359 |
| Panel B. Employment growth (ΔE2011- ΔE2010) | ||||
|---|---|---|---|---|
| Fuzzy | Sharp | |||
| (1) | (2) | (1) | (2) | |
| Treatment dummy | −0.1574 | −0.1472 | −0.1022 | −0.1035 |
| (0.0548) | (0.0709) | (0.0301) | (0.0295) | |
| *** | ** | *** | *** | |
| Constant | −0.1950 | −0.1985 | −0.2238 | −0.1926 |
| (0.0380) | (0.0360) | (0.0279) | (0.0247) | |
| *** | *** | *** | *** | |
| Relative time effects | Linear | Quadratic | Linear | Quadratic |
| Observations | 62 | 62 | 62 | 62 |
| R-squared | 0.6579 | 0.6581 | 0.6809 | 0.6958 |
*, **, *** refer to statistical significance levels of 10%, 5%, and 1%, respectively.
Authors’ calculations based on QP and DGERT data.
Change in employment growth, percentage points, (DE2011- DE2010), sharp RDD
According to the results, extensions have an adverse and statistically significant impact on employment growth. The results tend to be qualitatively similar whether a fuzzy or a sharp setup is used, whether linear or quadratic controls for relative time are included and whether the pre-reform trend is controlled for or not. Note, however, that the coefficients lose statistical significance when controlling for quadratic relative time effects and focusing on employment growth but remain largely unchanged when focusing on the change in employment growth.
The results are robust to a variety of different specifications (Table 3). Focusing on the specification with linear relative time effects, we now compare the baseline results based on the fuzzy RDD and the sharp RDD with alternative specifications or samples (Panels A and B), in the following order. “Controls” includes only affiliation status as control and not average firm size and export intensity as in the baseline specification. “Bandwidth” extends the observation window by including agreements signed after the new government took office in June 2011 to the end of August 2011. “Falsification” assesses whether there is a discontinuity when using a placebo date that evenly splits the number of agreements in the post-reform period (March–August) on each side of a fictional threshold (around the middle of May). The results indicate that excluding the controls and extending the bandwidth does not qualitatively change the results relative to the baseline. The falsification test does not point to any discontinuities in employment growth around the fictional reform date.
Sensitivity analysis, all firms
| Panel A. Fuzzy RDD1 | ||||||||
|---|---|---|---|---|---|---|---|---|
| Employment growth | Change in employment growth | |||||||
| Baseline | Controls | Bandwidth | Falsification | Baseline | Controls | Bandwidth | Falsification | |
| Treatment dummy | -0.0953 | -0.0511 | -0.0976 | -0.1574 | -0.1217 | -0.1540 | ||
| (0.0446) | (0.0163) | (0.0566) | (0.0548) | (0.0189) | (0.0523) | |||
| ** | *** | * | *** | *** | *** | |||
| Constant | -0.1042 | -0.0963 | -0.1078 | -0.1950 | -0.1350 | -0.1701 | ||
| (0.0388) | (0.0053) | (0.0523) | non-available | (0.0380) | (0.0123) | (0.0327) | non-available | |
| ** | *** | ** | *** | *** | *** | |||
| Relative time effects | Linear | Linear | Linear | Linear | Linear | Linear | ||
| Observations | 62 | 62 | 76 | 62 | 62 | 76 | ||
| R-squared | 0.3976 | 0.3472 | 0.4975 | 0.6579 | 0.5452 | 0.6898 | ||
| Panel B. Sharp RDD1 | ||||||||
|---|---|---|---|---|---|---|---|---|
| Employment growth | Change in employment growth | |||||||
| Baseline | Controls | Bandwidth | Falsification | Baseline | Controls | Bandwidth | Falsification | |
| Treatment dummy | -0.0578 | -0.0603 | -0.0164 | 0.0364 | -0.1022 | -0.1169 | -0.0898 | -0.0345 |
| (0.0262) | (0.0203) | (0.0264) | (0.0609) | (0.0301) | (0.0245) | (0.0210) | (0.0556) | |
| ** | *** | *** | *** | *** | ||||
| Constant | -0.1226 | -0.0891 | -0.1570 | -0.0699 | -0.2238 | -0.1352 | -0.2017 | -0.2129 |
| (0.0313) | (0.0115) | (0.0412) | (0.0649) | (0.0279) | (0.0143) | (0.0259) | (0.0541) | |
| *** | *** | *** | *** | *** | *** | *** | ||
| Relative time effects | Linear | Linear | Linear | Linear | Linear | Linear | Linear | Linear |
| Observations | 58 | 58 | 72 | 46 | 58 | 58 | 72 | 46 |
| R-squared | 0.4290 | 0.3917 | 0.5210 | 0.5057 | 0.6809 | 0.5650 | 0.7015 | 0.5902 |
| Panel C. Occupation level analysis (employment growth)2 | ||||||||
|---|---|---|---|---|---|---|---|---|
| Fuzzy RDD, Employment growth | Sharp RDD, Employment growth | |||||||
| Baseline | Controls | Bandwidth | Falsification | Baseline | Controls | Bandwidth | Falsification | |
| Treatment dummy | -0.1282 | -0.0543 | -0.1292 | -0.0558 | -0.0606 | -0.0462 | -0.0197 | |
| (0.0597) | (0.0209) | (0.0454) | (0.0282) | (0.0304) | (0.0213) | (0.0404) | ||
| ** | *** | *** | ** | ** | ** | |||
| Constant | 1.5142 | -0.0956 | -0.2796 | 1.4891 | -0.0897 | -0.2920 | -0.6206 | |
| (1.8044) | (0.0150) | (0.3563) | non-available | (1.8096) | (0.0265) | (0.3562) | (0.0827) | |
| *** | *** | *** | ||||||
| Relative time effects | Linear | Linear | Linear | Linear | Linear | Linear | Linear | |
| Observations | 3,320 | 3,320 | 4,257 | 3,048 | 3,048 | 3,985 | 2,451 | |
| R-squared | 0.0774 | 0.0205 | 0.1527 | 0.0821 | 0.0243 | 0.1646 | 0.1626 | |
Regressions are weighted by the number of employees in 2010 and include controls for log average firm size, export intensity, and affiliation status unless stated
otherwise.
*, **, *** refer to statistical significance levels of 10%, 5%, and 1%, respectively.
“Controls”: affiliation status only; “bandwidth”: October 2010-August 2011; “Falsification”: placebo reform date (mid-May 2011) using agreements in post-reform period only (March 2011-August 2011).
1Standard errors are robust and clustered by collective agreement and signature date.
2Standard errors are robust and clustered by collective agreement, occupation and signature date.
Authors’ calculations based on QP and DGERT data.
The results are also qualitatively and quantitatively similar when conducting the analysis at the occupation/agreement/affiliation level (Panel C). The specification is similar to the one for the baseline results except for the inclusion of occupation dummies. Standard errors are clusters by occupation, agreement and signature date. The inclusion of occupation dummies ensures that the effect of extensions is identified within similar occupations and hence not driven by differences in the occupational structure of agreements that extended and those that are not extended.
In order to analyze the effects of extensions across firms that are or are not affiliated to an employers’ association, we now allow their effects to differ across firms that are and those that are not by adding an interaction term of the treatment dummy with affiliation status. In this case, we consider a new version of our original specification as follows:
in which
Figure 7
The effects of extensions by affiliation status.
Results by affiliation status
| Panel A. Employment growth (ΔE2011)1 | ||||||||
|---|---|---|---|---|---|---|---|---|
| Fuzzy RDD | Sharp RDD | |||||||
| Baseline | Controls | Bandwidth | Falsification | Baseline | Controls | Bandwidth | Falsification | |
| Non-affiliated firms | -0.1121 | -0.1395 | -0.1114 | -0.0536 | -0.0515 | -0.0071 | 0.0684 | |
| (0.0470) | (0.0574) | (0.0592) | (0.0329) | (0.0248) | (0.0311) | (0.1080) | ||
| ** | ** | * | ** | |||||
| Affiliated firms | 0.179 | 0.1172 | 0.0087 | -0.0980 | -0.0982 | -0.061 | -0.0280 | |
| (0.0712) | (0.0876) | (0.0962) | (0.0204) | (0.0326) | -0.0292 | (0.0336) | ||
| ** | *** | *** | ** | |||||
| Constant | -0.0544 | -0.0587 | -0.0527 | non-available | -0.0786 | -0.0975 | -0.0722 | -0.0978 |
| (0.0180) | (0.0275) | (0.0300) | (0.0156) | (0.0187) | -0.0269 | (0.1082) | ||
| ** | ** | * | *** | *** | ** | |||
| Relative time effects | linear | linear | linear | linear | linear | linear | linear | |
| Observations | 62 | 62 | 76 | 58 | 58 | 72 | 46 | |
| R-squared | 0.4157 | 0.3802 | 0.5026 | 0.4579 | 0.414 | 0.5432 | 0.5393 | |
| Panel B. Change in employment growth (ΔE2011- ΔE2010)1 | ||||||||
|---|---|---|---|---|---|---|---|---|
| Fuzzy RDD | Sharp RDD | |||||||
| Baseline | Controls | Bandwidth | Falsification | Baseline | Controls | Bandwidth | Falsification | |
| Non-affiliated firms | -0.1787 | -0.2446 | -0.1706 | -0.1222 | -0.1309 | -0.0986 | -0.0337 | |
| (0.0653) | (0.1118) | (0.0650) | (0.0428) | (0.0306) | (0.0309) | (0.0928) | ||
| ** | ** | ** | *** | *** | *** | |||
| Affiliated firms | 0.2565 | 0.1080 | 0.1798 | non-available | -0.0512 | -0.0636 | -0.0681 | -0.0216 |
| (0.0916) | (0.1877) | (0.0887) | (0.0159) | (0.0317) | (0.0272) | (0.0255) | ||
| *** | * | *** | * | ** | ||||
| Constant | -0.0710 | -0.0814 | -0.0888 | -0.0865 | -0.1283 | -0.1113 | -0.1247 | |
| (0.0163) | (0.0481) | (0.0210) | (0.0164) | (0.0181) | (0.0212) | (0.0870) | ||
| *** | *** | *** | *** | *** | ||||
| Relative time effects | linear | linear | linear | linear | linear | linear | linear | |
| Observations | 62 | 62 | 76 | 58 | 58 | 72 | 46 | |
| R-squared | 0.6650 | 0.5670 | 0.6919 | 0.6990 | 0.5762 | 0.7091 | 0.5963 | |
| Panel C. Occupation level analysis (employment growth)2 | ||||||||
|---|---|---|---|---|---|---|---|---|
| Fuzzy RDD, Employment growth | Sharp RDD, Employment growth | |||||||
| Baseline | Controls | Bandwidth | Falsification | Baseline | Controls | Bandwidth | Falsification | |
| Non-affiliated firms | -0.1736 | -0.1388 | -0.1716 | -0.0470 | -0.0524 | -0.0379 | -0.0007 | |
| (0.0802) | (0.0607) | (0.0594) | (0.0295) | (0.0290) | (0.0214) | (0.0494) | ||
| ** | ** | *** | * | * | ||||
| Affiliated firms | 0.1927 | 0.1232 | 0.0834 | -0.0934 | -0.0966 | -0.0904 | -0.0595 | |
| (0.1271) | (0.1010) | (0.0848) | (0.0522) | (0.0583) | (0.0360) | (0.0489) | ||
| * | * | ** | ||||||
| Constant | 1.4994 | -0.0597 | -0.2883 | non-available | 1.4808 | -0.0978 | -0.3074 | -0.6435 |
| (1.8100) | (0.0331) | (0.3566) | (1.8108) | (0.0254) | (0.3565) | (0.0887) | ||
| * | *** | *** | ||||||
| Relative time effects | linear | linear | linear | linear | linear | linear | linear | |
| Observations | 3,320 | 3,320 | 4,257 | 3,048 | 3,048 | 3,985 | 2,451 | |
| R-squared | 0.0779 | 0.0235 | 0.1534 | 0.0830 | 0.0256 | 0.1666 | 0.1652 | |
Regressions are weighted by the number of employees in 2010 and include controls for log average firm size and export intensity unless stated otherwise. *, **, *** refer to statistical significance levels of 10%, 5%, and 1%, respectively.
“Controls”: affiliation status only; “bandwidth”: October 2010-August 2011; “Falsification”: placebo reform date (mid-May 2011) using agreements in post-reform period only (March 2011-August 2011).
1Standard errors are robust and clustered by collective agreement and signature date.
2Standard errors are robust and clustered by collective agreement, occupation and signature date.
Authors’ calculations based on QP and DGERT data.
Change in employment growth, percentage points, (AE2011-AE2010)
The results indicate that the adverse impact of extensions on employment growth tends to be concentrated among nonaffiliated firms. This is the case for the majority of specifications reported, including for our preferred specifications that control for the pre-reform growth rate in employment. The fuzzy RDD results suggest that the impact of extensions is negative and statistically significant for nonaffiliated firms, but positive and statistically significant for affiliated firms. Using the sharp RDD, the results are more mixed, with the results for employment growth suggesting that the effects are concentrated among affiliated firms and those for the change in employment growth that the effects are concentrated among nonaffiliated firms. When focusing on the change in employment growth, extensions have a significant impact on both nonaffiliated firms and affiliated firms, with their impact being about twice as large among nonaffiliated firms as among affiliated firms. The effects among affiliated firms may indicate that some of these firms only increase the pay of their nonunionized workers once extensions are issued. Alternatively, these effects may reflect the increase in market power by affiliated firms and the subsequent reduction in output and employment to maximize profits.
The sensitivity checks further suggest that the baseline results do not hinge on the inclusion of controls or the definition of the observation window and systematic differences across extended and non-extended agreements in occupational structure. Moreover, the falsification test does not point at the presence of any significant discontinuities around the fictive threshold in the post-reform period.
These results are consistent with the view that affiliated firms can shape the use of extensions for their own benefit at the expense of nonaffiliated outsiders. They also provide a first indication that representativeness matters because the wage floors negotiated in collective agreements appear to be less appropriate for affiliated firms than for nonaffiliated firms. This suggests that the lack of representativeness of employer associations is a potentially important factor behind the adverse effect of extensions.
We now consider the role of representativeness and retroactivity for the impact of extensions on the employment performance of nonaffiliated and affiliated firms. The degree of representativeness of employer associations is measured by the share of the workforce in affiliated firms in the total employment of the relevant sector. This definition is the same as the representativeness criterion that were introduced as part of the 2012 labor market reform.
The results indicate that degree of representativeness does not appear to matter significantly for the impact of extensions for either affiliated or nonaffiliated firms (Table 5a). In fact, almost all coefficients of the interactions between extension and representativeness are insignificant. Moreover, in additional robustness checks (available upon request), we find similar results when considering dummy variables defined at different representativeness thresholds (30% and 50%, for instance).
Table 5
| Panel A. Results on the role of representativeness by affiliation status | ||||
|---|---|---|---|---|
| Fuzzy | Sharp | |||
| (1) | (2) | (1) | (2) | |
| ΔE | ΔΔE | ΔE | ΔΔE | |
| Treatment effect * | −0.1278 | −0.1757 | −0.0822 | −0.0974 |
| non-affiliated firms | (0.0424) | (0.0621) | (0.0354) | (0.0386) |
| *** | *** | ** | ** | |
| Treatment effect * | 0.3415 | 0.3383 | −0.0780 | −0.0531 |
| affiliated firms | (0.1412) | (0.1542) | (0.0427) | (0.0454) |
| ** | ** | * | ||
| Representativeness * | −0.2729 | −0.1284 | −0.3197 | −0.0297 |
| non-affiliated firms | (0.1469) | (0.1888) | (0.1690) | (0.1893) |
| Representativeness * | * 0.1770 | 0.0388 | * 0.0805 | −0.0691 |
| affiliated firms | (0.0797) | (0.1047) | (0.0594) | (0.0769) |
| ** | ||||
| Treatment dummy * | 0.3024 | 0.1296 | 0.2443 | −0.1178 |
| non-affiliated firms * | (0.1603) | (0.2129) | (0.1706) | (0.2044) |
| representativeness | * | |||
| Treatment dummy * | −0.5177 | −0.2431 | −0.1288 | −0.0233 |
| affiliated firms * | (0.2553) | (0.2887) | (0.1087) | (0.0989) |
| representativeness | * | |||
| Affiliated firms | −0.2098 | −0.2005 | 0.0079 | −0.0016 |
| (0.0866) | (0.0741) | (0.0428) | (0.0406) | |
| ** | ** | |||
| Constant | −0.0025 | −0.0467 | −0.0265 | −0.0740 |
| (0.0390) | (0.0341) | (0.0332) | (0.0304) | |
| ** | ||||
| Relative time effects | linear | linear | linear | linear |
| Observations | 62 | 62 | 58 | 58 |
| R-squared | 0.5042 | 0.6747 | 0.5587 | 0.7248 |
| Panel B. Results on the role of retroactivity by affiliation status | ||||
|---|---|---|---|---|
| Fuzzy | Sharp | |||
| (1) | (2) | (1) | (2) | |
| ΔE | ΔΔE | ΔE | ΔΔE | |
| Treatment effect * | −0.1026 | −0.1688 | −0.0459 | −0.1100 |
| non-affiliated firms | (0.0406) | (0.0510) | (0.0300) | (0.0344) |
| ** | *** | *** | ||
| Treatment effect * | 0.1708 | 0.2452 | −0.0919 | −0.0498 |
| affiliated firms | (0.0692) | (0.0817) | (0.0237) | (0.0200) |
| ** | *** | *** | ** | |
| Treatment effect * | −0.0003 | −0.0006 | −0.0003 | −0.0005 |
| non-affiliated firms * | (0.0001) | (0.0002) | (0.0002) | (0.0003) |
| administrative delay | ** | *** | * | |
| Treatment effect * | −0.0001 | 0.0003 | −0.0001 | 0.0001 |
| affiliated firms * | (0.0002) | (0.0003) | (0.0002) | (0.0002) |
| administrative delay | ||||
| Affiliated firms | −0.0926 | −0.1715 | 0.0763 | −0.0111 |
| (0.0543) | (0.0493) | (0.0270) | (0.0282) | |
| * | *** | *** | ||
| Constant | −0.0549 | −0.0682 | −0.0785 | −0.0859 |
| (0.0191) | (0.0176) | (0.0161) | (0.0169) | |
| *** | *** | *** | *** | |
| Relative time effects | linear | linear | linear | linear |
| Observations | 62 | 62 | 58 | 58 |
| R-squared | 0.4425 | 0.7089 | 0.4730 | 0.7176 |
*, **, *** refer to statistical significance levels of 10%, 5%, and 1%, respectively.
“Representativeness” is measured by the share of the workforce in affiliated firms in the total employment of the relevant sector.
*, **, *** refer to statistical significance levels of 10%, 5%, and 1%, respectively.
“Administrative delay” is defined in terms of the number of days since the entry-into-force date of the collective agreement among affiliated firms and the publication date of the extension to nonaffiliated firms.
This may be surprising given the systematic differences in the impact of extensions between affiliated and nonaffiliated firms. The absence of an apparent role for representativeness here may be due to a number of factors. A technical explanation could be that it is not the variation in representativeness
Overall, the results do not allow drawing strong conclusions about the effectiveness of representativeness criteria in mitigating the adverse impact of extensions. However, even if representativeness criteria do not effectively ensure that the interests of nonaffiliated firms are taken into account, representativeness criteria may still play a useful role in the longer-term by promoting the degree of organization among employers, particularly if implemented gradually over time. This may be valuable per se as it may help to improve the quality of industrial relations as well as the degree of trust between social partners (see also Box 3.2 in IMF, 2016).
Our next topic concerns the requirement for nonaffiliated firms to retroactively pay wage increases over the period from the entry-into-force date of collective agreements among affiliated firms to the publication date of the extension to nonaffiliated firms. The rationale of applying retroactivity to extensions is to ensure that a level playing field between signatory and non-signatory firms is preserved, consistent with the spirit of sector-level bargaining and the logic behind extensions (Hijzen et al., 2019). However, their potential bite is considerable, particularly for liquidity-constrained firms: in fact, the typical time for processing an extension in Portugal in the period from late 2010 to early 2011 was about 180 days (about six months).
We find that retroactivity plays a potentially important role in explaining the adverse impact of extensions on employment among nonaffiliated firms (Table 5b). The degree of retroactivity is measured by the number of days between the entry-into-force date of the collective agreement among affiliated firms and the publication date of the extension to nonaffiliated firms. The negative average treatment effect reflects the impact of extensions on the change in employment growth for the typical administrative delay (180 days). The interaction of the treatment effect with the administrative delay gives the impact of a one-day increase in the administrative delay on the change in the growth rate of employment following an extension. This is negative for nonaffiliated firms, whereas it is insignificant or even positive for affiliated firms. The difference between affiliated and nonaffiliated is consistent with our discussion above because retroactivity should hit nonaffiliated firms directly, while it may indirectly benefit affiliated firms by reducing competition from nonaffiliated firms.
One can obtain an indication of the impact of extensions in the absence of retroactivity by considering their effect when there is no administrative delay in processing extensions, i.e. when the administrative delay is zero. This is done by reestimating our model while defining the administrative delay in absolute value rather than as the difference from 180. Doing so implies that the treatment dummy now captures the impact of extensions in the absence of any administrative delay, rather than its impact for an average administrative delay shown in Table 5b (results not reported). Under this specification, the overall impact of extensions on employment growth is reduced, and so is the extent to which the effects are concentrated among nonaffiliated firms. In the case of the fuzzy RDD, the results indicate that retroactivity accounts for a substantial part of the adverse impact of extensions, with the negative effect on employment growth in nonaffiliated firms falling by approximately 40%, but their effects remain sizeable and concentrated among nonaffiliated firms. By contrast, the results based on the sharp RDD suggest that extensions have no effect on employment growth in either nonaffiliated or affiliated firms in the absence of any administrative delay. Overall, the results suggest that retroactivity explains a significant part of the negative effect of extensions on employment growth among nonaffiliated firms. These results should be interpreted with some caution as the discussion relies heavily on the assumed linear relationship between the length of the administrative delay and the impact of extensions and employment growth.
At least in part, these results are likely to reflect the specific context during which the reform took place. As collective agreements are public documents and there was little uncertainty as to whether or not a collective agreement would eventually be extended, retroactivity should not pose any problem as long as firms act rationally and there are no financial frictions. However, in a context where economic conditions were deteriorating rapidly and many (nonaffiliated) firms were liquidity-constrained, the requirement to retroactively pay wage increases seems to have slowed the growth rate of employment considerably (i.e. it would have made employment growth even more negative in most cases). It is important to bear in mind that in periods of growth these effects would most likely be smaller. These findings are also consistent with the large job losses found in Martins (2019), also considering a period of economic downturn (including the great recession).
Collective bargaining has been regarded as an important mechanism toward reducing wage inequality in a labor market (e.g. Blanchard et al. 2014). Moreover, this effect can be strengthened by extensions, as these can widen dramatically the coverage of binding minimum wages for different occupations and job levels in multiple industries in a given country. In this section, we examine empirically the effects of extensions on wages and wage inequality.
In order to take account of the fact that wages are set separately for different job categories within agreements, we focus on changes in residual wages and wage inequality within job categories, agreements, membership status and years. In an effort to control for the confounding role of composition effects when examining the impact of extensions on residual wages over time, we restrict the focus to workers who are employed in both 2010 and 2011. The analysis is conducted by examining the change between 2010 and 2011 in the 5th, 10th, 15th, and 20th percentile of the residual wage distribution as well as the changes in each of these moments relative to the median. Apart from the new dependent variable, the econometric model is identical to that used for the analysis of employment growth in the previous section.
The results, presented in Table 6, show that extensions have a tendency to increase wages (only) in the bottom of the distribution and therefore also to reduce inequality. More specifically, extensions tend to increase wage growth by about 5 percentage points for workers in the fifth percentile of the residual wage distribution (column 1 of Panel B) and tend to reduce the growth rate of the P50/P5 percentile ratio by a similar amount. Moreover, the effects of extensions on wages and inequality become smaller when moving up the residual wage distribution. Its effects on the wages of workers in the 20th percentile of the residual wage distribution are insignificant in all specifications. We also find similar insignificant results for higher percentiles (available upon request). Martins (2019) when considering continuing workers also finds that wages increase following extensions.
Results on inequality
| Panel A. Fuzzy RDD | ||||||||
|---|---|---|---|---|---|---|---|---|
| (1) | (2) | (3) | (4) | (5) | (6) | (7) | (8) | |
| Δp5 | Δ(p50-p5) | Δp10 | Δ(p50-p10) | Δp15 | Δ(p50-p15) | Δp20 | Δ(p50-p20) | |
| Treatment effect | 0.0805 | -0.0865 | 0.0695 | -0.0755 | 0.0710 | -0.0770 | 0.0289 | -0.0349 |
| (0.0373) | (0.0481) | (0.0400) | (0.0532) | (0.0566) | (0.0721) | (0.0285) | (0.0453) | |
| ** | ** | * | ||||||
| Constant | -0.0286 | 0.0501 | -0.0082 | 0.0296 | -0.0248 | 0.0463 | -0.0109 | 0.0324 |
| (0.0221) | (0.0296) | (0.0205) | (0.0297) | (0.0327) | (0.0419) | (0.0165) | (0.0259) | |
| Relative time effects | Linear | Linear | Linear | Linear | Linear | Linear | Linear | Linear |
| Observations | 62 | 62 | 62 | 62 | 62 | 62 | 62 | 62 |
| R-squared | 0.0875 | 0.1217 | 0.2290 | 0.2353 | 0.1727 | 0.1858 | 0.0644 | 0.1265 |
| Panel B. Sharp RDD | ||||||||
|---|---|---|---|---|---|---|---|---|
| (1) | (2) | (3) | (4) | (5) | (6) | (7) | (8) | |
| Δp5 | Δ(p50-p5) | Δp10 | Δ(p50-p10) | Δp15 | Δ(p50-p15) | Δp20 | Δ(p50-p20) | |
| Treatment effect | 0.0493 | -0.0476 | 0.0494 | -0.0477 | 0.0519 | -0.0502 | 0.0184 | -0.0166 |
| (0.0232) | (0.0294) | (0.0213) | (0.0306) | (0.0296) | (0.0392) | (0.0147) | (0.0242) | |
| ** | ** | * | ||||||
| Constant | -0.0310 | 0.0522 | -0.0087 | 0.0300 | -0.0266 | 0.0478 | -0.0109 | 0.0321 |
| (0.0213) | (0.0282) | (0.0185) | (0.0275) | (0.0298) | (0.0389) | (0.0155) | (0.0247) | |
| * | ||||||||
| Relative time effects | Linear | Linear | Linear | Linear | Linear | Linear | Linear | Linear |
| Observations | 58 | 58 | 58 | 58 | 58 | 58 | 58 | 58 |
| R-squared | 0.1019 | 0.1442 | 0.2675 | 0.251 | 0.217 | 0.212 | 0.0756 | 0.1275 |
Results based on residuals from individual-level log base wage regression on job category dummies, collapsed by firm type (affiliated vs nonaffiliated), collective agreement, and year. Dp5 denotes the change in the 5th percentile (of the cell’s log base wage residual) between 2011 and 2010, D(p50−p5) denotes the difference between the median and the 5th percentile in 2011, and similarly for the remaining dependent variables.
All in all, these findings support a binding interpretation of the extension mechanism, in the sense that they in fact push upward the wages of the bottom tail of the distribution, which is in the background of the entire paper. The findings also suggest the existence of a trade-off between the adverse effects on employment documented in the previous section and the beneficial effects on the wages of low-wage workers and inequality documented here.
In many countries, collective bargaining coverage is supported by administrative extensions that widen the reach of collective agreements beyond their signatory parties to all firms and workers in their reference sectors. Because of their potential roles in stimulating wage growth and reinforcing downward wage rigidity, extensions have become the focus of an increasingly intense policy debate in recent years. However, given the lack of hard evidence on the effects of extensions, and of collective bargaining more generally, the debate has largely tended to be based on subjective priors rather than factual arguments. By exploiting a natural experiment on collective bargaining in Portugal, this paper seeks to contribute to the ongoing discussions by providing new insights on the causal impact of extensions.
More specifically, this paper analyzed the causal impact of administrative extensions on employment growth using a natural experiment that resulted from the immediate suspension of extensions by the government that took office in Portugal in June 2011. Our analysis employs a RDD that exploits the administrative delay in issuing extensions in combination with their suspension in June 2011 and novel matched employer–employee-agreement panel data. Importantly, this suspension resulted in a sharp and unanticipated decline in the probability that an extension was issued, with respect to the timing of the publication of the underlying collective agreement, several months prior to the change in government.
The results in the paper provide important insights for the debate on the role of extensions in countries undergoing adjustment periods—including across countries facing the labor market effects of the COVID-19 pandemic—but also on collective bargaining more generally:
First, our evidence indicates that extensions played an adverse role for employment growth during the period covered and, thereby, are likely to have amplified the unemployment response to the global financial crisis until they were suspended. However, we caution that the estimated adverse impact on employment growth may not necessarily generalize to periods with different economic conditions—in particular in periods of growth, as opposed to the recession period covered here—or countries with different institutional settings (including with respect to retroactivity and representativeness of unions and employer associations).
Second, the adverse effects of extensions on employment growth mainly concern firms that are not affiliated with an employers’ association, i.e. those that do not participate or are not represented in the bargaining of collective agreements. The concentration of adverse employment effects among nonaffiliated firms suggests that extensions suit the interests of affiliated firms better than those of unaffiliated firms. This may imply that the lack of representativeness of employer associations is a potentially important factor behind the adverse effect of extensions.
Third, however, the degree of representativeness of employer associations is not found to matter significantly for employment growth. This may reflect the low levels of, and limited variation in, representativeness in our data, or that representativeness criteria (such as those implemented in Portugal in 2012) are not sufficient to ensure effectively that agreements are in the public interest. However, even if the introduction of the strict representativeness criteria in 2012 did not have a direct impact on employment growth, they are likely to have had a major impact on wage adjustment by greatly reducing the number of extensions issued, and therefore, indirectly, contributed positively to employment growth. Over the longer term, they also may help to promote employer organization, particularly when representativeness criteria are introduced gradually, and contribute to the quality of industrial relations as well as trust between social partners
Fourth, the retroactivity with which extensions entered into force until the 2012 reform appears to be harmful for employment among nonaffiliated firms. This has two important implications. It suggests that our results are to some extent specific to the weak economic conditions under which the “natural” experiment took place. If there were no uncertainty about the extension of agreements and firms were not liquidity-constrained, then retroactivity would not be expected to slow down employment growth. It also suggests that the 2012 reform may have helped to reduce the adverse effect of extensions by removing their retroactivity. Concerns that this undermines the spirit of sectoral bargaining and extensions can partly be addressed by shortening the administrative delay associated with issuing extensions.
Fifth, there appears to be a trade-off between the adverse effects of extensions on employment growth and their beneficial effects on low wages and in promoting lower wage inequality.
Overall, this paper considers many key features of sectoral bargaining, most of which for the very first time, using a novel type of matched data, and does so in a causal framework. Hopefully further research for other countries and time periods will complement our findings and also contribute toward the establishment of a sounder international evidence base of the effects of collective bargaining.