The unequal impact of raising the retirement age: Employment response and program substitution

At the time of the 1992 reform, the pension system was characterized by a defined benefit scheme, with a final benefit equal to the average of the last 5 years of gross earnings (the so-called pension base) times an accrual factor of 2% times the years of contributions (up to a maximum of 40 years), without any accrual correction for the age at retirement. Thus, a worker with 40 years of contributions would retire with a replacement rate of 80%, which is quite a generous benefit. There existed two regular streams of access to a full pension benefit, which depended on the worker’s age and the number of years of contributions accrued during the working life. Where the age qualification prevailed, it was called an “old-age pension”, whereas where the contributions prevailed irrespective of age, it was called a “seniority pension”

As from January 2012, the former Seniority pension (pensione di anzianità) has been replaced by an Early retirement pension (pensione anticipata) (DL 201/2011, n.24).

The NRA for an old-age pension was 60 years for men and 55 years old for women, with at least 15 years of contributions. Alternatively, 35 years of contributions with no age limit for both men and women were required to be entitled to a seniority pension

A third exceptional early retirement scheme (called “prepensionamento”) was offered by the Government to workers’ unions during the 80s and 90s to allow workers employed in firms facing financial constraints the possibility to claim a full pension benefit on relaxed eligibility conditions.

With the 1992 pension reform, the NRA and the years of contributions required for claiming an old-age pension were gradually increased for both men and women, starting from January 1994. This reform introduced a quasi-experimental variation in pensionable age between individuals depending on their birth date (Table 1), which I exploit in the empirical analysis.

Figure 1 plots the NRA faced by each cohort born between January 1931 and December 1936. This represents the reference population included in the empirical analysis. As can be noticed, while men born before January 1934 were unaffected by the reform, as they could retire at the age of 60, workers born in the following years had to wait from 1 years to 5 years longer because of the NRA rise. These ages and cohorts’ discontinuities are exactly the variation exploiting in the DD empirical analysis to identify the causal effect of the reform. In what follows, I will refer to the cohorts born in 1931–1933 as the “control” and to those born in 1934–1936 as the “treated” cohorts.

Figure 1

Together with the NRA, the 1992 reform also increased a) the years of contributions needed to access old-age pension from 15 years to 20 years for those with <15 years of contribution in 1992

Article 2 of Law decree 503 of the 30th, December 1992.

In 1995, another pension reform was legislated, which changed both the eligibility rules for seniority pension and the calculation of old-age and seniority pension benefits based on a notional defined contribution system. The reform was characterized by a very long transition period and by a “grandfathering” approach aimed at protecting and preserving previous rules for older workers (Brugiavini et al., 2021), leaving the facto unaffected the cohorts included in our analysis

In particular, the 1995 reform changes the pension formula only for those with less than 18 years of contributions in 1995 (<1% of the estimation sample) and introduces a minimum age of 52 (than gradually increased) for claiming the seniority pension in 1996 (when individuals of my sample were already older than 60).

Hence, an important feature of the 1992 reform is that, while the NRA for claiming an oldage pension was raised by 5 years, the conditions to qualify for a seniority pension, i.e., 35 years of contributions with no age limit, remained unchanged. The seniority pension thus became a relatively more attractive option than the old-age pension to those individuals with long contribution histories, who, as shown by Brugiavini and Peracchi (2012), tended to react to the 1992 reform by anticipating the seniority pension claims to avoid the risk of future tightening of the eligibility conditions for the seniority pension, too. Since individuals with many years of paid contributions not only were in principle unaffected by the old-age pension reform (meeting already the eligibility condition for the seniority pension) but also tended to react to it by anticipating their labor market exit, they are excluded from the final sample of analysis.

In the years of the reform under scrutiny, there were three broad categories of unemployment schemes: an ordinary unemployment benefit, a short-time work scheme, and a long-term unemployment benefit, subject to a minimum number of paid contributions in the previous year and available only to some occupations/sectors of activity. The replacement rate varied between the different unemployment schemes, from <10% to 80% and coverage was in general very limited. Although their availability and generosity increased with time, at the end of 2004 the majority of unemployed (>70%) were still unmet by any unemployment benefit schemes (Leombruni et al., 2012). More details on the evolution over time of the eligibility conditions and the replacement rate for every single benefit scheme are provided in Appendix B.

The social security system also granted different types of disability benefits to individuals unable to earn an income because of certified health conditions and whose work capacity was reduced by at least 66 per cent. The first kind was available to workers who had accrued at least 5 years of contributions, the benefit being calculated with the standard earning-related pension formula. The second type of benefit was not subject to previous work attachment and all persons could claim it, conditioning on the presence of the certified health-related work limitation. This benefit was means-tested, the amount set at €279.47 per month, topped up by €512 for assistance for those who need help to accomplish daily tasks (MISSOC, 2021).

Any reform of social security rules that increases NRA influences retirement choices according to dynamic life-cycle models where rational forward-looking individuals choose between labor and leisure to optimize the present value of the life stream of income sources from work and pension (e.g., Burtless and Moffitt, 1984; Gustman and Steinmeier, 1985).

The standard life cycle model provides an insightful framework for modeling retirement decisions, which helps to detail the expected effects of the reform. Following Blundell et al. (2016), there are three main effects induced by the pension reform under scrutiny here:

Pension wealth effects – Because the reform increased the NRA, i.e., the minimum age at which old-age pension can be claimed without introducing any accrual correction for the age at retirement, the reform can be interpreted as a negative wealth shock, as it reduces the length of time that individuals receive pension benefits and thereby the total social security wealth. Standard life cycle theory predicts that affected individuals decrease consumption, increase savings, increase labor supply, and the retirement age through the income effect (for example, Attanasio and Brugiavini, 2003).

Liquidity effects – Public pension benefits tend to be illiquid: that is, individuals cannot borrow against future benefits. This can induce liquidity constraints on individuals’ behavior inducing them to retire at statutory retirement age (for example, Krueger and Pischke, 1992). This is particularly true in Italy, where public pension programs constitute a very large share of retirement savings and private pension had extremely limited diffusion (Brugiavini, 1999). As a result, I expect stronger labor supply effects and substitution toward unemployment and disability benefits for more liquidity-constrained individuals, who cannot finance their retirement until pension benefits become available. In contrast, the expected effect on inactivity is uncertain. More disadvantaged workers categories, who in general are more liquidity constrained, may not afford to retire without benefits but at the same time, they might be facing greater difficulties in remaining employed up to the new NRA.

Substitution effects – The operation of the tax, benefit, and pension rules, can affect the relative attractiveness of working vs. retirement. It has been shown that in Italy the pre-reform set of financial incentives implied a high implicit tax on work, which remained positive and significant even after the reform (Brugiavini et al., 2021), hence providing a strong incentive to retire as soon as the eligibility conditions for early or normal retirement are met. For the cohorts in analysis, substitution effects are expected to be stronger for workers who do not have the incentive to extend working life, having already reached “full contribution history” (i.e., those with 40 years of contributions – this subpopulation is excluded from my analysis) and low-skilled workers, because of a lower level of potential forgone earnings and perspective of future wage growth (Leombruni and Mosca, 2012).

ERA vs. NRA – Because the 1992 reform increased the NRA, the reduction in prospective pension wealth occurred relatively late in individuals’ work lives. On theoretical grounds, a life-cycle theory predicts that a worker’s reaction to benefit cuts will depend on when one first learns about the reform (Mastrobuoni, 2009). Hence, one would expect the 1992 reform to have a greater effect on pension claims and labor supply than a reform raising the ERA because there is less time for individuals to reoptimize and alter their savings and consumption plans. This reflects the fact that younger individuals have a longer horizon over which to absorb the “ unexpected” shock to the pension wealth (Krueger and Pischke, 1992; Attanasio and Brugiavini, 2003).

Overall, these theoretical predictions suggest that the degree of adjustment in labor supply decisions after the reform may be influenced by several types of constraints, incentives, and information problems, particularly among older individuals. These factors can also give rise to substantial heterogeneities in adjustment behavior across population groups, which I have empirically tested in my analysis.

The empirical analysis is based on the Working Histories Italian Panel (WHIP), an administrative data set based on a 7% random sample of the INPS archives (for more details on the WHIP data: Bena et al., 2012). The sample is representative of the population insured by the INPS, which is composed of non-agricultural private-sector workers. Only civil servants hired on an open-ended contract, some professional categories (e.g., lawyers, physicians, engineers, and architects), and workers without formal attachment to the labor market are excluded from the reference population.

The overall structure of WHIP builds upon a set of separate administrative archives covering jobs and various benefits spells. The archives are linked by means of a unique individual identifier and it is possible to construct the whole career of insured workers by tracking the starting and termination dates of the above-mentioned administrative spells

For more details on the linking procedure, see Bena et al. (2012).

The empirical analysis of this paper focuses only on the male population. This choice is motivated by the fact that in the years under analysis women experienced a striking positive trend in labor force participation rates

According to official national statistics (ISTAT), from 1986 to 2002 the employment rate was almost constant for men but raised by 24% for women.

The sample under analysis is composed of a set of control cohorts (born in 1931–1933) and treated cohorts (born in 1934–1936). Control cohorts consist of individuals who turned the age of 60 before the reform, i.e., reached the NRA for claiming an old-age pension before the increase established by the reform. In contrast, treated cohorts include individuals who were under 60 before the reform and consequently were affected by it (Figure 1). For every individual in the sample, I reconstructed the social security and work histories combining all employment and welfare benefits spells using as time unit the half-year (from now on, semester).

Since the paper aims to study the effect of the 1992 old-age pension reform on the transitions from work to retirement, the estimation sample includes only male workers who were in employment at 45–55 years old and who had regularly retired by the age of 67 years receiving any type of pension for private-sector employees (old-age, seniority, or early retirement). Moreover, I exclude men with >35 insurance years at 60 years old, as they are not affected by the increase in the NRA. The final dataset is a panel strictly balanced with respect to age and it includes 29,974 individuals from the age of 55–65 years old (659,428 observations).

Table 2 describes the final sample under analysis separately for the control and treated cohorts in terms of background characteristics, measured before the pre-reform NRA (panel A), and at pension receipt (panel B). Panel A shows that before the age of 60, control cohorts were marginally more likely to be still employed and to have worked in manual occupations. Annual earnings are higher among treated cohorts are more likely to retire through the seniority pension route (granting the right to full pension benefit at an earlier age); they claim pension benefits 2.2 years later and accrued on average 1.7 more years of contributions.

The outcome variables are defined as a set of binary variables Y_itj taking value one if individual i spent at least 1 month in semester t in state j (hence, the outcomes are not mutually exclusive)

I have also explored the possibility of defining the outcomes as mutually exclusive prevalent economic states, but since results were qualitatively unaffected, I decided to stick on the first definition as it makes more efficient use of the data.

Since most unemployed individuals were not covered by unemployment benefits at the time under analysis (Leombruni et al., 2012), the category “Unemployment with benefit” is narrower than both statistical unemployment and registered unemployment

This is an Italian specificity, while for example, in Austria, registered unemployment figures are generally higher than statistical unemployment (Melis and Lüdeke, 2006).

Notice that, since the data lacks information on the entire firm population and on whether employment terminations are initiated by firms or by employees, it is not possible to disentangle between voluntary supply driven transitions out of paid employment from those that are instead demand driven, i.e., initiated by firms. Nevertheless, since entering inactivity in most cases leaves workers without any income or subsidy, transitions from employment to inactivity arguably represents an adverse and unforeseen outcome for older workers, which could be related to firms’ behavioral reaction, particularly among low-income workers (Bovini and Paradisi, 2019).

Figure 2 plots the prevalence of each labor market outcome at every single age separately for the control cohorts, i.e., workers born in 1931–1933 who could all claim pension benefit at 60 years old, and treated cohorts, i.e., workers born after 1933 whose NRA was raised gradually up to 65 years by the 1992 reform.

Figure 2

The most common labor market states at 59 years old are employment, inactivity, and retirement with benefit, for >95% of the individuals fall within one of these states at this age. After the age of 59, the pension benefit take-up rate (panel A) raises, displaying kinks corresponding to the age of first eligibility faced by different birth cohorts of workers, confirming the empirical regularity also observed in several other countries (Behaghel and Blau, 2012; Gruber and Wise, 2007). This series of parallel stepwise lines is the result of the gradual increase of NRA from 60 to 65 induced by the 1992 reform affecting different individuals born in different cohorts.

Panel B displays the age profile of the employment rate. Among the control cohorts (1931–1933) the probability of leaving employment follows a stepwise decrease, symmetrically to the inflow into retirement at 60 years old. Among treated cohorts, the pattern is similar but smoother for the youngest cohorts. For the 1935 and 1936 cohorts whose NRA was increased the most (to 64 and 65 years old), the early exit from employment (Panel B) seems to coexist with some anticipation of pension claiming at 62–63 (Panel A). Although the intensity of the treatment was higher for the 1935 and 1936 cohorts, they had relatively more time to adjust their behaviors and, arguably, they could “escape” the tightening of the old-age pension exit route exploiting the early retirement options.

Moving to the “Inactivity” and the “Disability benefit” outcomes (panels C and D), it is possible to observe a distinct parallel stepwise pattern, with a series of delayed kinks in correspondence of the eligibility ages.

Eventually, panel E shows that the probability of being unemployed with benefit was higher among younger cohorts already before age 60 among the control cohorts born in 1931–1933. This pattern most likely depends on the gradual increase of the coverage and generosity of the benefits with time and on the fact that in the first half of the nineties, in the years 1992–1993, Italy experienced a worsening of economic conditions with a substantial rise of unemployment levels. I will deal with the presence of this and other possible common time shocks by saturating the difference-in-differences model with time-fixed effects and by running specific robustness tests (Tables D3 and D4 in Appendix). Moreover, the validity of the DD parallel trend assumption will be formally tested for all the outcomes separately in the following section (Figure 3).

Figure 3

To assess the effect of the rise in NRA, I adopt a DD strategy, exploiting the 1992 reform as a quasi-natural experiment. The staggered phase-in of the new NRA from 60 to 65 allows for comparison of the outcome levels between older and younger cohorts at the various steps of the tightening, using a standard approach exploited by previous studies on pension age reforms (Mastrobuoni, 2009; Staubli and Zweimuller, 2013, Cribb et al., 2016; Soosaar et al., 2021, Morris, 2021). With this DD set-up, the first difference is across cohorts: the cohorts are treated if born after 31 December 1933, whereas those born before that date were able to retire at the NRA of 60 under the pre-reform rules. The second difference is over age: treated ages are 60–64 as at these ages, treated cohorts became ineligible for old-age pension due to the rise of the NRA. However, since the NRA was raised gradually from 60 to 65 (Table 1), the reform did not affect all uniformly, as the post-reform cohorts had to wait from 1 to 5 additional years to become eligible for the old-age pension depending on their birth date (Figure 1). I take this point into account by building groups of treated and control cohorts that are age-specific, as shown in Table 3.

On this basis, to estimate the effect of the NRA rise, the primary approach is to compare the labor market behavior of untreated and treated cohorts at every single age, estimating the following DD regressions for each of the separate outcomes Y_it: (1) Yit=∑k∈{55,56,…65}βkTa*1[a=k]+γa+δc+τt+εit {Y_{it}} = \sum\nolimits_{k \in \{ 55,56, \ldots 65\} } {{\beta _k}{T_a}*1[a = k] + {\gamma _a} + {\delta _c} + {\tau _t} + {\varepsilon _{it}}}

The above specification, where i denotes individuals and t denotes semesters, includes fixed effects for age (γ_a) and birth cohort (δ_c). To control for the business cycle, also semester fixed effects are included (τ_t). Since age is measured in years (from 55 to 65) while birth cohorts and periods are measured in semesters (from 1931-s1 to 1936-s2 and from 1986-s1 to 2002-s1, respectively)

The categories of age, cohorts and periods are shown in Table B1.

Equation (1) estimates a separate DD coefficient β_k for the interaction between an indicator variable for the treatment group T_a and every single age group k, which lends itself to a test for the common trend assumption in the spirit of Autor (2003). If treated cohorts showed trends parallel to the control cohorts in the outcomes even in the absence of the reform, I should observe no significant difference in the take-up of the outcomes in the “placebo ages”, i.e., in all the ages before 60 (because the reform did not modify the eligibility conditions for these ages) or after 64 (because at 65 everyone was entitled to an old-age pension). The results from this specification are displayed in Figure 3.

To obtain an average effect of the reform over the entire set of treated ages, and to adhere more closely to previous literature, I also estimate the following equation: (2) Yit=β*1t[a<NRA]+γa+δc+τt+εit {Y_{it}} = \beta *{1_t}[a < NRA] + {\gamma _a} + {\delta _c} + {\tau _t} + {\varepsilon _{it}}

As in Staubli and Zweimüller (2013), Cribb et al. (2016), Soosaar et al. (2021), and Morris (2021), the set of interactions terms is replaced by a single indicator 1_t[a<NRA] that takes on value one if the individual age in semester t is below the regulated NRA. This variable captures the treatment of ineligibility for an old-age pension, which results from the interaction between treatment levels (i.e., ages) and groups (i.e., birth cohorts) and which varies over time because of the gradual increase of the NRA. The DD estimator β measures the average difference in mean outcomes between control and treated cohorts in treated ages (60–64 years old) minus the control and treated cohorts’ differences in mean outcomes for the untreated ages (before 60 and >64). Table C1 in the appendix shows what the treated and untreated calendar years and ages are for the cohorts under study, i.e., 1933 to 1936. The specification includes, as in previous studies adopting this approach

See for example Staubli and Zweimuller (2013) Page 25, Table 3, columns (2)–(4) and (6)–(8).

Some methodological issues left unmet by previous works using my same DD specification to study the effect of similar pension age reforms need to be stressed. First, since the main source of policy variation occurs at time and cohort levels, the standard errors should be clustered at these levels, accounting for 33 or 12 clusters, respectively. However, Bertrand et al. (2004) and Cameron et al. (2008) have stressed that conventional DD clustered standard errors may understate the true standard deviation in samples with <50 clusters. Hence, following their suggestion, I adopt the wild bootstrap (WB) technique to compute the clustered standard errors. Second, to avoid the problem of inflation of alpha level which can originate from testing multiple outcomes (the larger the number of tests, the higher is the chance to encounter a rare event and to conclude that there is a significant effect when there is none), I correct p-values using the Šidàk multiple hypothesis correction formula 1-(1-p)ⁿ where p is the original p-value and n the number of outcomes of the hypothesis tested (Abdi, 2007)

The wild bootstrap and Šidàk multiple hypothesis correction are implemented using the Stata macro developed by Roodman et al. (2019).

As pointed out by de Chaisemartin and D’Haultfoeuille, 2020a, b; Baker et al., 2021, in a staggered DD design like the one adopted here, the estimated DD coefficients is a weighted sum of several DD with potentially negative weights, since the outcome evolution is compared between consecutive time periods across treated and control groups whose composition varies with time (de Chaisemartin and D’Haultfoeuille, 2020a, b). Whenever the number of negative weights is high and there is treatment effect heterogeneity, the weighted average represented by the final DD coefficient might be biased and the sign of the estimated beta even reversed (de Chaisemartin and D’Haultfoeuille, 2020a, b). In Section 5.2, I present the results derived from estimating the two-way fixed effect estimators developed by de Chaisemartin and D’Haultfoeuille (2020a, b), which explicitly accounts for the problem of negative weighting, and it is robust even in the presence of treatment effect heterogeneity across groups or time.

The two-way fixed effect estimator is implemented using the Stata command “did_multiplegt” developed by Chaisemartin and D’Haultfoeuille (2020a) with the dynamic option (Chaisemartin and D’Haultfoeuille, 2020b).

This section describes how the impact of a rise in NRA varies between individuals with different socio-economic backgrounds. To do so, I first estimate Eq. (2) separately for different subgroups of the sample of analysis (Table 5) and then perform a fully saturated model with the simultaneous interaction of the indicator variable 1_t[a<NRA] with several indicators of socioeconomic position measured at 55–59 years old (Table 6). The full regression outputs are presented in Table C3 in Appendix.

The first subsample analysis in Table 5 aims to investigate the presence of a potential mechanism which might be driving the results, i.e., “persistency” into pre-reform labor market states resulting in passive – rather than active – program substitution. In fact, as suggested by Geyer and Welteke (2019), an observed increase, for example, in disability benefit take-up, could result from both a higher number of persons actively changing from employment to disability, or a higher proportion of persons simply staying longer in this status. Hence, I restrict the sample to those continuously employed and who never received benefits at 55–59 years old and show that the estimated effects of the NRA rise are very close to those obtained on the full sample, suggesting that the main results are not driven by “passive program substitution”. In the following rows, I compute the effect of raising the NRA on different groups, restricting the focus on continuously employed before 60 years old to avoid the potentially differential interference of passive program substitution.

For all the socio-economic dimensions analyzed in Table 5 (occupational grade, wage, and health), the effect of the reform is larger in the most disadvantaged subsamples, i.e., with low wage (the poorest tertile), employed as manual workers, and with poor health (with >1 month of sick leave per year of work, corresponding to the third tertile of the distribution of weeks of sick leave). In particular, the pension benefit reduction among workers with the lowest salary and occupational grade is roughly around twice the reduction observed among those with the highest salary and occupational grade. Interestingly, the subsample of executives resulted almost unaffected by the NRA increase.

Since this pattern might be driven by omitted variable bias, given that these characteristics are likely to coexist (manual workers have generally lower salaries and poorer health than executives), I expand Eq. (2) and estimate a fully saturated DD model which simultaneously interacts all these socio-economic conditions with the treatment DD variable 1_t[a<NRA]. Table 6 presents the results. Despite the model being quite demanding and the stringent values of alpha imposed by the Šidàk’s method, the heterogeneous effect of raising the NRA is confirmed. A rise in the NRA causes the largest reduction on workers with the lowest wage, occupational grade, and health and an intermediate reduction among those with the mid occupational grade, wage, and health, suggesting the presence of a clear socio-economic gradient: the greater the disadvantage, the greater the delay of pension claiming and the labor supply response.

Among more advantaged categories pension claiming drop was mild, and I detect a null effect on employment and inactivity rates. In contrast, the inactivity rate increased substantially among workers with low wages and low occupational grades, for whom the increase of inactivity exceeds the employment response.

Not much heterogeneity survives on the disability and unemployment outcomes, apart from a marginally significant higher risk of taking up disability pension benefits for people with poorer health. However, there is the possibility that I could not detect significant heterogeneous effects on these outcomes due to lack of power, since a very small proportion of individuals take up the two benefits.

A possible concern is that the characteristics used in this analysis are endogenous since they are measured at 55–59 years old, i.e., partly in the post-1992 years for the treated cohorts. However, if I measure characteristics only at 55 years and use information coming entirely from the pre-1992 period (at the expense of losing the possibility of having sick leave among the variables), the estimated effects are quantitatively the same for all the outcomes and the overall pattern is largely confirmed. Results are shown in Table D7 in Appendix.