In this section, I first show the impact of the reform on the retirement age. The parallel trends assumption is tested in Section 5.2. The main results for health care utilization and mortality are presented in Section 5.4 and Appendix A.3 analyzes heterogeneous treatment effects.
The impact of the reform on retirement
We know from the descriptive statistics in Section 4.4 that post-reform cohorts in the treatment group retire more than 5.3 months later than the corresponding birth cohorts in the control group. This section aims at quantifying the impact of the reform on retirement in more detail.
The retirement effects of the reform are perhaps best illustrated in a histogram. Figure 1 shows the retirement distribution for pre- and post-reform cohorts in the treatment group. Most evident in the left-most panel is the spike of retirements around age 63. The spike around 65 is also pronounced, which means that many workers continue to work past the age at which they become entitled to full pension benefits. The two oldest post-reform cohorts, i.e., those born in 1938 and 1939, seem to retire later than the pre-reform cohorts, but the spike around 63 is only marginally smaller. Remarkably, it almost vanishes for the 1940–1942 cohorts. These graphs provide clear evidence that the reform increased the actual retirement age.
I proceed by estimating the difference-in-difference Eq. 1 with the number of months employed between age 62 and 68 on the left-hand side:
$$ R_{i,j,s} =\alpha + \psi \left( LG_{s} \times CH_{j \in [1938,1942]} \right) + \phi LG_{s} + \lambda_{j}+ \textbf{X}_{i,j,s}\theta + u_{i,j,s} $$
(2)
The common treatment effect, \(\hat {\psi }\), is presented in column (1) of Table 4. Column (2) presents the results when we allow for heterogeneous effects across birth cohorts, i.e.:
$$ R_{i,j,s} = \alpha+ \sum\limits_{j} \psi_{j} \left( LG_{s} \times CH_{j \in [1938,1942]} \right) +\phi LG_{s} + \lambda_{j}+ \textbf{X}_{i,j,s}\theta + e_{i,j,s} $$
(3)
The common treatment effect amounts to 4.5 months and column (2) shows that this effect is largely driven by the youngest cohorts. For example, those born in 1942 retire more than 6.2 months later than the pre-reform cohorts as compared to 1.4 months for those born in 1939.
Table 4 The impact of the reform on retirement
How can we be sure that this movement in the retirement mass is not only the result of a general trend towards longer working lives? Figure 2 shows retirement distributions for the control group. Except for a slight decrease in the mass of retirements at ages 62 and 63, little seems to happen across these birth cohorts. I also estimate pre-reform trends for the retirement age in a similar fashion as for health in the previous section. Column (3) of Table 4 reports the estimation results after adding two interaction terms between pre-reform cohort j = 1935,1936 and the local government dummy to the specification in column (2). The estimated coefficients imply that local government workers born in 1935 and 1936 retire 0.5 and 1.1 months earlier than those born in 1937, respectively, accounting for the corresponding change in the control group. The coefficient for the 1935 cohort is significant at the 10 % level while the coefficient for the 1936 cohort is insignificant. These results support the interpretation that the first-stage effects are the result of the reform itself rather than a differential underlying trend in retirement age between the treatment and control group.
There are several plausible explanations for the between-cohort differences in labor supply response observed in columns (2) and (3). First, if norms adjust slowly in response to a change in the NRA, we should expect the labor supply adjustments to increase over time. In this specific case, though, the importance of norms should not be exaggerated. Sixty-five was already the NRA in all other major occupational pension plans as well as in the public pension system. Second, an immediate adjustment in response to changes in incentives could be prevented by adjustment costs or frictions (Gelber et al. 2013). Although the financial incentives to retire before 65 changed very quickly with the reform, there might be large non-financial costs of changing the retirement plans on short notice. Such costs should be higher for older cohorts that received news about the new rules just before they reached their intended retirement age.
Table 13 shows the first-stage effects for the alternative retirement definitions. Columns (1) and (2) show that the reform also had a significant impact on claiming behavior. The common treatment effect of 0.49 translates into an increase in the actual claiming age of 5.9 months. The income-based definition of retirement yields an estimate of 0.37 years or 4.4 months. Again, we see that the effect is driven by the youngest cohorts. Thus, these results verify that the reform effect on employment is robust to various definitions of retirement.
Can we say something about the characteristics of those who postpone their retirement date as a result of the reform (commonly referred to as the “compliers”)? Following Angrist and Pischke (2008), Table 5 reports the relative likelihood a complier has the characteristic indicated in the column heading. We see that compliers are relatively similar to other individuals in terms of marital status, pre-retirement income level and work amount (part-time vs. full-time). Instead, compliers are more likely to be in worse health (as measured by sickness absence and hospitalizations prior to the age of 60). They are also more likely to have a retired spouse than other married individuals, which provides evidence in favor of the complementarity-in-leisure hypothesis. Finally, compliers are less likely to have finished only elementary school.
Table 5 Complier characteristics ratios
Identifying assumption
The parallel trends assumption implies that the outcome variable evolved in the same way in the treated group as in the control group in absence of the reform. Figure 3 plots series of average outcomes for the treatment and control group before and after the reform for the main health measures. The two top panels show that the probability of being prescribed a non-zero quantity of prescription drugs and the total purchase of drugs evolved similarly for pre-reform cohorts in the two groups. The lower panels show that post-retirement hospitalization and mortality rates also seem to satisfy the parallel trends assumption. It is also reassuring that the levels are similar across the two groups.
We can test the parallel trends assumption more formally by estimating pre-reform trends in the difference-in-difference framework. Specifically, I extend Eq. 1 by adding two interaction terms between the local government dummy and cohorts j = 1935,1936. For the parallel trends assumption to hold, the estimated δ
j
coefficients for these two cohorts should be close to zero and insignificant. Table 6 reports the estimation results for the health outcomes shown in Fig. 3. There are 14 estimates in total and only one of them is significant (at the 10 % level). This supports the assumption that health developed similarly in the treatment and control group prior to the reform.
Table 6 Estimation of parallel trends
As mentioned in Section 3.2, the 1938 and 1939 cohorts could avoid the new rules by retiring prior to the reform. Such anticipatory behavior might be a problem to the identification strategy if it changed the composition of the treatment and control group in a way that is related to health. The preferred way to test for this would be to apply a similar DD framework as in the main analysis and look specifically at retirement behavior at ages 60–61 for the affected cohorts. However, a simultaneous reform in the public pension system makes such an analysis difficult. In 1998, the minimum claiming age in the public pension system was raised from 60 to 61 (Palme and Svensson 2004). As a result, individuals born in 1938 had to wait an additional year before they could claim public pension benefits. In contrast to private sector workers who were directly exposed to the new minimum claiming age, local government workers were unaffected by this reform as long as they retired under the pre-reform rules. Thus, we would not know to what extent a DD estimator would reflect anticipatory behavior among local government workers on the one hand, and later retirement among private sector workers on the other. Instead, I do two things to deal with this issue. First, by conditioning on being employed for 12 full months in the year of their 61st birthday, I exclude most individuals who potentially retire in anticipation of the reform. Second, I test whether the results are robust to excluding the 1938 and 1939 cohorts. These robustness tests, along with several others, are provided in the Appendix.
Income effects
One important aspect of estimating the health effects of reforms that promote later retirement is that these effects may operate through changes in lifetime income.Footnote 16 To illustrate the effect of the reform on lifetime income, I replace the dependent variable in Eq. 1 with log disposable income at age a and estimate it for ages a = 61,...,69. The difference-in-difference estimates from these regressions are shown in Fig. 4. There is a positive and significant effect on disposable income of about 2–5 % at ages 63–66, which corresponds to an annual increase in disposable income of SEK 3,500 to SEK 8,500. This reflects the increased labor supply at ages 63–64 and the corresponding difference between labor earnings and pension benefits. From age 67, the effect is negative and barely statistically different from zero. Remember that the transition rule explained in Section 3.2 implied that the pension wealth at age 65 was more or less unchanged for the first post-reform cohorts. The conclusion from these results is that the income effects should be rather small and that potential health effects are more likely to operate through other channels.
The impact of the reform on health
The results from estimating Eq. 1 are presented in Table 7. The reported coefficients measure the reform effect on each of the health outcomes given in the column headings.
Table 7 Effects on prescription drugs, inpatient care, and mortality
I find no effect on the utilization of prescription drugs. The extensive margin outcomes in columns (1) and (3), i.e., the probability of being prescribed a non-zero quantity of any drug or any mental drug, respectively, are insignificant and close to zero. The same is true for the intensive margin results in columns (2) and (4). In relative terms, the effect sizes range between −0.5 and 1.55%. The estimates for inpatient care and mortality are also insignificant and close to zero. The coefficient in column (7) implies that the reform increased the probability of dying before the age of 69 by 0.16 % points, which translates into a small relative effect of 3.68 %.
Even if all estimates are insignificant, we cannot rule out that later retirement has an impact on health. A key issue in ruling out effect sizes of important magnitude is the precision of the estimates. The extensive margin drug and hospital outcomes are estimated with high precision. The relative effects associated with the 95 % confidence intervals consistently range within a few percentage points around zero. The intensive margin results have lower precision. For example, the 95 % confidence interval of the estimate for the number of hospital days in column (6) corresponds to relative effects of −12.9 to 6.3 %. For mortality by age 69, the corresponding interval ranges from −7.4 to 14.8 %. Given that only 4.4 % of the individuals in the sample are deceased by age 69, it comes as no surprise that the standard error of the mortality estimate is quite large. I come back to the issue of precision in Section 9.
Next, I explored in detail the diagnoses codes to see whether the small effects on health care utilization and mortality mask any heterogeneous effects with respect to the hospitalization cause. I examine five medical causes based on their known relationship with retirement in the previous medical and health-economic literature. These include heart disease, cerebrovascular disease (stroke), diseases of the musculoskeletal system, lifestyle diseases (diabetes and alcohol/tobacco related diseases) and mental health. Diseases of the circulatory system (e.g. hypertension, myocardial ischemia and stroke) can often be related to stress and are often caused by correctable health-related behavior, such as an unhealthy diet, lack of exercise, being overweight, and smoking. I therefore complement this analysis by examining health events that are directly related to alcohol and tobacco consumption as well as type 2 diabetes.Footnote 17 Diseases of the musculoskeletal system are included to investigate whether postponing retirement has an effect on physical body functions. The mental health category includes drugs that treat psychosis, depression, anxiety and sleeping disorders.
Mortalities and hospital admissions are readily classified into each of these causes using the ICD codes. The ATC codes are then used to classify prescription drugs into categories that closely resemble the ICD classification. The aggregation of the ICD and ATC codes are described in Table 11.Footnote 18
To mitigate problems with multiple hypothesis testing, I combine information on cause-specific mortalities and health care utilization to create health indexes for each of these medical categories. First, I invert each outcome so that a higher value represents a better outcome. Then, I standardize each modified outcome by subtracting the control group mean and dividing by the control group standard deviation. Finally, I take an equally weighted average of the standardized outcomes. Table 8 presents the estimation results.
Table 8 Cause-specific health indexes
Again, the overall result is that the reform had no impact on post-retirement health. The only statistically significant coefficient is the coefficient related to cerebrovascular disease (significant at the 10 % level). Because a higher index value indicates a better outcome, the positive estimate implies that the reform reduced health problems related to cerebrovascular disease. This results suggests that continued work at older ages might provide individuals with better opportunities to preserve a healthy lifestyle than retirement since many of the risk factors for cerebrovascular disease are related to lifestyle. However, this result should be interpreted with caution because there is no direct effect on diabetes and alcohol/tobacco related diseases.
The effects of retirement on health
Up until now, I have focused on the effects of the reform on health (i.e., the intention-to-treat effect). However, as discussed in Section 2, previous studies have focused on the effects of retirement on health. To better relate to these studies, I estimate the health effects of postponing retirement in an Instrumental Variable framework, where the endogenous employment variable is instrumented by several interaction terms between being born in 1938 or later and working in the local government sector. This means that I estimate the causal effect for those individuals who postpone retirement due to the reform, i.e., the compliers. Assuming heterogeneous effects of postponing retirement on health, the 2SLS estimator estimates the local average treatment effect (LATE) instead of the average treatment effect (ATE). The coefficient of interest reflects the reform effect on the number of months employed before exiting the labor market, comparing local government workers born in 1938 or later to private sector workers in the same birth cohorts. The 2SLS estimates for the main outcomes and the cause-specific health indexes are presented in Tables 9 and 10, respectively.
The OLS estimates reflect the negative correlation that is typically observed between retirement age and health (those who retire early tend to be in worse health), but cannot be used to make any causal claims about the effect on retirement on health due to non-random selection into retirement. When health selection into retirement is controlled for, the negative relationship between retirement age and health disappears. All 2SLS estimates, but one (“any drug”), are statistically insignificant. These results are thus largely in line with the intention-to-treat effects.
Table 9 Results from the estimation (OLS and 2SLS) of linear regression models of health care utilization and mortality on employment
Table 10 Results from the estimation (OLS and 2SLS) of linear regression models of cause-specific health care utilization and mortality on employment
As discussed previously, a key issue in ruling out effect sizes of important magnitude is the precision of the estimates. The 2SLS estimation allows me to compare the precision of the mortality estimates to those of two previous studies. The most comparable study is Hernaes et al. (2013) who investigate the mortality effects of lowering the early retirement age for a group of Norwegian workers using a similar difference-in-difference strategy as in this paper. They find that a 1-year increase in the actual retirement age results in a 0.2 % point increase in mortality by age 70 (insignificant), which is somewhat smaller than what I find for mortality by age 69 (0.34 % points).Footnote 19 The effects are, however, estimated with similar precision. Hernaes et al. (2013) report a 95 % confidence interval that ranges from − 0.78– 1.18% points compared to −0.73 to 1.41 in this study. In another related study, Kuhn et al. (2010) find that the introduction of more generous early retirement rules for Austrian blue-collar workers had a significant effect on mortality among male workers, but no effect among female workers. For women, Kuhn et al. (2010) report that one additional year spent in early retirement results in a 0.02 % point increase in mortality at age 67. The effect is thus very close to zero, but the confidence interval ranges from −1.84 to 1.88 % points.Footnote 20