The effects of increasing the normal retirement age on health care utilization and mortality

3.1 Retirement benefits in Sweden

Sweden’s pension system has two main pillars, a universal public pension system and an occupational pension system. Swedish retirees generally receive most of their pension income from the public pension system, but the occupational pension system is an important complement. The occupational pension system consists of a number of different pension plans that are negotiated at the union level and cover large group of workers. In fact, the four largest agreement-based occupational pension plans cover around 90 % of the total work force. These include the pension plan for blue-collar private sector workers, white-collar private sector workers, local government workers, and state-level government workers, respectively. The focus of this study is the pension plan for local government workers.

3.2 The occupational pension reform for local government workers

The pre-reform occupational pension plan for local government workers, called PA-KL, covered local government workers born before January 1, 1938. PA-KL was defined benefit and directly coordinated with the public pension system. PA-KL stipulated that the sum of the annual occupational pension benefit and the public pension benefit should amount to a certain fraction of the individual’s pre-retirement income. The occupational pension would always pay out the residual amount net of the public pension benefit to reach a certain replacement rate. In year 2000, the gross replacement rate amounted to 73 % for a female local government employee with an average wage rate who retired at the age of 63. If the public pension accounted for 60 %, the occupational pension benefit would amount to 13 % of her qualifying income. Thus, local government workers only needed to know about the gross replacement rates to get a full picture of their retirement income.⁴

In the pre-reform pension plan, the age at which full or unreduced retirement benefits could be withdrawn, i.e., the normal retirement age (NRA), was different for different occupations. The NRA was either 63 or 65. Early withdrawals could be made from the age of 60, but the penalty rate at a given claiming age, i.e., the reduction in the gross replacement rate, was different depending on what NRA the worker faced. Here, I focus on workers who had a NRA of 63.

Workers who faced a NRA of 63 could retire at this age with a full benefit. The benefit was not actuarially increased for claims made after 63, which means they had little incentive to work past this age. Selin (2017) shows that an individual with median earnings who chose to work an additional year at age 63 lost benefits amounting to 71% of the current wage after discounting (the benefit accrual). In comparison, a private sector worker of similar age and with similar earnings faced a positive accrual rate of 10%. Broad categories of workers had a NRA of 63, including personal care workers, nurses, pre-school teachers, restaurant service workers, and cleaners.

In 1998 a new agreement, PFA98, was signed for Swedish local government workers. The most important change was that the NRA was set to 65 for all local government workers. This was achieved by introducing equal early retirement penalty rates for all occupations. The new penalty rates implied that the pension was reduced by 0.4 % per month of retirement before age 65. Rather than receiving a full benefit, retiring at age 63 as compared to 65 now implied a substantial benefit reduction of 9.6 % (0.4*12*2 = 9.6).

The reform implied a partial shift from defined benefit to defined contribution.⁵ This meant that the individual could always increase her pension wealth by postponing retirement until the age when she was obliged to retire or until no more pension rights could be earned. The shift was part of a general trend in favor of defined contribution systems. Thus, when the public pension system was reformed, see Section 3.3 below, it was natural to adjust the rules of the pension plan for local government workers as well.

While the reform substantially increased the incentives to postpone retirement beyond the age of 63, it did not change the stock of already accumulated occupational pension wealth. The reason for this was a transition rule that would compensate workers in post-reform cohorts for potential benefit reductions due to the new rules. The pension wealth earned up to December 31, 1997, was converted into a life annuity that corresponded to the annual pension benefit that the individual would have received if she had retired by that date. Pension rights earned after this date were accredited the new pension plan. If the resulting pension from these two components was lower than the corresponding pension in the absence of a reform, workers received the difference from the employer. As a result, the pension wealth at age 65 was more or less unchanged for the transition cohorts. Importantly, workers who retired before 65 were not eligible for this compensation, which implies that the most important effect of the reform was to raise the NRA from 63 to 65 for workers who had a NRA of 63 in the pre-reform pension plan. Naturally, the transition rule also implied that the new DC component became relatively more important for younger cohorts.

The new PFA98 agreement came into effect on January 1, 2000, for those born in 1938 or later. Those born in 1937 and earlier were completely unaffected by the occupational reform and would still be covered by the old plan. The reform was implemented rather quickly and without much media coverage.⁶ Local government workers could avoid the new rules by retiring prior to the implementation of the new pension plan on January 1, 2000. Given that the reform was agreed on in mid-1998, those born in 1938 and 1939 were given some room to retire under the old rules.

3.3 The public pension system and private sector pension plans

The first post-reform cohort in the empirical analysis, i.e., those born in 1938, are also the first cohort to participate in the new public pension system. The new system is notional defined contribution (NDC) and has been described by, e.g., Sundén (2006). The 1938 cohort receives one fifth of its benefit from the new system and four fifths from the old system. Each cohort then increases its participation in the new system by 1/20, so that those born in 1954 will participate only in the new system (Hagen 2013). Thus, the differences in financial incentives between adjacent cohorts are relatively small due to the gradual phase-in of the new pension system. Benefits from the new system were paid out for the first time in 2001, 3 years after it was legislated.

The 1938 cohort was also the first to be affected by the 2001 increase in the mandatory retirement age. Before 2001, most central agreements between trade unions and and employers’ associations had a stipulated retirement at the 65th birthday. Workers could work past this age, but only if the employer approved. From 2001, mandatory retirement ages below 67 were no longer allowed to be agreed on. The new legislation affected both private and public sector employees and there seem to have been very small effects of the reform on labor force participation rates (Laun and Palme 2017). This reform could, however, have affected the long-term trend towards increased labor force participation of 65–69-year-old females.

The control group is made up of private sector workers. There are two large occupational pension plans in the private sector: one for blue-collar workers (SAF-LO) and one for white-collar workers (ITP). The ITP plan was mainly defined benefit and the same rules applied to all birth cohorts studied in this paper. The SAF-LO plan, on the other hand, is a pure defined contribution scheme. The implementation of the SAF-LO plan in 1996 implied that blue-collar workers born between 1932 and 1967 were subject to special transitional rules. However, cross-cohort differences in retirement incentives are minor because of the long transition period. Importantly, all private sector workers in the relevant birth cohorts faced a normal retirement age of 65.

4.1 Methodological framework

4.2 Data on retirements

Individual demographics and labor market information is collected and maintained by Statistics Sweden. The Longitudinal Database on Education, Income and Employment (LOUISE) provides demographic and socioeconomic information. The data covers the entire Swedish population between 16 and 65 during the period 1987–2000, and individuals aged 16 to 74 between 2001 and 2010. The population of interest is local government workers whose NRA was increased from 63 to 65 in 2000. The main sample analyzed is composed of individuals born between 1935 and 1942. Those born in 1938 were the first ones to be affected by the new rules. The control group is made up of private sector workers in the same birth cohorts. The private sector workers faced a normal retirement age of 65 both before and after the local government pension reform.

Importantly, there is information in the data which allows me to distinguish these workers from other workers in the local government sector who had a NRA of 65 both before and after the reform. I use the Swedish Standard Classification of Occupations (SSYK-96) to identify workers in occupations who had a NRA of 63.⁷ Individuals who are observed working in any of these occupations between ages 61 and 63 are included in the treatment group. I identify workers with a NRA of 65 in the same way. If an individual is observed working in both occupation categories, I use the most recent observation to determine the NRA. SSYK codes are available from 1996, which means that those born in 1935 is the oldest cohort for whom occupation status is known at age 61.⁸ I define someone as working in the private sector if she has not been employed in the public sector between ages 61 and 63. It is more difficult to determine private sector affiliation from the data. The data which contain the SSYK codes only contain a small representative sample of private sectors workers (around 23 %). In contrast, the universe of public sector workers is included in this data.

I make four restrictions to the sample of local government and private sector workers born between 1935 and 1942. First, because the affected worker categories in the local government sector were dominated by women, male workers are excluded from the analysis. In fact, only 3 % of these workers are men. Second, I restrict the analysis to individuals registered as employed for 12 full months in the year of their 61st birthday. This restriction ensures that I observe at least one SSYK code for each local government worker. In order for the SSYK code to be reported, the individual must be employed during the “reference month,” which typically occurs at the end of the year. In effect, this restriction implies that the first month in which individuals are allowed to retire is the month in which they turn 62. It does not, however, rule out part-time work. A part-time worker might well be registered as employed for 12 full months in a given year. At age 61, the sample of local government workers are approximately evenly split between working full-time, more than 75 % but less than full-time, and less than 75 %, respectively. Third, I restrict the sample to individuals who have 5 years of consecutive employment prior to age 61 (at any work place).⁹ Finally, I also exclude individuals who are registered as self-employed at some point between ages 61 and 63. The final sample consists of 133,026 individuals of whom 57,415 are local government workers.

The retirement definition reflects the month in which an individual retires completely from the work force. This definition uses records of employment spells, which are obtained from the Register-Based Labor Market Statistics (RAMS). The information in RAMS is based on reports that all employers submit to the Swedish Tax Agency. For each employee, the employer must report how much wages and benefits have been paid out, how much taxes have been drawn and, most importantly, during which months the employee has been employed at the firm. This information allows me to infer in what month and year an individual exits the labor market. The decision to retire is equated with the month in which the individual’s last employer reports the employment contract to be officially ended. The outcome variable in the first-stage analysis on the retirement effects of the reform is defined as the number of months an individual is registered as employed between ages 62 and 68. The upper limit of age 68 is chosen because it is the oldest age to which the youngest cohort can be tracked.¹¹

I use two alternative measures of retirement. According to the first alternative definition, individuals who receive a positive amount of occupational pension income are classified as retired. The second definition is income-based. According to this definition, the individual retires the year before her annual earnings fall below 1 price base amount (≈ USD 5900 in 2010). I use the record-based definition of retirement as my main definition of retirement because it much better captures the individual’s actual exit from the labor force than the other two. Yearly fluctuations in income due to e.g. sickness or part-time work might cause individuals to cross the income-based threshold of retirement at multiple occasions. Moreover, an individual who has started to collect pension income might still work. Occupational pension benefits can typically be withdrawn if the hours of work are reduced accordingly, and the new public pension puts no restriction on the amount of work individuals can work while collecting pension. One potential drawback of the record-based definition is that too much emphasis is put on economically unimportant spells of employment after the individual has quit her “real” job. However, as we will see, the reform caused a significant movement in the mass of retirements at the age at which we would expect to the see the largest effects, i.e., age 63. In addition, all three definitions produce similar effects on the retirement age.

4.3 Data on health care utilization and mortality

I study mortality outcomes and two major types of health care utilization: hospitalizations and purchase of prescription drugs. Three register-based data sources are used for this purpose.

The analysis of drug prescriptions are based on data from the Prescription Drug Register, which contains information about all over-the-counter sales of prescribed medical drugs between 2005 and 2009. For each occasion when a prescription drug was bought, the data contains detailed information about the Anatomical Therapeutic Chemical (ATC) code of the drug, and the number of defined daily doses (DDDs) purchased over the entire period. The analysis of mortality is based on information from the Cause of Death Register. Causes of death are classified using the International Classification of Diseases (ICD). Hospitalizations are studied using information about inpatient care available in the National Patient Register.¹² For each hospitalization event, the register has information about the arrival and discharge date, and diagnoses codes in ICD format. Inpatient records exist from 1964 to 2010, while the mortality data ends in 2011.

The analysis focuses on the extensive and the intensive margins of health care utilization. For the extensive margin, I define a set of binary outcome variables that equal 1 one if the individual is prescribed a non-zero quantity of drugs or is hospitalized for at least one night during a pre-specified time period. The intensive margin outcome variables for drug prescriptions are given by the product of the DDD per package and the number of prescribed packages, summed over the years 2005–2009 for each individual (expressed in thousands). Information on the number of days spent in hospital is used to construct intensive margin outcomes for inpatient care. The intensive margin adds important variation to the quantity of consumed health care, especially for individuals with previous records of health care utilization.

Because the different health registers cover different years, the pre-specified time period over which health outcomes are defined will vary across the type of health event. The mortality data ends in 2011, which means that the maximum age up to which all cohorts can be tracked is 69. The outcome variable is thus set equal to 1 if the individual died before reaching this age. The hospitalization outcomes are based on an individual’s hospital admissions between ages 65 and 68. Age 65 is chosen as the lower age limit because our primary interest lies in estimating the effects on health care utilization after the individual is retired. Finally, all drug outcomes are based on prescriptions made between 2005 and 2009.

A concern with using health care data is that the utilization of health care might reflect other factors than the need for health care. One such factor is ability to pay. In principle, receiving care must not be influenced by the ability to pay since most medical service expenses in Sweden are covered by taxes. There is, however, evidence that there exists pro-rich inequity in the utilization of health care (Van Doorslaer et al. 2000; Van Doorslaer et al. 2004). I diminish this risk by studying both the purchase of prescription drugs, where such inequity is likely to play a role, and outcomes severe enough to require hospital inpatient care. Another potential factor are differences in time availability between retirees and workers. Those who work longer as a result of the reform face a higher non-monetary cost of seeking health care. To make sure that the treatment and control group face similar time constraints, I focus on health care received after the age of 65 when most individuals are retired.¹³ Again, focusing on severe outcomes that either require inpatient care or lead to death should also play down the importance of help-seeking behavior associated with time availability.

4.4 Descriptive statistics

The first row shows that post-reform cohorts in the treatment group retire about 5.4 months later than the pre-reform cohorts. The corresponding difference in the control group is very small, which yields a raw difference-in-differences estimate of 5.3 months. This is strong preliminary evidence that the reform had a positive impact on the retirement age. The second and third rows show that similar results are obtained for the two alternative measures of retirement. Since these definitions are measured at the yearly level, the raw difference-in-difference estimate in the second row of 0.56 reflects an increase in the claiming age of more than 6.5 months. The income-based definition of retirement reflects a smaller, yet sizable, effect of about 3 months.¹⁴

Table 3 shows that the two groups are similar in terms of several background characteristics, including marital status, the probability of having children (of any age) at home and immigrant status. The two groups also have similar pre-retirement health status. Sickness absence, measured as the number of years an individual has been absent from work for more than 14 consecutive days between ages 56 and 60, is only marginally higher in the treatment group, just like the probability of having been hospitalized during the same period.¹⁵ Differences apply mainly to education level and pre-retirement earnings. Local government workers have, on average, 0.5–0.6 years more of schooling and somewhat higher pre-retirement earnings than the private sector workers. The income distribution of the local government workers is, however, more compressed.

Turning to our health outcomes, we see that around 30 % of the local government workers are hospitalized for at least one night between ages 65 and 68. The private sector workers exhibit very similar hospitalization rates. The differences amount to less than 1 % point. The two groups are also similar with respect to drug purchase. More than 90 % of the individuals in the pre-reform cohorts are prescribed a non-zero quantity of drugs between 2005 and 2009. Around 40 % are prescribed mental drugs. Note, however, that the cross-cohort decline in drug purchase and hospital admissions is larger in the treatment group than in the control group (as indicated by the diff-in-diff estimator in column (7)). The opposite pattern is seen for our two measures of mortality, i.e., the probability of being dead by the age of 69. In sum, it is difficult to draw any conclusions about the existence of an effect of the reform on mortality and health care utilization based on these raw difference-in-difference estimates.

5.1 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.

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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.

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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.

5.2 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.

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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.

5.3 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.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.

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5.4 The impact of the reform on health

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.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 11.¹⁸

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.

5.5 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.

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).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.²⁰