Avoiding blunders involving 'immortal time'

As Groucho Marx once said ‘Getting older is no problem. You just have to live long enough’. (Queen Elizabeth II, at her 80th birthday celebration in 2006) This award proves one thing: that if you stay in the business long enough and if you can get to be old enough, you get to be new again. (George Burns, on receiving an Oscar, at age 80, in 1996) (Richard Burton died, a nominee 6 times, but sans Oscar, at 59. Burns lived to 100, so how much of the 41 years’ longevity difference should we credit to Burns’ winning the Oscar?) Some time ago, while conducting research on U.S. presidents, I noticed that those who became president at earlier ages tended to die younger. This informal observation led me to scattered sources that provided occasional empirical parallels and some possibilities for the theoretical underpinning of what I have come to call the precocity-longevity hypothesis. Simply stated, the hypothesis is that those who reach career peaks earlier tend to have shorter lives. (Stewart JH McCann. Personality and Social Psychology Bulletin 2001;27:1429–39) Statin use in type 2 diabetes mellitus is associated with a delay in starting insulin. (Yee et al. Diabet Med 2004;21:962–67) For almost two centuries, teachers have warned against errors involving what is now called ‘immortal time.’ Despite the warnings, and many examples of how to proceed correctly, this type of blunder continues to be made in a widening range of investigations. In some instances, the consequences of the error are less serious, but in others the false evidence has been used to support theories for social inequalities; to promote greater use of pharmaceuticals, medical procedures and medical practices; and to minimize occupational hazards. We use a recent example to introduce this error. We then discuss: (i) other names for it, how old it is and who tried to warn against it; (ii) how to recognize it, and why it continues to trap researchers; and (iii) some statistical ways of dealing with denominators measured in units of time rather than in numbers of persons. Patients whose kidney transplants (allografts) have failed must return to long-term dialysis. But should the failed allograft be removed or left in? To learn whether its removal ‘affects survival’, researchers1 used the US Renal Data System to study ‘a large, representative cohort of [10 951] patients returning to dialysis after failed kidney transplant’. Some 1106, i.e. 32% of the 3451 in the allograft nephrectomy group, and 2679, i.e. 36% of the 7500 in the non-nephrectomy group, were identified as having died by the end of follow-up. Patients in the two groups differed in many characteristics: to take into account a ‘possible treatment selection bias’, the authors constructed a propensity score for the likelihood of receiving nephrectomy during the follow-up. They used this together with other potential confounders to perform ‘multivariable extended Cox regression’’. The main finding of these analyses was that ‘receiving an allograft nephrectomy was associated with a 32% lower adjusted relative risk for all-cause death (adjusted hazard ratio 0.68; 95% confidence interval 0.63 to 0.74)’. In their discussion, the researchers suggest that their findings of ‘improved survival’ after allograft nephrectomy ‘challenge the traditional practice of retaining renal allografts after transplant failure’. The title of the article (‘Transplant nephrectomy improves survival following a failed allograft’) suggested causality. They emphasized the large representative sample and the extensive and sophisticated multivariable analyses, but they did caution that ‘as an observational study of clinical practice, their analysis remains susceptible to the effects of residual confounding and treatment selection bias’ and that ‘their results should be viewed in light of these methodologic limitations inherent to registry studies’. They suggested that a randomized trial to evaluate the intervention in an unbiased way would be appropriate. Similar concerns about residual confounding and selection bias, and the need for caution, were expressed in the accompanying editorial reiterating the limitations of the ‘retrospective interrogation of a database’. ‘Residual confounding’ may be a threat, but both authors and editorialists overlooked a key aspect of the analysis, one that substantially distorted the comparison. The overlooked information is to be found in the statements that: 3451 received nephrectomy of the transplanted kidney during follow-up; the median time between return to dialysis [the time zero in the Cox regression] and nephrectomy was 1.66 yr (interquartile range 0.73 to 3.02 yr). (Paragraph 1 of Results section) Overall, the mean follow-up was (only) 2.93 ± 2.26 yr. (Paragraph 3 of Results section) Since the 3451 patients who ultimately underwent a nephrectomy (the ‘nephrectomy group’) had to survive long enough to do so (collectively, approximately 6700 patient-years, based on the reported quartiles of 0.73, 1.66 and 3.02 years), there were, by definition, no deaths in these 6700 pre-nephrectomy patient-years. In modern parlance, these 6700 patient-years were ‘immortal’. There was no corresponding ‘immortality’ requirement for entry into the ‘non-nephrectomy group’. Indeed, all 10 951 patients returning to dialysis after failed kidney transplant began follow-up with their ‘failed graft in place’. Some 7500 of these remained in that initial state until their death (for some, death occurred quite soon, before removal could even be contemplated) or the end of follow-up, whereas the other 3451 spent some of their follow-up time in that initial state and then changed to the ‘failed graft no longer in place’, i.e. post-nephrectomy, state. How big a distortion could the misallocation of these 6700 patient-years produce? The article does not have sufficient information to re-create the analyses exactly. Figures 1 and 2 show a simpler hypothetical dataset which we constructed to match the reported summary statistics quite closely. It was created assuming no variation in mortality rates over years of follow-up or between those lived in the two states. The ‘virtual’ intervention was set up ‘retroactively’ and was limited to the dataset itself, rather than to real individuals, and so could not have affected (other than randomly) the mortality rates in the person-years lived in each state. Excerpts from the simulated mortality experience in the contrasted (‘organ intact’ vs ‘organ removed’) states. Hypothetical lifelines were generated to have an average mortality rate of 3785 deaths in (10 951 × 2.93 = 32 086) patient-years (PY), i.e.,11.8 per 100 PY (as in the actual nephrectomy study1), but with no variation over years of follow-up, and no difference (other than random) between states (‘name intact’ or ‘name removed’). We constructed the dataset by first generating names for 10 951 fictional persons, then distributing the numbers of new cohort entries in a smooth decreasing pattern over the 11 calendar years, and then applying the death rate of 11.8 per 100 PY to the various resulting lengths of available follow-up, until the total number of deaths matched the reported 3785 and the number of PY of follow-up matched the reported 32 086. The 10 951 hypothetical lifelines (3785 completed, 7166 censored) were then ordered from shortest to longest. Finally, starting from the day of return to dialysis and working forward, each follow-up day a number of persons were chosen randomly from among those who had not already been selected, were still alive and were being followed that day. These persons were designated to undergo an electronic ‘removal’ whereby, within the database, just their names (not their failed transplants) were (electronically rather than surgically) removed. The timings of these ‘removals’ (3471 in all) were set so that the median and quartiles of the delay between return to dialysis and becoming nameless matched the delays in the article. The selections, made by a random number generator in 2012, were made blindly, in a retroactive lottery, applied in a forward direction, beginning in January 1994, to lifelines that had already run up to December 2004. Just as in Leibovici16 and in Turnbull et al.,17 these interventions were limited to the 2012 computer file, and could not have affected the comparative mortality rates. Shown are 30 such lifelines selected systematically from these 10 951 ordered hypothetical ones, with a completed lifeline indicated by a single straight line, and a censored one by a pair of lines forming an arrowhead. The timing of the name removal is indicated by an x, and the post-intervention PY by red rather than grey boundary lines. Mortality rates and rate ratios produced by the (A) mis- and (B) proper allocation of pre-‘intervention’ patient years. As explained in Figure 1, the hypothetical data for the 10 951 patients were constructed to have an average mortality rate of 3785 deaths in (10 951 × 2.93 = 32 086) patient-years (PY), i.e. 11.8 deaths per 100PY (as in the actual study), but with no variation over years of follow-up, or between states (no, or pre-‘intervention’ (white background) and post-‘intervention’ (pink background). Indeed, the selection of those who changed states (from white to pink polygon, in B) was made at random, and retroactively. The time location (relative to when the allograft failed) of each death is indicated by a black dot. In B, upper panel, the number being followed at any time is smaller than 3451 because some who had received the ‘intervention’ were already dead before the last ones received it. Figure 2A shows that even though the data were generated to produce the same mortality rate of 11.8 per 100 PY (person-years) in the person-years in the initial and post-‘intervention’ states, the inappropriate type of analysis used in the paper, applied to these hypothetical data, would have resulted in a much lower rate (6.4) in the ‘intervention group and a much higher one (17.1) in the ‘non-intervention’ group. The reason is that none of the 1031 deaths post-‘intervention’ could have occurred, and none of them did occur, in the pre-‘intervention’ PY that are in the to the rate of the 1031 post-‘intervention’ deaths occurred in the post-‘intervention’ the deaths occurred not in but rather in the much of = PY lived in the initial state. The of the PY from the led to the higher than it should have of it was because of these PY they had already that the 3451 patients to have the in other it may not have been that they lived longer because they underwent the but rather that they underwent the ‘intervention’ because they long enough to undergo it. can with some for long of they this bias’ in a suggested that the mortality in could be reported the who die have In this of the data, with no the inappropriate analysis led to an rate ratio of = The corresponding of and an ‘improved survival’ of at years the first 11 years of the of vs years), would have been as having been produced by the whereas they are of the misallocation of the Figure shows an of mortality rates in states. of to the state in which the death would have been should it at that the rates are from random the theoretical rates used to these hypothetical The theoretical rates as over the follow-up years. In the PY in each of follow-up time would be by who were almost one older than the who PY the and so the mortality rates in would be the person-years in the post-‘intervention’ state are a summary rate ratio matched of follow-up time would be than a rate would need to match the person-years on As the between with its on the time and with its on the time does not these but the end of this we a to some we on this against this error at to the when and that: and are by persons in it no of to that mean age at or the age at which the number of deaths be in the of and and it were an into the of the of the on that the mean age at death of and was of of of of of ages still and that the ages of and of of years’ and differed to an or greater a may no be made on of those but and whose mean age at death was It would be almost to them and the of their a the reason for the longevity before they have while may die at any age from their the the of the of to in the of the of and persons in of the time during which the are first in one group and then in the that in the there were on persons and persons. The number of are within these two groups over the calendar and the are This is a so long as the two groups were during the calendar to no or But as in practice, persons are being during the of the the of time at which they the group is into years had the of to when age to age the longevity of with that of the The show that by no a but on the a at age this is it is that all are from age while in actual some do not in a and (as time allocation of follow-up time in the et al. to with into and years. the based on this in and We that the ‘immortal had been used by in the but is the first we of to have the in in examples all the allocation of such with no example of the consequences of The two of the and do have an the difference between and rates based on two groups of and persons, and state the a study has a for a of time before a is to be in the the time during which the is being should be from the of They an to the it is in this that are the ‘immortal in the title of a the Since than a and by and have the number of ‘immortal errors in this cohort in these was at the time of or a medical The were created by the patients into those who were a at some time during follow-up and those who were not in clinical but not all received it at entry to the each follow-up time is into the the of be and the it the of the In of their and use other real to the same and show the consequences of the other examples of by other of in other even with in to 1 before it received the the study of transplant the of the of an how such a blunder can be and 1 some ways to recognize time and to the associated We that some of the from the the to as a were at entry and remained when a authors to the treatment group and the group, rather than to the time when the patients were in the treatment or or states. 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