Immortal Time Bias in Observational Studies
Recent large-scale cohort studies that reported an important reduction in mortality and chronic obstructive pulmonary disease (COPD) morbidity with inhaled corticosteroids may be biased. We used a population-based cohort of Saskatchewan residents 55 years of age or over, first hospitalized for COPD during 1990 to 1997, to study this potential bias. These 979 subjects were followed for a year from discharge until their first readmission for COPD or death (389 subjects). Inhaled corticosteroid exposure was measured as any dispensing within 90 days after discharge. Cox's proportional hazards model was used to compare the time-fixed analysis employed in the recent studies with the alternative time-dependent analysis. The time-fixed adjusted rate ratio was 0.69 (95% CI: 0.55-0.86) for inhaled corticosteroid use within 90 days, whereas the timedependent rate ratio was 1.00 (95% CI: 0.79-1.26). With the time-fixed analysis, the rate ratios were affected by the length of the exposure period, decreasing from 0.98 for a 15-day exposure period to 0.51 for 365 days, but remained stable between 1.06 and 0.94 with the time-dependent analysis. Inhaled corticosteroid use after hospitalization for COPD was not found to reduce mortality and morbidity. Although observational studies can be valuable, the recent reports of reductions in mortality and morbidity with inhaled corticosteroids are biased by their inappropriate allocation of exposure and analysis of immortal time.
Keywords: epidemiologic methods; cohort studies; databases; treatment effectiveness; epidemiologic biases
Chronic obstructive pulmonary disease (COPD) affects nearly 8 million Americans over the age of 45. These subjects incurred close to 700,000 hospitalizations in 1998 (1). Moreover, the number of deaths due to COPD in the United States has more than doubled in the last 2 decades, reaching nearly 110,000 in 1998 (2). The optimal treatment of COPD remains an important challenge, and the role of inhaled corticosteroids in the treatment of COPD is highly debated (3, 4). Although a meta-analysis of several trials showed that high doses of inhaled corticosteroids reduced the decline in lung function but not exacerbation rates (5), more recent randomized trials found no benefit on lung function across all degrees of COPD severity (6-11). However, some beneficial effect was observed on the rate of exacerbations or on the use of health care resources. A meta-analysis of these latter trials summarized this reduction in the rate of exacerbation with inhaled corticosteroids but found no decrease in all-cause mortality (12).
Three recent observational cohort studies suggest that inhaled corticosteroids given after hospital discharge for COPD arc highly effective in preventing COPD morbidity and all-cause mortality (13, 14, 15). These cohort studies employed an intent-to-treat approach to emulate a randomized trial. This approach may have introduced a bias that has been documented in epidemiology, namely that arising from immortal time (16, 17). It refers to cohort studies with follow-up time during which a subject cannot, by definition, incur the outcome event under study. The inappropriate consideration of such immortal person-time, particularly when misclassified with respect to exposure, may produce biased estimates of the rate ratio.
In this paper, we show that the approach used by these previously published studies, by its exposure allocation and data analysis, introduces an immortal time bias that leads to a significant distortion of the results. We delineate the nature of the bias and assess its impact using data from another population-based cohort of patients with COPD.
Source of Data and Cohort Definition
The source population of patients with COPD was identified using the computerized databases of the Saskatchewan Department of Health. These databases were developed as a result of the universal health insurance program provided to the residents of this Canadian Province since 1975 (18). Subjects newly treated for COPD were included if they had been dispensed at least three prescriptions on at least two different dates for a bronchodilator ([beta]^sub 2^-agonist, inhaled anlicholinergic or theophylline) within a 1-year period between January 1, 1990 and December 31, 1997. Cohort entry was the date of the third prescription, at which point subjects were at least 55 years of age. Subjects with any prescriptions for bronchodilators or other asthma drugs, including inhaled corticosteroids, nasal corticosteroids, cromones (cromoglycate and nedocromil), and ketotifen, during the 5-year period before cohort entry were excluded. All subjects were followed until the date of death, the date of emigration from the province, the date of end of coverage of the health insurance plan, or December 31, 1999, whichever occurred first.
The study cohort was defined as all subjects hospitalized for COPD during this period. The first hospitalization with a primary diagnosis of COPD was selected, and cohort entry was taken as the date of discharge. all subjects were then followed for up to 1 year, in accordance with the first of the previously published studies, that we specifically replicate and refer to in this paper as "the previously published study" (13).
The outcome was the first of readmission with a primary diagnosis of COPD or death from any cause during the 1-year follow-up, whichever occurred first. In conformity with the design of the previously published study, we excluded all deaths that occurred within 30 days of cohort entry and censored all exposure information after the outcome (13).
Inhaled Corticosteroid Exposure
We identified all prescriptions of inhaled corticosteroids dispensed to the cohort members during follow-up. As in the previously published study, a subject was considered a "user" if he/she filled a prescription for an inhaled corticosteroid anytime during the first 90 days of follow-up and was considered exposed for the entire follow-up period. To illustrate the bias, we used narrower and wider time windows of 15, 30, 180, and 365 days.
We first classified person-time of follow-up as either exposed or unexposed. Person-time before the first inhaled corticosteroid prescription date was classified as unexposed to inhaled corticosteroids and exposed thereafter. This approach was compared with the intent-to-treat approach of the previously published study that classifies all person-time of exposed subjects as exposed, including the person-time prior to the first prescription.
We also used Cox's proportional hazards models to estimate the rate ratio for the time-fixed exposure definition of the previously published study. It was compared with Cox's proportional hazards model with time-dependent exposure, which considered a subject as unexposed before filling the first inhaled corticosteroid prescription and exposed thereafter. Analyses were also adjusted for age at cohort entry and sex as well as for the use of other COPD medications dispensed during the 90-day period. Finally, to show that the bias is not specific to inhaled corticosteroids, we repeated the identical analyses with inhaled [beta]-agonists.
The cohort included 1,072 subjects who were hospitalized for the first time for COPD. They were on average 73 years old at cohort entry (discharge from hospital), and 60% were male. During follow-up, 93 subjects died within 30 days of discharge and were excluded. Among the remaining 979 subjects, 158 died of any cause, and 299 were hospitalized for COPD during the 1-year follow-up. Together, there were 389 subjects who either died or were hospitalized for COPD. During the first 90 days of follow-up, 383 subjects (39% of the cohort) received inhaled corlicosteroids. These are compared with the 596 subjects who did not receive inhaled corticosteroids within 90 days of discharge (Table 1). We note that, as was observed in the previously published study (13), the users of inhaled corticostcroids are much more likely to have received inhaled [beta]-agonists, ipratropium bromide, oral corticosteroids, antibiotics, and xanthines during this same 90-day period.
Table 2 displays the person-time analysis. It indicates that the rale of readmission or death is 50% higher among nonusers than users. It shows that the missclassified analysis based on the 90-day definition of exposure produces a rate ratio of 0.66. When the immortal (and unexposed) person-time preceding exposure (30.2 person-years) is correctly allocated to the nonuse group, the crude rate ratio becomes 0.79, which is still lower than 1.
Figure 1 displays the rate of readmission or death as a function of follow-up time. The rate increases rapidly after hospital discharge to reach almost 3 per 1,000 per day and decreases by the 100th day of follow-up to around 1 per 1,000 per day. Thus, because the rate of the outcome is higher early after discharge, we can expect that a significant number of these early events will be classified as "unexposed" because they will not have the entire 90-day period to receive inhaled corticosteroids.
Table 3 presents the effect on each analysis of changing the size of the exposure time window from 15 days up to the entire year. Under the time-fixed analysis, the rate ratio decreases gradually from 0.98 for a 15-day exposure period to 0.51 for the full 365-day period. In contrast, the time-dependent analysis produces more stable rate ratios ranging from 1.06 to 0.94, with none statistically different from 1. In particular, the comparison for the 90-day exposure definition used by the previously published study of Sin and Tu indicates that the rate ratio of 0.68 (95% CI: 0.55-0.84) underestimates the corrected time-dependent estimate of 0.94 (95% CI: 0.76-1.17).
Table 4 presents a similar analysis, but using inhaled [beta]-agonists as the exposure of interest. Although the patterns are similar, the rate ratio for inhaled [beta]-agonist exposure is higher overall than for inhaled steroids. Table 5 displays the crude and adjusted rate ratios for the 90-day exposure definition. It shows that even after adjustment, the biased rate ratio (0.69; 95% CI: 0.55-0.86) for inhaled corticosteroid use still underestimates greatly the corrected rate ratio (1.00; 95% CI: 0.79-1.26).
We have shown that a major bias was present in the observational studies that suggested the effectiveness of inhaled corticosteroids in preventing readmission and all-cause mortality in patients previously hospitalized for COPD. The bias, which arises from the simplified exposure definition that inappropriately allocates exposure and immortal time, and inappropriate data analysis, produces a distorted impression that these drugs are effective by artificially increasing the rate of the outcome among "nonusers" of the drug. Our reanalysis of comparable data from another cohort of patients with COPD, from which we were able to accurately reproduce the biased analysis, indicated that the bias was large. Indeed, the proper analysis found little or no association between inhaled corticosteroid use and COPD outcomes.
The bias is the result of a combination of the inclusion of immortal person-time in the cohort and the misclassification of exposure. The bias was initiated by the exposure delinition. A user was defined by filing a prescription for an inhaled corticosteroid anytime during the 90-day span after cohort entry. This implies that a subject who was readmitted for COPD after 10 days of follow-up and did not receive a prescription for inhaled corticosteroids during this short 10-day span is considered a "nonuser" even if the patient was due to receive such a prescription after this 10-day period. Thus, subjects who incurred the outcome early after discharge (cohort entry) were less likely to be exposed, merely because the opportunity was low. As a result, we expect the rate of the outcome to be high early in this group. On the other hand, a "user" who filled his/her first prescription for inhaled corticosteroids on the 80th day of follow-up is, by definition, free of endpoints during the first 80 days. These first 80 days are thus immortal by definition. Thus, nonusers are permitted to have endpoints at anytime during the initial 90-day period, and particularly early, whereas users must receive their first prescription before the event. The bias is accentuated by the higher rate of the outcome early during follow-up. This forces a majority of these early events to be classified as "unexposed" because they will not have the same opportunity to receive inhaled corticosteroids during the first 90 days. The bias is further accentuated by misclassifying exposure because the analysis considers subjects as users, even during the time before lilting the prescription that defines them as users. Such person-time should instead be classified as unexposed until exposure begins. The bias is large because follow-up starts at discharge for all cohort members, but outcomes are forced to occur and be counted after an immortal time period imposed by exposure for the users but not for the nonusers. The result of this differential treatment of users and nonusers during the first 90 days of follow-up will be a higher than expected rate of the outcome in the nonusers, even if the drug has no effect and the rate is constant over follow-up.
The bias is corroborated by the fact that it is a function of the length of the exposure period, which was arbitrarily chosen to be 90 days in the previously published study. Indeed, the rate ratios decreased gradually from 1.0 to 0.5 as the length of the exposure period increased from 15 days (very close to discharge) to 365 days. The latter time window is identical to that used in another study published recently that suggested that there was a strong dose-response for the protective effect of inhaled corticosteroids (14). Rate ratios estimated from the proper time-dependent analysis, on the other hand, were practically unchanged. To show that this bias is not specific to inhaled corticosteroids, we repeated the analyses with another COPD drug that appeared to have no effect using this 90-day period, namely inhaled [beta]-agonists. We found exactly the same phenomenon, with the exception that subjects using inhaled [beta]-agonists do, in fact, have an increased rate of the outcome. Thus, the characteristic of this bias is to systematically underestimate the effect; it produced a rate ratio of 1.08 when in fact it was 1.67. The time-dependent analysis, which considers the proper exposure in addition to comparing subjects on the same day of follow-up, accounts for all these sources of bias.
The biased design we described was first employed in a cohort of over 22,000 elderly patients hospitalized for COPD in Ontario, Canada (13). Although this first observational study of inhaled corticosteroid effectiveness was embraced as "exciting" for COPD (19), a puzzling implication was that merely a single prescription of inhaled corticosteroids is sufficient to reduce by almost 30% the risk of death from all causes and not only from COPD. It is now evident that as used in the previously published study such unexpectedly high effectiveness is not real but is the result of bias. The same approach has also been used in several recent studies of COPD and asthma (14, 15, 20, 21). These studies may thus be subject to the same bias we describe in this paper. It may be necessary to re-evaluate the analysis of their data and thus verify the extent of this bias.
Our own observational study is also susceptible to the common biases, including confounding by indication. Indeed, inhaled corticosteroids are expected to be prescribed to patients with more severe disease, who are at higher risk of readmission or death. Thus, the finding of a rate ratio of 1.0 for inhaled corticosteroid use cannot be interpreted as an absence of effectiveness. Like all similar administrative database studies, the diagnosis of COPD was only based on criteria such as age, bronchodilator use, and, for the outcome, hospital discharge summaries. In the absence of information on smoking, symptoms, and spirometry measures, subjects in the cohorts may have been misclassified as having COPD, whereas hospitalizations may have been missed. Assuming that inhaled corticosteroid use did not affect the diagnostic classification of the outcome, we can expect that such misclassification would attenuate the rate ratio toward unity. However, the unintended yet possible inclusion of patients with asthma as patients with COPD by these administrative criteria would lead to an apparent but fallacious beneficial effect of inhaled corticosteroids in COPD. In addition, exposure was defined in a rudimentary way to remain consistent with the recent previously published cohort study (13). Indeed, once subjects filled a prescription for inhaled corticosteroids they were considered exposed until the end of follow-up, irrespective of whether they refilled it. In addition, subjects considered unexposed because they did not fill a prescription during the first 90 days may have been subsequently exposed during follow-up. Thus, even our time-dependent analysis with a 90-day exposure window is subject to missclassification that tends to attenuate the rate ratio toward 1. For these reasons, our analysis should not be interpreted as evidence that inhaled corticosteroids are ineffective in COPD. However, it does demonstrate that the previous study cannot be taken as evidence that these drugs are effective.
With COPD being one of the major causes of death in the United States, the clinical implications of these studies are large. Although observational studies can be a valuable addition to randomized controlled trials to demonstrate treatment effectiveness or benefit, they must be properly conducted to minimize bias. Our study indicates that the uncertainty about the effectiveness of inhaled corticosteroids in COPD remains (3, 4).
Acknowledgment: The author would like to thank Mary Rose Stang for her assistance in compiling/obtaining the data and Pierre Ernst for his helpful comments.
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Division of Clinical Epidemiology, Royal Victoria Hospital, McGill University Health Centre; and the Departments of Epidemiology and Biostatistics and Medicine, McGill University, Montreal, Quebec, Canada
(Received in original form October 28, 2002; accepted in final form March 24, 2003)
Supported by grants from the Canadian Institutes of Health Research (CIHR) and Fonds de la recherche en sante du Quebec. The acquisition of the database was funded by grants from AstraZeneca, Boehringer-lngelheim, and GlaxoSmithKline. The author is the recipient of a Distinguished Investigator award from the CIHR.
Correspondence and requests for reprints should be addressed to Dr. Samy Suissa, Ph.D., Division of Clinical Epidemiology, Royal Victoria Hospital, 687 Pine Avenue West, Ross 4.29, Montreal, PQ, H3A 1A1 Canada. E-mail: samy.suissa@clinepi. mcgill.ca
This paper is dedicated to the memory of Alvan Feinstein, an eminent teacher and leader in the development of clinical epidemiology.
Disclaimer: this study is based on de-identified data provided by the Saskatchewan Department of Health. The interpretation and conclusions contained herein do not necessarily represent those of the government of Saskatchewan or the Saskatchewan Department of Health.
Copyright American Thoracic Society Jul 1, 2003
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