An Eternal Dilemma: Exposing the Impact of Immortal Time Bias on Antifibrotic Effectiveness

Nearly a decade ago, nintedanib and pirfenidone became the first medications approved by the U.S. Food and Drug Administration for the treatment of idiopathic pulmonary fibrosis based on a pair of randomized controlled trials (RCTs) demonstrating the drugs slowed the decline in lung function compared with placebo (1, 2). To date, no single RCT has been able to establish a mortality benefit for either drug, which is not surprising for a rare, deadly disease like IPF, in which powering a trial to show a reduction in mortality is incredibly difficult (3). Although there is a lack of clinical trial evidence supporting a mortality benefit for the antifibrotics, observational studies (as well as pooled clinical trial analyses) have repeatedly suggested one may exist (4–10).

Despite these hopeful observations, concerns have been raised that every prior observational study that found the use of antifibrotics improved survival falls victim to “immortal time bias” (11). This bias can occur in cohort studies when the treatment group gains an advantage over the control group because treated patients are considered “immortal” during the period between cohort entry and the time of prescription, as they must have survived that interval to be included in the analysis.

In this issue of AnnalsATS, Xu and colleagues (pp. 1407–1415) set out to address this bias by evaluating the effects of the antifibrotics on mortality in IPF while adjusting for immortal time (12). It is a well-written manuscript, and the authors deserve praise for their meticulous and rigorous methodology. Like many prior observational cohorts, they conducted a retrospective review of patients with IPF using a large administrative database. Their cohort was identified using classification codes and prescriptions for antifibrotics, and mortality was assessed using a combination of different sources. To mitigate the immortal time bias, antifibrotic therapy was labeled as a time-dependent variable. There were several subgroup analyses, multivariate adjustments, and even a simulation study, which bolsters their methodology. Importantly, the authors’ inclusion of said simulation study and their clear description of their statistical analyses (including in a detailed online supplement that readers are encouraged to review) provides a highly adaptable framework for investigators who wish to mitigate bias in similar future cohort studies.

The results of this well-designed analysis are intriguing and, on the surface, conflict with prior cohort evaluations of the antifibrotics that did not account for immortal time bias. Specifically, the authors observed no significant improvement in their primary outcome of mortality with antifibrotic use. To demonstrate the effect of their adjustments, they showed that if immortal time bias was ignored (both excluded and misclassified), a significant difference in mortality was observed. Clinically important subgroup and sensitivity analyses were also performed in patients who initiated therapy within 2 months (the group most likely to benefit from treatment) and in those older than 65 years (the group most likely to be diagnosed with IPF). In the early-start cohort, there was a nonsignificant trend toward a mortality benefit compared with those who initiated treatment after 2 months. Furthermore, when the early-start group was restricted to only patients older than 65 years, a significant mortality benefit of treatment was observed. Summarized, this research conveys that there is likely an improvement in mortality in older patients with IPF who start antifibrotics soon after diagnosis, although younger patients and those who start the antifibrotics several months after diagnosis do not derive such benefit.

Although the methods used in this paper are innovative, this is not the first analysis to address immortal time bias when evaluating mortality related to antifibrotic use in IPF. A team from the Mayo Clinic (which included one of the authors of this editorial) recently published a similar investigation of Medicare beneficiaries and observed a significant reduction in mortality with antifibrotic use while using a time-varying Cox proportional hazards model to adjust for immortal time bias (13). There are several key differences between the methodologies of these studies, such as their inclusion and exclusion criteria (the Mayo study only included those older than 65 yr, and their index date definition only included first diagnosis of IPF rather than first diagnosis or date of first fill in this study), censoring decisions (the Mayo study censored for a gap of ≥45 d without a prescription fill), and follow-up period (the prior study did not limit follow-up to 2 yr).

Of those variances, it is most important to examine the censoring decisions between these two studies more closely, as they likely contributed to differences in their primary outcome. Xu and colleagues raise a valid concern regarding the censoring of patients who stopped therapy in the Mayo study, which could have introduced selection bias. This is a thought-provoking point, one that should encourage a reconsideration of how best to define treatment exposure in cohort evaluations. In observational studies, especially those reviewing large administrative databases, exposure misclassification is a common problem that can bias results, depending on how stringently treatment criteria are defined. For example, Krumme and colleagues performed a study involving a cohort of patients on antiplatelet therapy, in which increasing restrictions on the definition of treatment continuation were applied (14). In the more liberally defined exposure cohorts, more biases were introduced, with widely variable results, whereas in the most strictly defined cohort, the findings closely approximated prior RCTs. In the case of the antifibrotics, should a patient who only receives a single prescription for an antifibrotic (i.e., <30 d of medication) really be classified as exposed to therapy? If not, what is the appropriate degree of compliance to most accurately evaluate their effectiveness in real-world clinical practice? This is particularly challenging, considering the wide range of adherence to antifibrotics that has been reported in real-world settings (15). These complexities highlight the difficulty of conducting cohort studies with rigorous methodology, while accurately representing therapeutic effectiveness in real-world clinical practice. Perhaps most importantly, it also highlights the urgent need for more effective treatment options for patients with IPF, as relatively minor methodologic concerns would likely have no influence on outcomes for a highly efficacious drug.

Despite these methodologic decisions and the clear differences in primary outcome results between the two studies, the findings may not be so incongruent, particularly when considering their clinical applicability. In their sensitivity analysis of patients aged ≥65 years, Xu and colleagues observed a significant reduction in mortality for patients who initiated antifibrotics within 2 months of diagnosis. The results of this sensitivity analysis not only align closely with the previous Mayo study (and other prior publications) but also hold the most clinical relevance.

In summary, the study from Xu and colleagues represents a significant addition to the IPF literature, offering insights that are both methodologically and clinically relevant. The research underscores the need for meticulous statistical adjustments in cohort evaluations and emphasizes the importance of timely initiation of antifibrotic therapies in older patients with IPF, pending future treatment advances.