The problem is rooted in a fundamental asymmetry in the literature. For prospective clinical trials, regulatory bodies such as the FDA provide detailed instructions on how endpoints should be defined and collected. Retrospective studies, which reconstruct patient outcomes from medical charts, institutional databases, and cancer registries, enjoy no such framework. These studies are indispensable, filling gaps where trials are infeasible because of cost, rare diseases, or the need for decades of follow-up, but investigators must make consequential judgments about index dates, event definitions, and censoring without formal support. Because those judgments are rarely described in published papers, readers cannot easily evaluate study quality, and other researchers cannot reliably replicate the findings in new datasets.

At the heart of every time-to-event analysis are three dates: the index date, which marks the start of follow-up; the event date, when the outcome of interest occurs; and the follow-up end date, at which a patient who has not experienced the event is censored. The elapsed time between the index date and whichever comes later is the patient’s follow-up time. Patients who remain event-free when observation stops, or who are lost to follow-up, are right-censored, and standard methods such as the Kaplan–Meier estimator and Cox proportional hazards regression are designed to incorporate these incomplete observations rather than discard them. Errors in any of the three dates translate directly into biased survival estimates. The index date, the authors stress, must be a point at which all patients are genuinely at risk and verifiably event-free, such as the date of diagnosis, surgery, or end of treatment, and it must be applied uniformly to everyone, even though different endpoints within the same study may require different index dates.

Getting the index date wrong invites one of the most insidious errors in observational research: immortal time bias. This occurs when a group classification, such as treatment response, can only be ascertained after follow-up has nominally begun, so that the event-free period required to reach that classification is wrongly credited to the group being studied. Remedies exist, including landmark analyses that restart follow-up at a fixed post-index time point and include only patients still event-free, as well as time-dependent modeling approaches, but all of them require that researchers record exactly when post-baseline characteristics were ascertained during data extraction. The authors illustrate the endpoint-specific nature of these choices with a retinoblastoma study in which progression-free survival was measured from the date of first visit, while recurrence-free and treatment-free survival both started at the end of chemotherapy.

The follow-up end date poses its own traps, particularly when multiple endpoints are being analyzed simultaneously. In a breast cancer study examining metformin use, recurrence-free survival ended at the last date a patient was known to be recurrence-free, while overall survival ended at the last date known to be alive. A common and easily overlooked mistake is to use last known alive as the censoring date for recurrence-free survival as well. Unless a scan confirmed the patient was disease-free on that date, the assignment artificially extends event-free time and produces overly optimistic survival estimates, a subtle form of bias that is difficult to detect after the fact. The authors also urge researchers to record the reason follow-up ended, whether an administrative cutoff, death, or loss to follow-up, because the key assumption underlying standard survival methods is that censoring is independent of event risk, and patients lost because they became too ill to attend clinic violate that assumption.

Imaging-detected events introduce another layer of complexity. When progression is found on a scan, the true event date lies somewhere between the last negative scan and the first positive one, a situation known as interval censoring. Standard methods treat the detection date as the event date, a reasonable approximation when scan intervals are short and consistent, but one that can introduce meaningful bias when intervals are long or vary systematically between treatment groups. The practical recommendation is to collect both the interval start and end dates during extraction, preserving the option to apply specialized interval-censored methods later. Partial dates present a similar challenge: rather than silently entering a full date when only the month or year is known, researchers should record the actual level of granularity, pre-specify how ambiguity will be resolved, and test alternative assignments in sensitivity analyses.

Deciding what counts as an event in the first place is equally consequential. Death from any cause makes overall survival straightforward, but endpoints involving recurrence or progression demand explicit answers to thorny questions: is a clinical assessment sufficient, or is radiologic confirmation required, and how should a patient who dies with signs of recurrence but without formal assessment be classified? The authors point to the STEEP criteria for breast cancer, first published in 2007 and updated in 2021, as the model for consensus-based event definitions, and urge investigators in other disease settings to document their definitions with comparable rigor. Competing events add further nuance. In a study of cancer-specific mortality, death from cardiovascular disease precludes death from cancer, and standard Kaplan–Meier analysis censors such deaths as uninformative, which overestimates cancer-specific mortality. When competing events are non-negligible, methods such as the cumulative incidence function and Fine-Gray subdistribution hazard regression are alternatives, but they can only be used if the type and date of every competing event were captured during abstraction.

Once the data are collected, the real detective work begins. The authors recommend that clinicians and statisticians jointly scrutinize Kaplan–Meier plots, always including three elements often omitted in published papers: the number-at-risk table, censoring tick marks, and pointwise confidence bands. Survival estimates become unstable when few patients remain under observation, and a practical rule of thumb is to truncate the plot where fewer than five patients remain at risk in any group. Clusters of censoring tick marks can reveal administrative features such as data lock dates, while large, regular drops in the curve may signal that events are being detected at scheduled assessment visits rather than continuously. Crossing survival curves suggest that a single summary hazard ratio may be misleading, because the direction of the association reverses over time, and early plateaus may indicate a mismatch between the index date and the earliest time events can realistically occur.

Sensitivity analyses complete the framework, testing how dependent results are on the specific assumptions made during extraction. These include alternate index and censoring dates, more and less inclusive event definitions, competing risks approaches, and scenarios for missing cause-of-death information in which unknown deaths are variously attributed to the cancer and to other causes. For such analyses to be possible, the underlying components, such as recurrence and death dates recorded separately, must be captured from the start rather than collapsed into a single event flag. Updating outcomes over time, a routine practice in oncology, requires similar care: when both progression-free and overall survival are tracked, every patient except those known to have died without prior progression needs review, since previously progressed patients may generate new deaths, and formerly censored patients may have new events or later censoring dates.

The guidance comes with important limitations, which the authors acknowledge directly. It addresses right-censored, single-event endpoints and does not cover recurrent events, left truncation, or multistate data, and it concerns what information to collect rather than which analytic method to apply, a choice that should always be made with a statistician. Reporting guidelines such as STROBE specify what should be reported about observational studies but do not address the abstraction decisions that shape statistical inference. By distilling decades of methodological expertise into a practical checklist, illustrated with a publicly available lung cancer dataset and a worked example tracing endpoint creation from raw records to analysis-ready variables, the authors aim to build time-to-event analyses on foundations of rigorously collected data. The payoff, they argue, is research that is more reproducible, more interpretable, and more likely to contribute meaningfully to the evidence base that guides patient care.

Subject of Research: Methods for collecting reproducible time-to-event endpoints in retrospective observational oncology studies

Article Title: Practical guidance for collecting reproducible time-to-event endpoints in retrospective observational oncology studies

Article References: Practical guidance for collecting reproducible time-to-event endpoints in retrospective observational oncology studies. (n.d.). https://doi.org/10.3389/fepid.2026.1958489

Image Credits: AI Generated

DOI: 10.3389/fepid.2026.1958489

Keywords: survival analysis, time-to-event endpoints, retrospective studies, oncology, censoring, Kaplan-Meier, Cox regression, immortal time bias, competing risks, progression-free survival, data collection, reproducibility