Competing Risks: State the Probability Question Before the Model

When a competing event such as death can occur before the efficacy event of interest (objective disease progression, leukemia relapse, or orthopedic joint revision), the clinical development team must first state which probability question the primary endpoint claims. The cumulative incidence function (CIF), computed nonparametrically via the Aalen-Johansen estimator, answers the absolute-risk question: what is the actual probability that a patient experiences the event of interest by time t in the real presence of competing events? The cause-specific hazard (CSH), modeled using standard Cox regression, answers the rate question: at what instantaneous rate does the event occur among participants who remain alive and free of all other events? Censoring competing deaths and calculating one minus Kaplan-Meier answers neither question: it estimates a hypothetical world where death cannot occur and systematically overstates the absolute failure probability (Gooley et al., 1999).

Under the ICH E9(R1) estimands framework, death is an intercurrent event that affects the existence of subsequent outcome measurements: variables cannot be measured after death, yet the addendum says these data should not generally be regarded as missing. Whether death is folded into a composite endpoint (in effect the composite-variable strategy, which FDA's oncology endpoint guidance reflects when it prefers progression-free survival [PFS] over time-to-progression [TTP]) or handled as a competing event depends on the trial's target estimand. Regulators already ask for the event breakdown: the European Medicines Agency (EMA) PFS appendix states that competing-risks analyses of the PFS components should be available at the time of analysis. The primary-analysis choice is genuinely contested. An NHLBI biostatistics group (Troendle et al., 2018) concludes, with simulation support, that the primary efficacy analysis of a two-arm randomized trial should generally use the cause-specific hazard, because a treatment effect on the competing event alone can distort a cumulative incidence comparison; a methods paper on reporting recommends presenting all cause-specific hazards and all cumulative incidence functions (Latouche et al., 2013). All quantities, risk sets, and model specifications must be locked in the protocol and statistical analysis plan before database unblinding; switching quantities post-unblinding represents endpoint rescue rather than principled inference.

In classical time-to-event trial design, right-censoring occurs when an individual's event time is unobserved due to study completion, administrative database lock, or loss to follow-up. In those situations, the participant remains at risk for the event after the censoring date, and standard survival models assume that censoring is non-informative—that censored individuals share the same failure probability as those continuing under observation. Detailed conventions for these mechanisms are set out in the guide to writing censoring rules.

A competing risk changes this foundational assumption. A competing risk is an observed, mutually exclusive first event that either permanently precludes the occurrence of the primary event of interest or alters its probability of occurrence fundamentally. When an elderly patient dies of cardiovascular failure in an oncology study before radiological disease progression can be documented, tumor progression for that individual is not merely postponed or unrecorded; it is rendered biologically impossible. Similar competing dynamics govern multiple therapeutic areas:

• Oncology: Objective disease progression versus death from comorbid conditions or surgical complications before documented progression.

• Hematology and Cellular Therapy: Malignancy relapse versus non-relapse mortality, such as severe graft-versus-host disease or fatal infection following hematopoietic stem-cell transplantation.

• Orthopedics: Aseptic implant loosening requiring surgical revision versus all-cause mortality in an octogenarian arthroplasty cohort.

• Cardiovascular Disease: Ischemic stroke or myocardial infarction versus non-cardiovascular death.

ICH E9(R1) terms these occurrences intercurrent events—events occurring after treatment initiation that affect either the interpretation or the existence of the measurements associated with the clinical question of interest. Section A.3.1 of the guideline names terminal events such as death among the intercurrent events that affect the existence of measurements, and the addendum states that for terminal events such as death the variable cannot be measured afterward, "but neither should these data generally be regarded as missing." It adds that the treatment policy strategy generally cannot be implemented for terminal events, and it calls death perhaps the most salient example of the need for the composite strategy. However, the phrase 'competing risk' does not appear anywhere in ICH E9(R1). The guideline provides the strategy taxonomy (treatment policy, hypothetical, composite variable, while on treatment, and principal stratum), while the mathematics of cumulative incidence and subdistribution hazard models comes from the statistical literature. Protocol authors must explicitly connect the E9(R1) strategy to the corresponding probability estimator.

When protocol authors and biostatisticians specify an endpoint subject to competing events, they must explicitly select which probability question the trial intends to answer. Two distinct mathematical quantities exist, and they diverge as competing event rates rise:

1. The Absolute Risk Question (Cumulative Incidence Function): What is the real-world probability that a patient experiences event type 1 by time t, accounting for the fact that other patients experience event type 2 first? The cumulative incidence function, denoted F₁(t) = P(T ≤ t, Event = 1), represents the absolute failure proportion in the real study population. It is nonparametrically estimated by the Aalen-Johansen estimator (Putter et al., 2007) and modeled multivariately using Fine and Gray's (1999) proportional subdistribution hazards regression.

2. The Event Rate Question (Cause-Specific Hazard): Among patients who remain alive and free of all events at time t, what is the instantaneous rate of experiencing event type 1? Denoted λ₁(t) = lim(Δt→0) P(t ≤ T < t+Δt, Event=1 | T ≥ t) / Δt, this rate answers the etiologic question of biologic disease activity. It is estimated by fitting a standard Cox proportional hazards model where occurrences of event type 2 are treated as right-censored at their failure date.

The fundamental biostatistical disconnect is that the cause-specific hazard has no direct, one-to-one interpretation in terms of absolute cumulative probability for that event alone. As shown in survival calculus, the cumulative incidence of cause 1 depends on both the cause-specific hazard for cause 1 and the overall survival probability, which in turn reflects the cause-specific hazard for cause 2:

F₁(t) = ∫₀ᵗ S(u⁻) · λ₁(u) du, where S(u) = exp( - ∫₀ᵘ [ λ₁(v) + λ₂(v) ] dv )

Because overall event-free survival S(u) is depleted whenever a competing event occurs, a treatment that alters the hazard of cause 2 will shift the cumulative incidence of cause 1 even if it has no biological activity on cause 1. Noting that the cause-specific hazard has no direct interpretation in terms of the probability of a particular failure type, Fine and Gray (1999) proposed a proportional hazards model for the subdistribution hazard, defined as:

γ₁(t) = lim(Δt→0) P(t ≤ T < t+Δt, Event=1 | T ≥ t or [T < t and Event ≠ 1]) / Δt

Under the Fine-Gray formulation, individuals who experience the competing event remain in the risk set after that event. This construction links regression coefficients directly to the cumulative incidence function, but it creates an artificial risk set: an individual who died at month 3 can still sit in the denominator at month 24. The subdistribution hazard ratio is therefore not a rate among living patients, and it is easily misread by clinical investigators who interpret every hazard ratio that way.

A recurring error in trial protocols and draft statistical analysis plans is the unreflective application of the Kaplan-Meier estimator to endpoints with competing events. Analysts treat competing deaths as ordinary right-censoring and compute the complement of the Kaplan-Meier estimate, presenting 1 - KM as the 'cumulative probability of disease progression.'

Gooley et al. (1999) noted that it is not uncommon to see the complement of the Kaplan-Meier estimate interpreted as the probability of failure in this setting, and explained why the cumulative incidence estimate is the appropriate tool instead. Once competing events occur, 1 - KM is never smaller than the cumulative incidence and generally overstates it. The Kaplan-Meier estimator assumes that individuals censored at time t would go on to fail at the same rate as those who remain under observation. For a patient who has died, that is impossible. By treating deceased patients as if they could still progress, 1 - KM estimates failure in a hypothetical cohort in which the competing death cannot occur.

Censoring a competing death is not wrong in itself: it is how a Cox model estimates the cause-specific hazard, a real-world rate among participants still free of both events. The problem starts when the censored analysis is read as a probability of progression. From an estimand standpoint under ICH E9(R1), that reading implements a hypothetical strategy: a scenario is envisaged in which the intercurrent event would not occur, and treating deaths as non-informative censoring for that purpose rests on an untestable independence assumption. The regulator record points the same way. FDA's oncology endpoint guidance notes that in TTP analyses death events are censored, representing informative censoring. EMA's PFS appendix states that there is no satisfactory way to correct for informative censoring, which should be minimised by adequate design and conduct, and that withdrawals from study therapy before adjudicated progression are likely to be informative, so censoring them should always be questioned. If a hypothetical estimand is chosen, its clinical plausibility and assumptions must be defended during study design, not retroactively after an imbalance in deaths emerges.

The choice between composite endpoints, cumulative incidence functions, and cause-specific hazard models is dictated by the trial's core estimand. Protocol authors drafting endpoint definitions under ICH M11 protocol specifications must align the endpoint definition, the intercurrent event strategy, and the statistical estimator before authoring the statistical analysis plan.

E9(R1) does not assign the cumulative incidence function or the cause-specific hazard to a named strategy, which is why the last row is labelled a competing-risks estimand rather than an E9(R1) strategy. A team that chooses either quantity should describe in the estimand how death without progression is handled (as an observed, distinct first event rather than missing data or ordinary loss to follow-up) and justify the choice in the protocol instead of attributing it to the guideline. The hypothetical row and the competing-risks row can use the same Cox model with deaths censored; what differs is the claim. One reports a rate among event-free participants, the other asserts what would have happened if nobody had died.

This alignment explains FDA's position on PFS and TTP. Its 2018 oncology endpoint guidance defines TTP as time from randomization until objective tumor progression, excluding deaths, and states that compared with TTP, PFS is the preferred regulatory endpoint because PFS includes deaths and thus can be a better correlate of overall survival. In TTP analysis, the guidance notes, death events are censored, either at the time of death or at an earlier visit, representing informative censoring (a nonrandom pattern of loss from the study). PFS folds death into a composite variable, so deaths before documented progression count as endpoint events.

Folding death into a composite endpoint does not remove the need for competing-risks thinking. Because PFS is a composite of different events (for example new lesions, progression of existing lesions, and death), EMA's PFS appendix recommends reporting separate analyses for the individual event types using descriptive summary tables and, where appropriate, competing-risks approaches, and states that competing-risks analyses of the components should be available at the time of analysis. Those component analyses show whether an apparent PFS benefit is driven by fewer progressions or by a shift in deaths without progression.

To show how cumulative incidence and naive Kaplan-Meier calculations diverge on the same data, consider the following worked example. Table 2 presents a synthetic cohort of 12 participants in a two-arm trial, followed for up to 24 months for objective progression (event of interest) and death without progression (competing event). One participant (P-004) is lost to follow-up at month 8, so from that point the estimates are no longer simple fractions of 12; every value in Table 3 is computed with the stated estimator.

When these 12 participant histories are summarized at 12 and 24 months, the numerical divergence between naive Kaplan-Meier censoring and Aalen-Johansen cumulative incidence is immediately evident:

In this cohort, the naive 1 - KM calculation reports a 24-month progression probability of 71.4%, whereas the Aalen-Johansen cumulative incidence is 55.0%: an absolute overstatement of 16.4 percentage points, about 30% in relative terms. At 12 months the gap is 12.1 points (57.1% versus 45.0%). A team presenting 1 - KM as the 'probability of progression' to an adjudication committee or governance body would overstate the absolute progression risk.

The same rows also give the two hazard readings in their simplest constant-rate form (events divided by person-time; an illustration, not a Cox fit). The 12 participants contribute 114 person-months before their first event or censoring, so the cause-specific progression rate is 6 / 114 = 5.3 per 100 person-months and the cause-specific death rate is 3 / 114 = 2.6 per 100 person-months. A subdistribution reading keeps the three participants who died in the risk set. If they are carried to the 24-month end of follow-up, the denominator grows to 173 person-months and the progression rate falls to 6 / 173 = 3.5 per 100 person-months. The six progressions are the same; only the risk set changes. The subdistribution rate is lower because people who can no longer progress are still counted as at risk, which is why cause-specific and subdistribution hazard ratios estimate different quantities and cannot be swapped in a protocol.

Having established that 1 - KM overstates absolute risk, it is tempting to conclude: 'Always use the cumulative incidence function and Gray's test for the primary analysis.' For confirmatory randomized trials, the methods literature does not support that shortcut.

Biostatisticians at the National Heart, Lung, and Blood Institute (Troendle, Leifer, and Kunz, 2018) examine two-arm randomized trials with simulation studies and do not recommend using the primary event's cumulative incidence function as the primary efficacy analysis. Their reasoning exposes a vulnerability in CIF-based treatment comparisons (the oncology framing below is illustrative; their worked example is cardiovascular):

• Cross-Hazard Contamination: Because the cumulative incidence of the primary event depends on the hazard of the competing event, a treatment effect that operates solely on the competing event can generate a false-positive finding on the primary event's CIF.

• Apparent Harm from Effective Therapies: If an investigational drug dramatically lowers early mortality without affecting tumor progression rates, more patients survive to develop tumors. The experimental arm will exhibit a higher cumulative incidence of progression than the control arm, creating the false appearance of oncologic harm.

• Apparent Efficacy from Toxic Therapies: Conversely, a toxic therapy that accelerates early non-disease deaths will remove patients from the tumor risk set, artificially suppressing the cumulative incidence of progression. Gray's test could register statistical significance even though the therapy possesses zero antitumor efficacy.

Troendle et al. (2018) conclude that for randomized two-arm trials, the primary efficacy analysis should generally evaluate the cause-specific hazard using a Cox model that treats the competing event as independent censoring, which they report is reasonably robust even with a shared, moderately prognostic, unobserved frailty. When a strongly prognostic shared frailty is a concern, they suggest considering a composite endpoint or a bivariate test instead.

Troendle et al. also show that a composite endpoint is not a free remedy, because folding the competing event in can dilute the treatment effect. In the Women's Health Initiative estrogen-plus-progestin trial, the primary coronary heart disease outcome (nonfatal myocardial infarction or coronary death) had a hazard ratio of 1.28 (P = 0.04), indicating significant harm. Because the therapy had no effect on noncoronary death, adding noncoronary death to form a composite diluted the hazard ratio to a nonsignificant 1.10.

How should trial teams resolve this? Latouche et al. (2013), in the Journal of Clinical Epidemiology, recommend that a competing-risks analysis report results on all cause-specific hazards and all cumulative incidence functions, because a covariate's effect on a cause-specific hazard can differ from its effect on the corresponding cumulative incidence. A practical reconciliation is to pre-specify one quantity as primary for testing (in a randomized superiority trial, most often the cause-specific hazard, following Troendle et al.) and to report the full set of cause-specific hazards and cumulative incidence curves, so that both the rate question and the absolute-risk question are answered. Neither metric alone gives the complete picture.

Selecting between the cause-specific hazard and the subdistribution hazard is not merely an analytical preference; it dictates sample size calculations, event counts, and protocol power. Powering a trial on cumulative incidence differences (Fine-Gray / Gray's test) versus hazard rate differences (Cox / log-rank test) requires distinct mathematical assumptions.

Tai, Wee, and Machin (2011, Trials) illustrate these dynamics with the SQNP01 randomized trial in advanced nasopharyngeal cancer (221 patients), in which distant metastasis was the event of interest and loco-regional recurrence the competing event:

• Effect Size Concordance: Treatment had no effect on the competing event, and the two analyses agreed: unadjusted csHR 0.43 (95% CI 0.25-0.72) versus subHR 0.43 (95% CI 0.25-0.76). The log-rank test on the cause-specific hazards (p = 0.002) and Gray's test on the cumulative incidences (p = 0.003) led to the same conclusion.

• Discrepant Sample Size Requirements: Both sample-size methods build on the Schoenfeld formula and need two inputs: the planned hazard ratio and the anticipated proportion of participants failing from the event of interest. Even with similar effect sizes, the subdistribution hazard analysis required many more subjects than the cause-specific analysis to detect the same magnitude of effect.

• When the Subdistribution Model Earns Its Place: The cause-specific sample-size method they describe assumes constant cause-specific hazards and a treatment that affects the event of interest but not the competing event. Tai et al. conclude that if an intervention moves the main and competing events in opposing directions, a subdistribution hazard analysis may be warranted.

Protocol authors must state three explicit design elements in the sample size section: (1) whether sample size is sized for the cause-specific hazard ratio or subdistribution hazard ratio, (2) the assumed background rate and hazard shape of competing events, and (3) the primary test statistic that governs trial success.

To withstand regulatory inspection and avoid suspicion of post-hoc outcome manipulation, endpoint specifications must be finalized and frozen in the protocol and statistical analysis plan before database unblinding. Shifting between cause-specific hazard models and cumulative incidence functions after observing trial results is a form of data-dredging or post-hoc endpoint rescue.

Trial teams should incorporate the following exact language components into their study documentation:

1. Unambiguous Event Definition: 'The primary endpoint is the time from randomization to the first documented objective radiological progression per RECIST 1.1. Death from any cause without documented prior progression is a competing event: its date and adjudicated cause will be recorded, and it will be neither counted as progression nor treated as loss to follow-up.' Adjudication of deaths and progression dates should follow the endpoint adjudication charter.

2. Explicit Specification of Primary Test and Estimator: 'The primary efficacy analysis will estimate the cause-specific hazard ratio of progression between Treatment Arm A and Treatment Arm B using a Cox proportional hazards model stratified by the randomization factors. For estimation of the cause-specific hazard, deaths without documented progression will be right-censored at the date of death. The hypothesis will be tested with a two-sided stratified log-rank test at alpha = 0.05.'

3. Mandated Cumulative Incidence Reporting: 'Cumulative incidence functions for objective progression and for death without progression will be estimated by treatment arm using the Aalen-Johansen method, with estimates and 95% confidence intervals at 6, 12, 18, and 24 months. Treatment differences in cumulative incidence will be evaluated with Gray's test as a pre-specified supplementary analysis.' For PFS-type composite endpoints, the same section should list the competing-risks analyses of the components that EMA's PFS appendix expects to be available at the time of analysis.

4. Prohibition of Post-Hoc Estimator Switching: 'Under no circumstances will a non-significant cause-specific hazard analysis be substituted with a subdistribution hazard analysis (or vice versa) after database unblinding. Any post-unblinding exploratory modeling must be explicitly designated as post-hoc supportive analysis in the Clinical Study Report.'

Competing risks cannot be resolved by software defaults or retrospective re-analysis. Frame the competing event through an ICH E9(R1) strategy, state whether the primary endpoint targets absolute risk (CIF) or the event rate among event-free participants (CSH), and pre-specify the estimator, test, and reporting set in the protocol and SAP before unblinding. This article is methodological guidance: it does not replace trial-specific statistical review or regulator consultation, and no analysis choice described here guarantees regulatory acceptance.

• ICH Harmonised Guideline E9(R1): Addendum on Estimands and Sensitivity Analysis in Clinical Trials to the Guideline on Statistical Principles for Clinical Trials (Step 4 final, 2019)

• EMA CHMP Appendix 1 to Guideline on Evaluation of Anticancer Medicinal Products: Methodological Considerations for PFS and DFS in Confirmatory Trials (EMA/CHMP/27994/2008/Rev.1)

• FDA Guidance for Industry: Clinical Trial Endpoints for the Approval of Cancer Drugs and Biologics (December 2018)

• Gooley TA, Leisenring W, Crowley J, Storer BE. Estimation of failure probabilities in the presence of competing risks: new representations of old estimators. Statistics in Medicine 1999;18(6):695-706

• Fine JP, Gray RJ. A Proportional Hazards Model for the Subdistribution of a Competing Risk. Journal of the American Statistical Association 1999;94(446):496-509

• Latouche A, Allignol A, Beyersmann J, Labopin M, Fine JP. A competing risks analysis should report results on all cause-specific hazards and cumulative incidence functions. Journal of Clinical Epidemiology 2013;66(6):648-653

• Tai BC, Wee J, Machin D. Analysis and design of randomised clinical trials involving competing risks endpoints. Trials 2011;12:127

• Troendle JF, Leifer ES, Kunz L. Dealing with competing risks in clinical trials: How to choose the primary efficacy analysis? Statistics in Medicine 2018 (doi:10.1002/sim.7800)

• Putter H, Fiocco M, Geskus RB. Tutorial in biostatistics: Competing risks and multi-state models. Statistics in Medicine 2007;26(11):2389-2430

• ICH Efficacy Guidelines status page (ICH E20 'Adaptive Designs for Clinical Trials')