Non-Proportional Hazards: What One Hazard Ratio Can Hide

When a confirmatory time-to-event endpoint exhibits non-proportional hazards (NPH)—whether because an immunotherapy takes months to separate the survival curves, a targeted effect wanes after treatment stops, or an experimental regimen causes early toxicity before producing a durable tail—the single hazard ratio (HR) from a standard Cox proportional hazards model stops estimating a constant relative event rate. Instead, that single number becomes a weighted average of time-varying ratios whose value shifts with the event accrual schedule, administrative data cut, and censoring distribution. As a 2024 systematic review of non-proportional hazards methods in Statistical Methods in Medical Research concludes, the standard Cox HR estimate under NPH is neither robust nor meaningful and lacks a clear clinical interpretation because its numerical value depends on the censoring distribution and the follow-up window observed.

For clinical development leaders and trial biostatisticians, that mathematical reality creates three operational obligations before database lock and unblinding: first, diagnose and name the time-varying pattern early using both Kaplan-Meier visual shape and pre-specified residual diagnostics rather than relying on a single summary statistic; second, treat the choice of effect summary as an estimand decision under ICH E9(R1), which requires the population-level summary to reflect the treatment effect rather than confounding from differences in duration of observation; and third, pre-specify companion summaries and sensitivity analyses in the Statistical Analysis Plan (SAP) rather than attempting a post-hoc endpoint rescue after seeing the unblinded curves.

A standard Cox proportional hazards model specifies the hazard in the experimental arm h_1(t) as a constant multiple of the control-arm hazard h_0(t): h_1(t) = h_0(t) * exp(beta). Under true proportional hazards, the time-specific hazard ratio HR(t) = h_1(t) / h_0(t) stays invariant at exp(beta) whether the trial is analyzed at 12 months, 24 months, or 48 months. When the biological effect changes over follow-up—so HR(t) is a function of time exp(beta(t))—maximizing the standard Cox partial likelihood no longer estimates a structural constant. Instead, the score equation solves for a single scalar hat(beta) that approximately weights each instantaneous log-hazard ratio by the information (observed events and relative risk-set sizes) present at each event time prior to administrative cutoff.

That weighting mechanism explains why two analyses of the exact same underlying treatment effect can produce contradictory single-number summaries. Because early follow-up typically contains the largest risk sets and the lowest cumulative censoring, early events carry heavy weight in the partial likelihood. If a therapy exhibits a four-to-six-month biological lag before slowing disease progression or mortality, an early data cut dominated by pre-separation events will produce an estimated Cox HR close to 1.0—or above 1.0 if early toxicity or rapid progression occurs in a vulnerable subset. If follow-up continues for another 18 months without heavy drop-out, late events accruing after curve separation pull the single Cox HR downward. As Bardo et al. (2024) synthesize across the methodological literature, under NPH the standard Cox HR estimate is neither robust nor meaningful, and because the weights depend on how many participants remain uncensored at each timepoint, the estimate depends directly on the censoring distribution.

Even before a formal test rejects proportionality, a single hazard ratio carries a structural interpretability trap identified by Miguel Hernán in The Hazards of Hazard Ratios (Epidemiology, 2010). Unlike a cumulative risk ratio or survival probability difference measured from randomization, a hazard at time t conditions on having survived event-free up to t. Whenever treatment affects early event rates in a population with unmeasured frailty—meaning some participants are biologically more susceptible to early events than others—the control and experimental risk sets are progressively depleted of high-risk individuals at different speeds. Consequently, late period-specific hazards compare non-exchangeable survivor subsets, and a single summary HR blends genuine biological dynamics with built-in selection over follow-up time. Readers who treat an HR of 0.75 as a 25% reduction in the probability of dying during the study conflate an instantaneous conditional rate ratio with a cumulative risk contrast.

In oncology, the clinical consequences of compressing a time-varying survival trajectory into a single HR were highlighted in the New England Journal of Medicine in 2018 through correspondence by Alexander, Schoenfeld, and Trippa titled "Hazards of Hazard Ratios — Deviations from Model Assumptions in Immunotherapy" (indexed under Proportional Hazards Models, Kaplan-Meier Estimate, Survival Analysis, and Immunotherapy). When survival curves separate late or cross, the problem is not merely a technical violation of a regression diagnostic; it is also an estimand question. How a trial team writes its time-to-event censoring rules and defines its ICH E9(R1) estimand and intercurrent-event strategies determines which events and observation windows enter the risk set—and therefore determines what a single Cox HR averages over.

Non-proportional hazards are not a single phenomenon. Methodological reviews, including Bardo et al. (2024) and the Cross-Pharma Non-Proportional Hazards Working Group guidance (Roychoudhury et al., 2023), classify deviations from proportional hazards into three recurring clinical trajectories, each with distinct consequences for the unweighted log-rank test and the single Cox HR:

1. Delayed treatment effect (late separation): The experimental and control Kaplan-Meier curves track closely for an initial period [0, t_0] (where HR(t) approx 1.0) before diverging in favor of the experimental regimen (HR(t) < 1.0 for t > t_0). This pattern is typical of cancer immunotherapy, where the treatment effect needs time to build before events are prevented. Pre-separation events contribute noise without treatment signal to the unweighted log-rank numerator, eroding statistical power and pulling the single Cox HR toward unity.

2. Diminishing (waned) treatment effect: The survival curves separate rapidly after randomization (HR(t) < 1.0 early), but the instantaneous hazard ratio drifts back toward 1.0—or above 1.0—during later follow-up. Diminishing effects arise when fixed-duration therapy ends, acquired drug resistance emerges, or control-arm participants switch to effective subsequent therapy after progression. Here, an early interim or primary cut captures the peak hazard reduction and overstates long-term durability.

3. Crossing hazards and crossing survival curves: The experimental arm experiences a higher early event rate than control (HR(t) > 1.0 for t < t_c) followed by a substantially lower late event rate (HR(t) < 1.0 for t > t_c); if the late benefit is large enough, the Kaplan-Meier curves themselves cross. Bardo et al. note that a delayed effect can produce crossing hazards when the comparator is an active treatment with an immediate response, as is often the case in immuno-oncology trials; any regimen with early toxicity or procedural risk followed by later benefit can produce the same shape. Under crossing curves, early negative log-rank differences and late positive differences partly cancel each other, and a single Cox HR hides both the early excess risk and the late survival plateau.

Recognizing which trajectory is present requires pairing visual plots with formal residual diagnostics. Visually, proportional hazards imply that the survival curves do not cross and that the complementary log-log survival curves, log(-log S(t)) plotted against log(t), maintain a constant vertical separation. Formally, the standard diagnostic used in the methods literature and the cross-pharma working-group guidance (Mukhopadhyay et al., 2022; Roychoudhury et al., 2023) is the Grambsch-Therneau test, which evaluates whether scaled Schoenfeld residuals from the fitted Cox model exhibit a non-zero slope over transformed time (alongside smoothed Schoenfeld residual curves that trace hat(beta)(t) continuously across follow-up).

Despite the simplicity of those checks, published clinical trials rarely report them. In an audit of published trial practice synthesized by Bardo et al. (2024) (citing Jachno et al.), Kaplan-Meier curves, Cox proportional hazards models, and unweighted log-rank tests dominated primary time-to-event reporting, yet only about 11% of reviewed trial publications reported either formal testing or visual inspection for non-proportional hazards. Furthermore, in progression-free survival (PFS) trials, teams should check that apparent delayed separation or step-like curve behavior is not an artifact of asymmetric visit windows or reader discordance by cross-checking their central imaging read charter and assessment schedules.

Neither FDA nor EMA has issued a standalone guideline dedicated to statistical testing under non-proportional hazards. Instead, final and draft regulatory expectations sit inside broader oncology, estimand, and adaptive-design documents. Because several high-profile documents remain in draft consultation as of October 15, 2026, clinical development and regulatory strategy teams must distinguish binding or finalized regulatory expectations from draft recommendations that are not yet for implementation.

In August 2025, FDA released its draft guidance Approaches to Assessment of Overall Survival in Oncology Clinical Trials (Docket FDA-2024-D-5850; 90 FR 40367), explicitly marked Draft — Not for implementation. Because it is a draft, it describes FDA's proposed approach rather than a requirement, but it is the most direct FDA text on proportional-hazards checks for overall survival. Four passages matter here:

• Pre-specified assumption checks in the SAP: FDA states that Statistical Analysis Plans should include pre-specified analyses to assess any assumptions for the statistical methods used, explicitly naming proportional hazards as an example, and warns that if non-proportional hazards are observed, early overall survival data may not represent the true overall survival effect.

• Design and SAP expectations when NPH is anticipated: When non-proportional hazards are anticipated at the design stage, FDA expects additional considerations for adequate overall survival assessment to be pre-specified: the trial should be designed for long-term data collection, sample size and power calculations should be based on justifiable assumptions, and the SAP should pre-specify sensitivity analyses and supplementary metrics such as landmark survival rates and restricted mean survival time (RMST).

• Retention of Cox HR and log-rank as the general primary framework: Crucially, FDA's draft guidance still generally recommends the hazard ratio obtained from a Cox proportional hazards model (with its 95% confidence interval) and the log-rank test as the primary overall survival analysis on an intent-to-treat (ITT) basis, accompanied by event-driven timing and Kaplan-Meier plots. Landmark survival and RMST are positioned as pre-specified supplementary and sensitivity analyses rather than automatic replacements for the primary test.

• No post-hoc endpoint rescue: FDA states that post-hoc analyses are considered exploratory and suitable for hypothesis generation, but not suitable for statistical testing with alpha allocation. The draft also notes that it is not possible to determine whether bias is introduced when statistical approaches are selected retrospectively, that summary measures carry high uncertainty when extensive crossover or non-proportional hazards were not accounted for at study design, and that subgroup results cannot be used to salvage a trial that was not successful based on evaluation of the overall ITT population.

In Europe, the finalized EMA CHMP Appendix 1 to the Guideline on the Evaluation of Anticancer Medicinal Products in Man (EMA/CHMP/27994/2008/Rev.1, adopted December 2012, effective July 2013) establishes parallel rules for progression-free survival (PFS) and disease-free survival (DFS) in confirmatory trials. EMA states that planned sensitivity analyses should address important assumptions in the methods used—explicitly listing proportional hazards alongside deviations, missing data, uninformative censoring, and unscheduled assessments. For effect quantification, EMA directs sponsors to plot survivor functions and estimate the hazard ratio, medians, other percentiles, and event-free percentages at particular timepoints; warns that over-reliance on differences in medians should be avoided because a single percentile is generally less informative than considering the survival curve as a whole; states that the choice of the summary measure should be justified and pre-specified; and notes that changes to the SAP made with knowledge of accruing data give rise to regulatory concern.

Similarly, when sponsors consider modifying a trial's target event count or follow-up duration in response to slower-than-expected event accrual or emerging delayed separation, document status matters. FDA's December 2019 Guidance for Industry on Adaptive Design Clinical Trials for Drugs and Biologics (Docket FDA-2018-D-3124) is final and defines an adaptive design as prospectively planned modifications to one or more aspects of the design based on accumulating data from subjects in the trial, including prospectively planned modifications to the total number of events, subject to Type I error control and data-access firewalls. By contrast, ICH E20 (Adaptive Designs for Clinical Trials) reached Step 2b on 25 June 2025 and was issued by FDA for public comment in September 2025 (Docket FDA-2025-D-3023); as verified on the ICH Efficacy Guidelines status page on October 15, 2026, ICH E20 remains a Step 3 draft guideline (not for implementation) and must not be cited as a finalized regulatory requirement.

When mechanism-of-action evidence, Phase 2 survival tails, or comparator kinetics suggest that hazards may separate late or cross, the highest-leverage fixes occur while the protocol and Statistical Analysis Plan endpoint definitions are still open and blinded. Methodological literature offers two distinct design philosophies—a conservative log-rank reinforcement approach and a pre-specified robust combination-test approach—and trial teams should weigh both explicitly.

In a pointed methodological commentary in the Journal of Clinical Oncology, National Cancer Institute biometricians Boris Freidlin and Edward L. Korn (Freidlin & Korn, 2019) argue that the unweighted log-rank test and standard Cox model remain appropriate primary analyses for definitive trials even when treatment effects are delayed—provided the trial's event target, follow-up duration, and interim monitoring rules are adjusted at design. Specifically, they propose that, when delayed effects or long-term cures are a concern, log-rank-based designs with a slightly inflated sample size (about 10%), additional follow-up, and modified interim futility analyses can provide robust power, and they caution against abandoning the log-rank test in favor of tests that can squeeze out more statistically significant results from observations that have no clinical significance.

Complementing that perspective, the Cross-Pharma Non-Proportional Hazards Working Group published a detailed design and analysis framework in Statistics in Biopharmaceutical Research (Roychoudhury et al., 2023). The authors explicitly describe their framework as a "straw man" proposal intended to spur methodological alignment rather than a regulator-endorsed mandate, and state clearly that when NPH is not expected, traditional log-rank testing and the Cox HR should remain the primary analysis. When biological or clinical evidence makes NPH plausible at design, however, their working-group guidance recommends four concrete protocol design rules:

• Minimum follow-up of approximately twice the control-arm median survival: Event-driven cutoffs triggered solely by fast enrollment and early control events can truncate observation before the late tail matures. Locking a minimum follow-up floor (such as minimum follow-up on all randomized participants—or calendar duration from last patient randomized—approximating twice the expected control median) ensures the late portion of the survival curve is observed with adequate numbers at risk.

• At least two pre-specified treatment-effect scenarios in the protocol power section: Rather than powering solely under a constant-HR assumption, the protocol and simulation report should document operating characteristics under at least two plausible scenarios—typically a proportional-hazards reference scenario and a piecewise delayed-effect or crossing-hazards scenario—supporting FDA's August 2025 draft OS guidance expectation that sample size and power calculations rest on justifiable assumptions.

• Interim futility timing delayed until at least 45%–50% of target events: If a therapy requires three to six months to separate the survival curves, an aggressive early futility look at 25%–30% information is dominated by pre-separation events and carries a high risk of falsely terminating an effective drug. Unless an independent Data Monitoring Committee identifies an emerging safety signal, Roychoudhury et al. (2023) recommend scheduling interim futility analyses no earlier than 45%–50% of total planned events.

• Prospective governance for any event-target adaptation: If the sponsor plans to adapt the total number of events or extend follow-up based on interim accumulating data, that rule should be written prospectively into the design with prespecified Type I error control and blinding firewalls under FDA's final December 2019 Adaptive Design guidance.

Because no single statistic captures both early risk and late survival benefit when hazards vary over time, Bardo et al. (2024) emphasize that there is no consensus on a single best method under non-proportional hazards. Selecting the primary test and its companion effect summaries is a design-stage trade-off among statistical sensitivity, directionality safety, and clinical interpretability.

Proponents of weighted and combination log-rank tests point to the Fleming-Harrington G^(rho, gamma) family, which weights each event time by [S(t-)]^rho * [1 - S(t-)]^gamma: G^(0,0) is the standard unweighted log-rank test, G^(0,1) emphasizes late separation, G^(1,0) emphasizes early separation, and G^(1,1) emphasizes mid-trial differences. The MaxCombo test takes the maximum standardized statistic across a pre-specified set of Fleming-Harrington weights, adjusting the p-value for multiplicity via the asymptotic multivariate normal covariance matrix (see our guide to multiple endpoints and Type I error control).

To quantify how often alternative tests change trial conclusions in practice, Mukhopadhyay et al. (JAMA Oncology, 2022) reconstructed survival data from published Kaplan-Meier curves across 63 randomized immuno-oncology trials comprising 35,902 patients and 150 treatment comparisons. Evaluated at a two-sided 0.05 significance level:

• The standard log-rank test and MaxCombo 2 (the authors' primary MaxCombo variant, covering proportional-hazards and delayed-effect scenarios) were concordant in 90% of comparisons (135 of 150).

• In all 15 discordant comparisons (10%), MaxCombo 2 achieved nominal statistical significance where the unweighted log-rank test did not, and 12 of those 15 discordant comparisons exhibited statistically significant proportional-hazards violations on Grambsch-Therneau testing.

• The difference in restricted mean survival time (dRMST) was concordant with the standard log-rank test in 91% of comparisons and was not more sensitive than the log-rank test for detecting treatment differences.

While Mukhopadhyay et al. conclude that pre-specified MaxCombo testing offers a pragmatic alternative under anticipated delayed separation, Freidlin & Korn (JCO, 2019) provide essential counter-evidence that every SAP author must weigh before replacing a primary log-rank test:

• Late-emphasis weights discount early harm: Because G^(0,1) assigns near-zero weight to early events and heavy weight to late events when few patients remain at risk, Freidlin and Korn show that it is possible for the experimental-arm survival curve to sit below the control-arm curve throughout follow-up while a late-emphasis test still rejects the null hypothesis in favor of the experimental arm.

• Bidirectional rejection on crossing curves (the KEYNOTE-042 pathology): Because a combination test takes the maximum across early-emphasis and late-emphasis weights, when survival curves cross, the same dataset can reject the null hypothesis both in favor of the experimental treatment (via late weights) and in favor of the control treatment (via early weights). Applied to reconstructed KEYNOTE-042 progression-free survival curves (pembrolizumab versus chemotherapy), Freidlin and Korn report that a maximum test rejected the null in favor of pembrolizumab and, on the same data, in favor of chemotherapy (one-sided P < .0001 each way), and that MaxCombo gave the same result. A p-value from a combination test does not by itself define a coherent direction of clinical benefit when early harm and late benefit coexist.

Regardless of whether the primary hypothesis test uses the unweighted log-rank statistic or a pre-specified MaxCombo test, the regulatory texts (FDA August 2025 draft OS guidance; EMA 2012 PFS/DFS Appendix 1) point the same way as the methods literature: FDA's draft asks for pre-specified supplementary summaries when non-proportional hazards are anticipated, EMA's appendix warns against over-reliance on medians instead of the whole survival curve, and the cross-pharma working group states that a single summary measure is not adequate when the treatment benefit is not constant over time. The SAP should pre-specify a companion estimation package drawn from three interpretable, time-anchored summaries:

• Milestone (landmark) survival difference at pre-specified clinical horizons t*: The difference in Kaplan-Meier survival probabilities S_1(t*) - S_0(t*) (for example, at 12, 24, and 36 months) directly answers the clinical question of what proportion of randomized patients remain alive and event-free at a fixed milestone. FDA's 2025 draft OS guidance names landmark survival rates as a supplementary analysis, and EMA's 2012 appendix lists the percentage of patients event-free at particular timepoints among the effect-size estimates to report. Its limitation is that each milestone evaluates only a single vertical slice of the survival curve and ignores how patients reached t*.

• Restricted mean survival time (RMST) difference up to truncation time tau: Defined as the area between the two Kaplan-Meier curves from randomization to tau, dRMST(tau) = integral_0^tau [S_1(t) - S_0(t)] dt, RMST measures the average event-free time gained or lost over a defined window without relying on proportional hazards. However, as Freidlin & Korn (2019) and Mukhopadhyay et al. (2022) report, dRMST was not more sensitive than the log-rank test in the immuno-oncology reanalysis, and its statistical significance depends on the chosen truncation horizon tau. Rather than picking tau after inspecting the curves, teams should lock the clinical and data-maturity criteria for tau in the SAP using our dedicated guide on justifying the RMST comparison horizon in clinical trials (and when non-terminal events face death as a competing event, align the probability question using our framework on competing risks in clinical trials).

• Piecewise hazard ratios across pre-specified clinical epochs: As Bardo et al. (2024) document, partitioning follow-up into pre-specified intervals (for example, Months 0–6 during induction versus Month 6+ during maintenance) makes early risk versus late benefit visible, though period-specific HRs beyond Month 6 still condition on surviving the first 6 months (Hernán, 2010) and must be interpreted alongside unconditioned survival curves.

To make the behavior of a single hazard ratio concrete—and to give biostatistics and clinical development teams an operational specification they can lift directly into an SAP—this section provides two original methodological assets: a synthetic crossing-and-delayed-effect survival trajectory demonstrating cut-point sensitivity, and a model-assumption interpretation checklist mapping diagnostic signals to pre-specified actions.

Synthetic Data Disclosure: The survival trajectories and summary metrics in the chart and table below are synthetic worked data generated deterministically from a known piecewise constant hazard model solely to illustrate how a single Cox HR averages over time-varying hazards and shifts across administrative data cuts. They do not represent an independently conducted clinical study, patient cohort, or regulatory submission.

In this synthetic two-arm example, the control arm has a constant monthly hazard h_0(t) = 0.048 (median survival about 14.4 months). The experimental arm follows a stylized three-epoch trajectory of the kind described for immunotherapy against an active comparator: an early excess-hazard phase (Months 0–6) (h_1 = 0.065, period HR(t) ≈ 1.35), a transition phase (Months 6–12) (h_1 = 0.036, period HR(t) = 0.75), and a durable late-benefit phase (Months 12–36) (h_1 = 0.023, period HR(t) ≈ 0.48). The single Cox HRs below are the large-sample values the Cox partial-likelihood estimator converges to under this model, not draws from a simulated sample. The main column assumes every participant is followed from randomization to the data cut with no other censoring; a second column repeats the calculation with uniform enrollment over 12 months, so each cut is a calendar date and recent enrollees are censored early.

Notice what happens in the cut-point table below when the same synthetic trial is summarized by a single standard Cox HR at four data cuts. With everyone followed to the cut, the single HR is 1.18 at an immature Month 9 cut (suggesting net harm); 1.00 at Month 15, just after the curves cross (suggesting no effect while concealing both the 7.3-percentage-point survival deficit at Month 6 and the emerging late benefit); and 0.79 by Month 36 (concealing the early period HR of 1.35). With 12-month staggered enrollment, the same hazards give 1.30, 1.16, 0.94, and 0.82 at the same calendar cuts. Only the censoring pattern changed, which is the dependence Bardo et al. (2024) describe. None of those single numbers describes the clinical trajectory on its own.

To operationalize the regulatory expectations of FDA's August 2025 draft OS guidance and EMA's 2012 PFS/DFS Appendix 1 along with the three-step analysis structure of Roychoudhury et al. (2023), the SAP should lock a deterministic diagnostic-to-reporting pathway before database lock. The workflow diagram and checklist table below are structured so biostatisticians can adapt them directly into an SAP assumption-verification section—while explicitly prohibiting post-hoc selection of favorable test statistics.

flowchart TD
    A["Step 1: Execute Pre-Specified Primary ITT Analysis<br/>(Standard Log-Rank + Cox HR, or Pre-Specified MaxCombo with Type I Error Control)"] --> B["Step 2: Run Pre-Specified Diagnostic Battery at Locked Data Cut<br/>1. Kaplan-Meier & log(-log S(t)) visual plots<br/>2. Grambsch-Therneau scaled Schoenfeld residual test & smooth beta(t) curve<br/>3. Follow-up maturity & censoring distribution audit"]
    B --> C{"Does PH Hold With Adequate<br/>Follow-Up Maturity?"}
    C -->|"Yes: Parallel log-cumulative-hazard<br/>& non-significant residual slope"| D["Step 3A: Report Standard PH Summary Package<br/>- Primary ITT p-value & Cox HR (95% CI)<br/>- Kaplan-Meier curves & medians<br/>- Pre-specified milestone survival S(t*)"]
    C -->|"No: Delayed separation, diminishing effect,<br/>crossing curves, or immature follow-up"| E["Step 3B: Report Pre-Specified NPH Companion Package<br/>- Primary ITT test result (unchanged alpha allocation)<br/>- Cox HR explicitly caveated as follow-up-weighted average<br/>- Pre-specified milestone survival differences at t*<br/>- Pre-specified dRMST(tau) & piecewise epoch HRs"]
    E --> F["Pre-Specification Firewall:<br/>No post-hoc test substitution, no data-driven t* or tau selection,<br/>and no subgroup salvage of an unsuccessful ITT primary endpoint"]

Even a well-written SAP must acknowledge four methodological and regulatory boundaries when applying these rules:

• No universal consensus statistic exists under NPH: As Bardo et al. (2024) conclude from their systematic review (whose literature search closed on 15 March 2022), no single test or estimator dominates across all non-proportional hazard patterns. Moreover, Freidlin & Korn (2019) and Mukhopadhyay et al. (2022) represent an active, unresolved methodological debate between NCI biometricians (who favor log-rank designs with ~10% sample-size inflation and extended follow-up) and industry working-group statisticians (who favor pre-specified MaxCombo testing paired with multi-metric estimation).

• Empirical meta-analysis caveats: The 90% concordance and 15-of-15 discordance figures in Mukhopadhyay et al. (2022) were derived from patient-level data reconstructed from published Kaplan-Meier curves across 63 immuno-oncology trials rather than locked sponsor individual patient datasets, and share co-authors with the Cross-Pharma NPH Working Group straw-man guidance (Roychoudhury et al., 2023).

• Scope boundaries of finalized standards: ICH E9(R1) (final, 2019) and FDA's Adaptive Design guidance (final, December 2019) contain no hazard-ratio or NPH-specific mathematical formulas; they govern the population-level summary principle and prospective adaptation rules, respectively. Likewise, EMA's 2012 Appendix 1 specifically addresses PFS and DFS in confirmatory anticancer trials.

• Draft guidance watchpoints (as of October 15, 2026): FDA's August 2025 overall-survival guidance (Docket FDA-2024-D-5850) and ICH E20 on Adaptive Designs (Step 3; FDA Docket FDA-2025-D-3023) remain drafts not for implementation. Trial teams should re-verify the ICH Efficacy Guidelines status page and FDA guidance dockets before locking regulatory submission documents.