Restricted Mean Survival Time: Justify the Comparison Horizon

Choose the restriction horizon the way you choose any other estimand attribute: before outcomes are seen, from the clinical question, and within the follow-up the trial will actually have. RMST up to a truncation time tau is the mean of event-free time when follow-up is cut off at tau, which equals the area under the survival curve from time zero to tau. The between-arm difference is the average event-free time gained within that window. It is expressed in months or years and does not depend on a proportional-hazards assumption. Because tau sets the window over which the contrast is computed, a different horizon is a different quantity, not just a more or less precise estimate of the same one. On late-separating curves, the size of the difference moves with the horizon. On crossing curves, even its sign can change.

The horizon matters most when hazards are not proportional. When curves separate late or cross, a single hazard ratio is hard to translate into clinical terms, and medians can point the other way. The CheckMate 057 reanalysis discussed below is a published example. RMST answers a narrower and more concrete question: how much event-free time, on average, each arm accumulated within a stated window.

Five things belong in the protocol or statistical analysis plan (SAP) before unblinding:

1. One primary, clinically justified horizon. Tie tau to the expected course of the disease and to the time by which a clinically meaningful difference is plausible, and write the rationale down.

2. A feasibility and precision check. Show at design that planned accrual and follow-up will leave enough participants at risk in both arms at tau. Commit to reporting arm-specific numbers at risk and the Kaplan-Meier standard error at the horizon.

3. A fixed estimator. Name Kaplan-Meier integration or a prespecified flexible parametric model, together with the variance method. Rule out switching once the data are seen.

4. Arm-level results and a scaled companion. Report each arm's RMST with a confidence interval, the between-arm difference, and at least one scaled measure such as the time lost ratio or the RMST ratio.

5. A short list of alternative horizons. Prespecify two or three other horizons and report them as supplementary analyses outside the alpha-controlled testing plan. That way they cannot be read as a search for the most favorable window.

The example below is synthetic. It involves no patients, no real trial and no reanalysis. We simulated an overall-survival endpoint for 1,000 participants (500 per arm) from two prespecified piecewise-exponential survival curves. The curves run close together through month 12 and separate afterward, a delayed-separation pattern. Enrollment was uniform over 30 months, and the data cutoff fell 54 months after the first randomization, so potential follow-up ran from 24 to 54 months. About 5% of participants per year were lost to follow-up. RMST was estimated as the exact area under each arm's Kaplan-Meier curve. Variances came from the Kaplan-Meier-based formula given by Karrison and colleagues, and 95% confidence intervals from a normal approximation.

Read at 12 months, the window closes before the curves separate. Experimental RMST is 10.28 months and control RMST is 9.97 months, a difference of 0.31 months (95% CI −0.12 to 0.74). Read at 36 months, the difference is 2.96 months (95% CI 1.33 to 4.58). Within three years, the experimental arm averaged about three more months alive. The data did not change between those two readings; only the window did.

Push the horizon to 48 months and the difference grows to 4.66 months. But the last stretch of that window rests on 24 experimental and 14 control participants still at risk. The confidence interval widens only modestly, from about 3.3 to 4.4 months across, because the area accumulates over the whole curve. Thin tail support matters more for interpretation than for interval width. The late part of the window describes a small group of participants, and a few events can reshape the curve there.

Values are from the synthetic dataset described above and are rounded; ratios were computed before rounding.

The scaled measures behave differently from the absolute difference. The time lost ratio is (tau − experimental RMST) / (tau − control RMST). Across 24, 36 and 48 months it stays between 0.80 and 0.81, a roughly 19–20% reduction in time lost within the window. Over the same horizons the absolute difference triples, from 1.54 to 4.66 months, and the RMST ratio climbs from 1.09 to 1.20. Karrison and colleagues recommend supplementing the RMST difference with the time lost ratio, because it scales the effect against the largest improvement possible within the window. A further companion, the average survival difference, is the RMST difference divided by tau. It moves the effect back to the probability scale: 0.026 at 12 months and 0.082 at 36 months.

This is a demonstration of window mechanics under one assumed curve shape. It says nothing about how often real trials show this pattern or how large real effects are.

The methods literature offers no single formula for tau. Four approaches recur. Each leaves the sponsor owing reviewers a specific piece of evidence.

Pak and colleagues treat the window as a study characteristic. It "should be prespecified in the study protocol with a certain clinical justification" and should not be changed for the final primary analysis. They add that its length may be informed by both clinical significance and study feasibility. The rule removes analyst discretion at analysis time. It does not protect against a badly placed window, which is the risk Freidlin and Korn describe below. What the reader is owed: the clinical rationale, plus design-stage evidence that follow-up will reach the landmark in both arms.

Royston and Parmar choose a design value of the horizon, t*, that approximately minimizes the required sample size. They then allow a final value at analysis, because realized accrual, follow-up and survival can differ from the design assumptions. The analysis-stage value depends on the designed RMST difference and the observed variance, not on the treatment effect observed in the data. It is capped at the largest uncensored event time to avoid extrapolation. What the reader is owed: the rule as written before unblinding, the design value, the realized value, and confirmation that the rule did not use the observed difference.

Karrison and colleagues cite an earlier proposal to base tau on the precision of the estimated survival curves. Their two worked examples were post hoc reanalyses of the NRG/RTOG 0521 and 0534 prostate cancer trials. In both, they used horizons (12 and 11 years) at which the standard error of the survival estimates was at most 7.5%, with 21 to 39 participants still at risk per arm. The same paper states that a convenient landmark should be designated a priori in the protocol to avoid potential inflation of the type I error. What the reader is owed: the standard-error ceiling, the grid of candidate horizons, and the at-risk counts at the chosen point.

The synthetic example shows why the at-risk counts matter. Both arms' Kaplan-Meier standard errors stay below 7.5% through month 52, by which point one control participant remains at risk. A standard-error ceiling alone would not have stopped the horizon from running into a nearly empty tail. Pair it with a minimum at-risk count fixed at design.

Tian and colleagues show that RMST can be estimated with valid inference up to the largest follow-up time, whether that time ends in an event or in censoring. For two arms, they suggest the smaller of the two arms' largest follow-up times. The condition is that the density of the censoring distribution does not fall to zero too fast near the end of follow-up, which uniform enrollment typically satisfies. Wider windows do not guarantee more power. The truncation time also becomes a random quantity, which they say "always needs to be accompanied explicitly" with the estimate. In the synthetic data, this rule lands at 52.1 months. There the difference is 5.37 months (95% CI 2.94 to 7.80), with 10 experimental participants and 1 control participant at risk. The inference can be valid and the window still hard to interpret or compare. Tian et al. note that a censoring-driven horizon varies across studies and subgroups, which complicates meta-analysis and subgroup analysis. What the reader is owed: the realized tau in every table, and a statement on whether the censoring condition is plausible.

The matrix below summarizes the four approaches.

Leaving the horizon, the estimator or the alternative horizons to analyst discretion invites the charge of horizon shopping, which means moving tau after seeing the curves. Freidlin and Korn reviewed comments published in the Journal of Clinical Oncology that proposed RMST reanalyses. The horizons used ranged from 15 to 108 months and appeared to be based on the observed Kaplan-Meier curves, so the quoted significance is potentially exaggerated if they were chosen to maximize it. The specification below is a recommended structure drawn from the methods literature and regulator text. No regulator prescribes it.

Take a common case. The clinical team wants 36 months because benefit is expected late. The statisticians warn that at-risk support thins after 24 months. The decision belongs at design and should rest on projected curves, not observed ones:

1. Project the numbers at risk and the Kaplan-Meier standard error at 24, 30 and 36 months in each arm. Base the projection on the planned accrual, follow-up and dropout and the assumed survival curves.

2. If the projection meets the prespecified at-risk floor and standard-error ceiling at 36 months in both arms, name 36 months as primary and carry 24 months as a supplementary horizon.

3. If it does not, either extend planned follow-up or name the latest horizon the design supports as primary and carry 36 months as a supplementary horizon. On extending follow-up, FDA's draft overall-survival guidance says that when non-proportional hazards are anticipated, the study should be designed for long-term data collection.

4. Do not settle the dispute after unblinding. Eaton and colleagues found that under late differences, the power of the RMST test can approach that of the log-rank test if the restriction time is late. Karrison et al. note that with delayed effects, an RMST comparison tends to have lower power than the log-rank test. A short horizon chosen for comfort can miss a late effect, and a long horizon chosen after the fact is horizon shopping.

• Primary horizon. State one numerical value of tau (for example, 36 months from randomization) with a written clinical rationale. Cover the expected timing of separation, historical control survival, and why the window answers the clinical question.

• Feasibility rule. Record the projected at-risk counts and standard errors that justified the horizon, plus a fallback fixed in advance. For example: "if fewer than a prespecified number of participants remain at risk in either arm at 36 months, tau becomes the latest month at which both arms meet the floor." The floor is a team choice to justify at design. At-risk counts partly reflect survival in each arm, so whenever the fallback fires, report the realized tau and the reason.

• Estimator. Use the exact area under the Kaplan-Meier step function or a prespecified flexible parametric model, and name the variance method; Royston and Parmar prefer flexible parametric modelling. Keep tau within the follow-up observed in both arms, because a Kaplan-Meier curve is undefined beyond an arm's last observation if that observation is censored. Do not switch estimators after results are seen.

• Reporting. Report each arm's RMST with a 95% confidence interval and the difference with its interval. Add the time lost ratio, the RMST ratio or both, plus the numbers at risk, cumulative events and Kaplan-Meier standard error at tau in each arm. If any rule could change tau, report the realized value.

• Alternative horizons. Prespecify two or three horizons (for example, 24 and 48 months) and report them as supplementary analyses with no alpha allocation. Because each horizon defines a different summary, these are not sensitivity analyses in the ICH E9(R1) sense, since those target the same estimand. FDA's draft likewise describes supplementary analyses as targeting different estimands. Sensitivity analyses for the primary horizon vary assumptions instead, such as the censoring assumptions or the estimator. For how sensitivity analyses attach to an estimand, see Missing Data vs Intercurrent Events: Estimand-Aligned Sensitivity Analysis.

• Censoring and intercurrent events. Apply the same censoring rules and intercurrent-event strategy as the primary time-to-event analysis: loss to follow-up, withdrawal of consent and data cutoff. See Time-to-Event Endpoints: Writing Censoring Rules Readers Can Follow.

The workflow below shows how the horizon decision moves from clinical question to a locked SAP.

flowchart TD
  A["Clinical question and expected timing of separation"] --> B["Candidate horizons from the clinical rationale"]
  B --> C["Project at-risk counts and Kaplan-Meier SE per arm at each candidate"]
  C --> D{"At-risk floor and SE ceiling met at the clinical horizon in both arms?"}
  D -->|Yes| E["Name the clinical horizon as primary tau"]
  D -->|No| F{"Can planned follow-up be extended?"}
  F -->|Yes, extend and re-project| C
  F -->|No| G["Name the latest supported horizon as primary and keep the clinical horizon as supplementary"]
  E --> H["Lock estimator, variance method and reporting shell"]
  G --> H
  H --> I["Lock two or three alternative horizons as supplementary analyses"]
  I --> J["Finalize the SAP before unblinding"]

Before unblinding, check the draft SAP against this list.

Public regulator text sets direction on prespecification. It gives no method for choosing tau. Read each document for its scope and status.

FDA's draft guidance Approaches to Assessment of Overall Survival in Oncology Clinical Trials (docket FDA-2024-D-5850) was prepared by the Oncology Center of Excellence, CDER and CBER. It is the most specific public regulator text on RMST in this context:

• Supplementary analyses when non-proportional hazards are anticipated. "If non-proportional hazards are anticipated, sponsors should specify in the SAP additional sensitivity analyses to evaluate the robustness of the overall survival results. Supplementary analyses, such as landmark survival rates, restricted mean survival time, or other metrics, should be specified in the SAP and may provide supplementary information to further characterize overall survival." The same section says supplementary analyses should target different estimands.

• Design for long follow-up. When non-proportional hazards are anticipated, the draft says the study should be designed for long-term data collection, with sample size and power calculations based on justifiable assumptions.

• The post hoc boundary. Statistical analyses of overall survival should be specified a priori in the protocol or SAP, before any knowledge of results or unblinding. FDA considers analyses outside that scope post hoc and exploratory, suitable for hypothesis generation but not for statistical testing with alpha allocation.

• The default summary. The draft generally recommends the hazard ratio from a Cox model as the summary measure, and the log-rank test for the primary analysis of overall survival when there is alpha allocation.

• Not a sole or primary evaluation. For handling subsequent therapy or crossover, the draft lists RMST among the approaches that evaluate different estimands through supplementary analyses. It adds that many of these methods rely on unverifiable assumptions and generally are not suitable as the sole or primary evaluation of overall survival.

EMA's Appendix 1 on progression-free and disease-free survival (EMA/CHMP/27994/2008/Rev.1) was adopted on 13 December 2012 and came into effect on 1 July 2013. It does not mention RMST. It matters here for the general rules it sets for time-to-event summaries:

• Justify and prespecify the summary measure. The size of effect should be quantified by plotting the survivor functions and by estimating the hazard ratio, the median and other percentiles, and event-free percentages at particular time points. Over-reliance on differences in medians should be avoided, and "in any case, the choice of the summary measure should be justified and pre-specified."

• Plan for departures from proportional hazards. Sensitivity analyses should be planned to address important assumptions in the methods used, including proportional hazards.

• Distrust late changes. For open-label trials, the appendix warns that amendments to important aspects of the analysis made in the knowledge of accruing data would give rise to concern.

The appendix predates later revisions of the parent anticancer guideline. Check EMA's current text before citing it in a submission.

Neither FDA's draft nor EMA's appendix prescribes a method for choosing tau, endorses a data-driven horizon search, or names a horizon for any indication. ICH E9(R1) supplies the framework, treating the summary measure as an estimand attribute and separating sensitivity from supplementary analyses, but it says nothing about RMST. The sponsor carries the burden of choosing and justifying tau in advance and of showing that the follow-up supports it.

RMST characterizes and stress-tests a time-to-event result. It does not rescue a failed primary analysis.

Freidlin and Korn, of the National Cancer Institute, examined comments in the Journal of Clinical Oncology that proposed RMST reanalyses of published trials. The horizons used were 15, 21, 24, 45, 48 and 108 months. Because the choices appeared to be based on the observed Kaplan-Meier curves, the quoted significance is potentially exaggerated if the horizons were chosen to maximize it. Choosing tau before the study is hard too: the shape of the curves is uncertain, and a poor choice could dramatically reduce power. Their conclusion is that RMST and related methods can be useful secondary analyses. More convincing evidence is needed before abandoning log-rank-based primary analyses of definitive trials.

In Eaton and colleagues' design study, the choice of restriction time had a large impact on power, while the durations of accrual and follow-up had little influence. With early differences, the RMST test had higher power than the log-rank test. Under proportional hazards or late differences, its power could approach that of the log-rank test if the restriction time was late. They recommend a restriction time that is clinically relevant to the disease and the trial setting. Royston and Parmar's simulations show the other side: in their non-proportional-hazards designs, the RMST test held its planned power while the log-rank test was underpowered. The direction depends on the shape of the departure, which is one more reason to fix the horizon from the expected curve shape, not the observed one.

Pak and colleagues show the interpretive value. They reconstructed data from the published CheckMate 057 curves, which compared nivolumab with docetaxel in advanced non-small cell lung cancer. For overall survival, the hazard ratio was 0.73, and the medians were 12.2 versus 9.4 months with overlapping confidence intervals. For progression-free survival, the hazard ratio was 0.92 (P = .39) on curves that crossed around month 7, while the median favored docetaxel (2.3 versus 4.2 months). The RMST difference favored nivolumab on both endpoints. Within a 24-month window, overall-survival RMST was 13.0 versus 11.3 months, a difference of 1.7 months (95% CI 0.4 to 3.1; P = .01).

Two cautions apply. The 24-month window was the authors' choice in a reanalysis, not a horizon prespecified by the trial; for a new trial, their own recommendation is to fix the window in the protocol. And the example shows interpretability, not a regulatory basis for a claim.

When proportional hazards hold, the hazard ratio and the log-rank test remain the default. Karrison et al. echo Royston and Parmar's view that the Cox hazard ratio should be the primary measure when the assumption is reasonably satisfied, and that RMST-based measures are a good choice when it is violated. Under delayed separation, a supplementary RMST analysis translates the curves into time gained within a stated window, provided the window was locked before unblinding. Adjacent decisions that the horizon has to agree with:

• Competing risks. When another event type prevents the event of interest, settle the probability question before the estimator. See Competing Risks: State the Probability Question Before the Model.

• Multiplicity. If any horizon enters the alpha-controlled hierarchy, it needs a place in the multiple-testing plan; supplementary horizons stay outside it. See Multiple Endpoints in Clinical Trials: Hierarchy, Co-Primaries, and Error Control.

• SAP lock. For what else the plan has to fix before unblinding, see Statistical Analysis Plans for Endpoints: What Must Be Locked Before Unblinding.

This is methods guidance for trial teams, not clinical advice. The examples come mainly from oncology, so applying them to other therapeutic areas is an analogy, not evidence. The power statements come from simulation studies in specific scenarios.

Peer-reviewed methods research and regulator documents cited in this guide:

1. Royston P, Parmar MKB. Restricted mean survival time: an alternative to the hazard ratio for the design and analysis of randomized trials with a time-to-event outcome. BMC Med Res Methodol. 2013;13:152.

2. Pak K, Uno H, Kim DH, et al. Interpretability of cancer clinical trial results using restricted mean survival time as an alternative to the hazard ratio. JAMA Oncol. 2017;3(12):1692-1696.

3. Tian L, Jin H, Uno H, et al. On the empirical choice of the time window for restricted mean survival time. Biometrics. 2020;76(4):1157-1166.

4. Karrison T, Hu C, Dignam J. Scaling and interpreting treatment effects in clinical trials using restricted mean survival time. Clin Trials. 2025;22(1):3-10 (published online 2024).

5. Freidlin B, Korn EL. Methods for accommodating nonproportional hazards in clinical trials: ready for the primary analysis? J Clin Oncol. 2019;37(35):3455-3459.

6. U.S. Food and Drug Administration. Approaches to Assessment of Overall Survival in Oncology Clinical Trials: Guidance for Industry (Draft Guidance). August 2025; Docket FDA-2024-D-5850.

7. U.S. Food and Drug Administration. Approaches to Assessment of Overall Survival in Oncology Clinical Trials (guidance page; status Draft).

8. International Council for Harmonisation. E9(R1) Addendum on Estimands and Sensitivity Analysis in Clinical Trials to the Guideline on Statistical Principles for Clinical Trials. Step 4, 20 November 2019.

9. European Medicines Agency. Appendix 1 to the guideline on the evaluation of anticancer medicinal products in man: methodological consideration for using progression-free survival (PFS) or disease-free survival (DFS) in confirmatory trials. EMA/CHMP/27994/2008/Rev.1. Adopted 13 December 2012; effective 1 July 2013.

10. Eaton A, Therneau T, Le-Rademacher J. Designing clinical trials with (restricted) mean survival time endpoint: practical considerations. Clin Trials. 2020;17(3):285-294.