Pembrolizumab in Combination With Epacadostat or Placebo in Cisplatin-ineligible Urothelial Carcinoma (KEYNOTE-672/ECHO-307): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pembrolizumab in Combination With Epacadostat or Placebo in Cisplatin-ineligible Urothelial Carcinoma (KEYNOTE-672/ECHO-307) (NCT03361865), a randomized phase 3 study. The primary outcome is Objective Response Rate (ORR) With Pembrolizumab + Epacadostat Versus Pembrolizumab + Placebo.

2. Clinical Question

3. Trial Design

The registry identifies NCT03361865 as a Phase 3, randomized, parallel-group trial with enrollment of 93 participants. Its stated purpose was to evaluate the efficacy and safety of pembrolizumab plus epacadostat versus pembrolizumab plus placebo among participants with cisplatin-ineligible urothelial carcinoma. The two listed regimens were pembrolizumab 200 mg plus epacadostat 100 mg BID and pembrolizumab 200 mg plus placebo BID.

Random allocation is relevant because, in principle, it supports comparison of groups formed without selecting treatment according to participants’ observed characteristics. The registry lists the allocation as randomized. It lists masking as none, while the official trial title describes the study as double-blind. These registry entries do not agree, and the record does not explain the discrepancy. The masking details should therefore not be inferred from the title alone.

The primary outcome was objective response rate, assessed at Week 9. The registry defines the intention-to-treat population as all randomized participants. The arm counts reported for the outcome were 44 and 49. The study status is completed, and the registry reports primary completion on 2018-08-09. These registry entries describe the registered design and outcome timing; they do not establish what analysis procedures were planned or used beyond what is explicitly recorded.

The registry also lists safety and tolerability outcomes concerning participants who experienced adverse events and participants who discontinued study treatment due to an adverse event. There are three outcome measures in total, including the primary outcome, but only two secondary outcomes are posted in the record summarized for these results. The registry record does not report a detailed statistical analysis plan, an original sample-size justification, or details of interim analyses. Those features cannot be reconstructed from the enrollment or outcome estimates alone.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intention-to-Treat (ITT) population consisted of all randomized participants.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The Intention-to-Treat (ITT) population consisted of all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Objective Response Rate (ORR) With Pembrolizumab + Epacadostat Versus Pembrolizumab + Placebo, measured over Week 9.

Objective response rate is a binary-outcome summary expressed as the percentage of participants meeting the response definition. For this trial, the definition was a confirmed complete response or partial response under RECIST v1.1, determined by the investigator. The outcome was assessed at Week 9. The registry additionally says that responses were based on investigator assessments per RECIST 1.1 without confirmation, using all scans up to the cutoff date. Because the wording includes both “confirmed” in the definition and “without confirmation” in the assessment description, the record leaves some ambiguity about the operational response rule.

Response rate is used to describe how many participants meet a prespecified tumor-response category during the stated assessment period. It provides a direct proportion for each randomized group, unlike a time-to-event measure, which accounts for the timing of events. The registry reports 31.8% for pembrolizumab plus epacadostat and 24.5% for pembrolizumab plus placebo. These percentages describe the observed response proportions in the posted outcome population; by themselves, they do not establish that the underlying response probabilities differ.

A binary endpoint also simplifies varied participant experiences into response or no response according to the stated criteria. It does not summarize response duration, progression-free survival, overall survival, or other outcomes unless those are separately reported. The registry record’s primary measure is specifically the Week 9 objective response rate, and the available results should be interpreted within that scope.

7. Results Posted in the Registry

• Pembrolizumab 200 mg + Epacadostat 100 mg BID: 31.8% (14/44) versus 24.5% (12/49) on control; risk difference 7.3 percentage points (95% CI -11.0 to 25.6), risk ratio 1.30 (0.67–2.50); unadjusted two-proportion z-test p = 0.432.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either meets the response definition or does not. A response rate is the number of participants classified as responders relative to the number assessed in the relevant group, expressed as a percentage. The registry reports arm estimates of 31.8% and 24.5%, with outcome arm counts of 44 and 49. These are descriptive estimates for the randomized groups, not guarantees of the response rate that would be seen in another sample.

What does the risk difference represent?

The risk difference expresses the contrast between the two response proportions on an absolute scale. The reported direction is epacadostat combination minus placebo combination. Its estimate is 0.073, and its 95% confidence interval is -0.110 to 0.256. A value of zero represents equal proportions on this scale. Values above zero represent a higher observed response proportion in the epacadostat arm, while values below zero represent a higher proportion in the placebo arm. Because the interval spans zero, the posted estimate is compatible with differences in either direction.

The confidence interval quantifies sampling uncertainty under the method used to construct it. It is not a range containing a fixed percentage of individual responses, and it does not account automatically for every possible source of bias or uncertainty. Its interpretation depends on the analysis method and assumptions. The registry record does not report the full statistical plan or enough detail to verify all analysis choices, so the interval should be read as the reported precision summary rather than as a complete account of uncertainty.

How should the p-value be read?

The recalculated unadjusted comparison has p = 0.432. A p-value describes how unusual results at least as incompatible with a specified null comparison would be if that null comparison and the test assumptions held. It does not measure the probability that the null is true, the probability that a result is due to chance, or the size or clinical importance of an effect. A non-small p-value does not prove that the regimens have the same response rate. In this comparison, the confidence interval is useful alongside the p-value because it displays the range of contrasts that remain compatible with the estimate at the stated confidence level.

The posted comparison also gives a risk ratio of 1.299 with interval limits 0.675 and 2.501, and an odds ratio of 1.439 with interval limits 0.580 and 3.571. A risk ratio compares response probabilities as a ratio, while an odds ratio compares response odds. These scales answer a related but different question from the risk difference. The intervals for both relative measures include the value representing no relative difference. The different scales should not be treated as interchangeable, and their numerical size does not directly express the absolute change in response probability.

Why use a confidence interval?

A point estimate alone can obscure how much the result could vary because of sampling. A confidence interval pairs the estimate with a range of values that are reasonably compatible with the data under the interval’s assumptions. Wider intervals indicate less precision. Here, the arm-specific intervals and the contrast interval show that the observed proportions do not pin down a narrow range for the underlying response difference. The contrast interval is especially relevant when the scientific question is the difference between regimens.

The posted calculations are unadjusted re-calculations based on the summary statistics. They should be distinguished from a sponsor’s prespecified or adjusted analysis, which is not included among the registry analysis entries. The registry lists zero analysis entries. Therefore, there is no posted sponsor analysis to compare with these summary-based calculations, and the record does not establish whether a more detailed analysis was performed elsewhere.

Randomization supports a treatment-group comparison by making allocation independent of participants’ measured and unmeasured characteristics in expectation. It does not guarantee balance in a modest-sized trial, eliminate missing outcome information, or remove uncertainty. The record identifies an intention-to-treat population as all randomized participants, which is a useful population definition, but does not report the missing-data procedures or whether all randomized participants contributed a Week 9 response classification.

General statistical context: binary outcomes can be analyzed using methods that model a response probability or compare response proportions directly. The chosen method affects the interval and test, particularly with small group sizes or sparse outcomes. The registry record does not specify the method used for the sponsor’s primary analysis, and the posted summary should not be used to infer an unreported protocol or analysis plan.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the response proportions and their difference. The reported response rate was 31.8% for pembrolizumab plus epacadostat, with a 95% confidence interval from 22.46 to 55.24. For pembrolizumab plus placebo, the estimate was 24.5%, with a 95% confidence interval from 15.33 to 43.67. Both arm intervals cover a wide range of possible response proportions, so neither arm estimate is highly precise.

The most direct interval for the treatment contrast is the risk difference of 0.073, with 95% confidence limits of -0.110 and 0.256. This interval includes zero and extends to values in both directions. Thus, the observed contrast does not precisely distinguish a higher response proportion in one arm from a higher proportion in the other. The point estimate is only one part of the result; the interval conveys that the data remain compatible with a broad range of contrasts.

Confidence intervals are not guarantees that the true value lies within the displayed limits. In general, an interval procedure has a stated long-run coverage property under its assumptions. It also does not account for uncertainty caused by features that are not represented in the analysis, such as unreported missing-data handling or possible measurement limitations. Here the registry describes investigator assessments and gives no further detail about missing Week 9 assessments.

The confidence intervals for the relative measures are also wide: the risk ratio is 1.299, with limits 0.675 and 2.501, and the odds ratio is 1.439, with limits 0.580 and 3.571. These intervals reinforce that the comparison is not tightly estimated. The record’s reported precision should therefore be read as limited, rather than as evidence of equivalence or of a firmly established difference.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size display is a planning illustration based on the observed risk difference, not a record of the trial’s original design justification. Its figures are participants per arm, rather than total participants or total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted in each row is the stated fraction of the observed effect. The registry record does not report the assumptions used for the trial’s own original sample-size planning.

The 80% power column gives the planned participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding number per arm for a design with a 90% chance under the same conditional framework. Power is a property of a proposed design under assumed conditions; it is not the probability that the study’s conclusion is correct.

The rows target 100%, 75%, and 50% of the observed effect. The displayed requirements increase as the target effect becomes smaller: the figures for 100% are 591 per arm for 80% power and 790 per arm for 90% power; for 75%, they are 1,029 and 1,377; and for 50%, they are 2,267 and 3,034. This pattern reflects a general principle: smaller differences are harder to distinguish from sampling variation and therefore require more participants, all else equal.

These figures are not observed power for the completed trial. They are planning illustrations that depend on the stated assumptions and the observed effect used as their starting point. Since observed effects can be imprecise, especially in a small study, treating them as known planning truths would overstate what the illustration can establish. The registry record does not report the original trial’s sample-size calculation or its assumptions.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.245; treatment proportion p₁ = 0.318; average p̄ = 0.282.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6360 = 1.2466.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6339 = 0.5335.
4. n = (1.2466 + 0.5335)² / (0.0733)² = 590.1, rounded up to 591 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.244897959183673                          # control proportion
p1 <- 0.318181818181818                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3361865)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 591 (80% power), 790 (90% power)
 75% of observed effect: n per arm = 1,029 (80% power), 1,377 (90% power)
 50% of observed effect: n per arm = 2,267 (80% power), 3,034 (90% power)
power.prop.test: 590.1 
Simulated power at n = 591 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists three outcome measures in total: the primary objective response rate and two secondary safety and tolerability outcomes. The secondary outcomes concern the number of participants experiencing adverse events and the number discontinuing study treatment due to adverse events. The record summarized for these results includes two posted secondary outcomes. It does not report a multiplicity strategy, such as an adjustment procedure or a hierarchy for interpreting multiple outcomes. Without such information, the nominal uncertainty for one result should not be treated as if it automatically accounts for examining multiple outcomes.

The registry record does not report whether there were interim analyses, whether any interim findings affected study conduct, or what statistical stopping rules may have applied. It also does not provide a complete statistical analysis plan. These details cannot be inferred from the trial’s Phase 3 designation, completion status, enrollment, or posted endpoint values.

The primary population is described as intention-to-treat and is defined as all randomized participants. This identifies the intended population for the primary outcome, but the record does not state how missing or unevaluable response assessments were handled. It does not give a count of participants with missing Week 9 assessments, explain imputation or censoring rules for this binary outcome, or say how deviations from assigned treatment were handled in the analysis.

The outcome definition also contains an important wording detail: it refers to confirmed complete or partial responses, while the assessment description says investigator assessments were used without confirmation and included all scans up to the cutoff date. The registry does not resolve this wording or provide further adjudication details. These omissions constrain independent evaluation of the endpoint and analysis process. They do not establish that a particular method was or was not used; they mean that it is not reported in the registry record.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: malignant neoplasm progression (18.6%), urinary tract infection (12.2%), chronic kidney disease (6.1%), device occlusion (4.7%), haematuria (4.7%).

The safety results report participant counts in groups with safety denominators of 43 for pembrolizumab plus epacadostat and 49 for pembrolizumab plus placebo. Serious adverse events affected 23 participants in each group. Other adverse events affected 42 participants in the epacadostat group and 47 in the placebo group. The total safety group lists 46 participants with serious adverse events and 89 with other adverse events, with 92 participants at risk for each category. These are counts of participants affected, not a measure of event severity beyond the categories stated.

The registry also reports 17 deaths in the epacadostat group and 19 in the placebo group, with 36 in total. The record does not establish that these deaths were caused by treatment, nor does a count alone describe timing, context, or comparison adjusted for follow-up. The listed serious adverse event terms include malignant neoplasm progression at 18.6%, urinary tract infection at 12.2%, chronic kidney disease at 6.1%, device occlusion at 4.7%, haematuria at 4.7%, and urosepsis at 4.7%. The denominator and further event-level details are not reported in the registry record.

Safety counts are descriptive. They should not be interpreted as proof that a regimen caused or prevented an event. The safety denominators total 92, while enrollment is 93; the reason for this difference is not reported in the registry record. The posted safety information does not replace detailed assessment of event timing, exposure, seriousness, relatedness, and discontinuation.

15. What the Result Does, and Does Not, Mean

The posted results show a higher observed Week 9 objective response rate in the pembrolizumab plus epacadostat group than in the pembrolizumab plus placebo group: 31.8% versus 24.5%. The estimated risk difference was 0.073. These are descriptive results for the trial’s reported groups and should be interpreted together with their uncertainty. The 95% confidence interval for the difference, -0.110 to 0.256, includes zero and allows for a range of possible differences in either direction.

The result does not establish that the regimens have identical response rates. A broad interval that includes zero is not proof of equivalence, and the registry does not report an equivalence or noninferiority framework. Nor does the point estimate alone establish a dependable difference. The recalculated unadjusted p-value of 0.432 does not resolve that uncertainty; it is a summary of compatibility with a null comparison under the test assumptions, not a measure of clinical importance or a probability that a treatment effect exists.

The primary endpoint concerns investigator-assessed objective response at Week 9. It does not, by itself, establish the duration of response, longer-term disease control, survival, or any other outcome not reported through that endpoint. The record’s wording about confirmation is not fully consistent, and the details of missing assessment handling are not reported. These features limit how fully the response result can be evaluated.

The safety counts describe participants with adverse events and deaths in the listed groups. They do not identify causation, account for every aspect of exposure or follow-up, or establish a complete comparison of harms. Overall, the registry record gives a response estimate and safety counts but leaves substantial uncertainty about the treatment contrast and several details of analysis. No treatment recommendation follows from these registry results alone.

16. Why This Trial Matters Statistically

This trial is statistically informative as an example of the distinction between an observed difference and a precisely estimated difference. The response percentages differ descriptively, but the contrast interval spans zero and values in both directions. That combination illustrates why effect estimates should be interpreted with their uncertainty rather than by comparing percentages alone or relying on a p-value in isolation.

The trial also highlights the importance of identifying the analysis population and endpoint definition. The registry specifies an intention-to-treat population and a Week 9 response measure, yet the description combines a confirmed-response definition with assessments described as unconfirmed. The record does not resolve that wording or detail the handling of missing assessments. Such details affect how readers understand what outcome was actually classified and which participants contributed information.

Another statistical issue is the limited information available about the analysis plan. The record lists no analysis entries and does not report multiplicity procedures, interim analyses, or the trial’s original sample-size rationale. Consequently, the displayed recalculated comparison can be read as an unadjusted summary-based analysis, but it cannot stand in for an unreported sponsor analysis plan.

Finally, the planning illustrations show how required sample size depends on the target effect and desired power. They are not a retrospective measure of what the completed trial could detect, and they are not evidence that the study was designed around those values. Together, these features make transparent reporting of estimands, analysis choices, missing data, and planning assumptions especially important for interpreting clinical trial evidence.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several limitations specific to this trial’s posted results. The primary endpoint definition refers to confirmed complete or partial responses, while the assessment description says responses were based on investigator assessments without confirmation. It does not clarify how these statements were reconciled or describe independent review of responses. The assessment timeframe is Week 9, with scans up to the cutoff date, but details of assessment timing and missing evaluations are not reported.

The primary analysis is described for the intention-to-treat population, defined as all randomized participants. However, the record does not report the number of participants with missing or unevaluable response assessments or how such cases were treated. It lists outcome arm counts of 44 and 49, while the safety denominators are 43 and 49. The reason that the safety denominator total is 92 whereas enrollment is 93 is not reported in the registry record.

The registry lists masking as none, whereas the official title describes the study as double-blind. The record does not explain the inconsistency, so the extent of masking cannot be established from these entries. The registry also does not report the detailed analysis plan, multiplicity handling, interim analyses, or the original sample-size justification. There are no analysis entries listed, limiting comparison of the summary-based recalculation with a sponsor-reported analysis.

Safety information is presented as counts and selected event terms, without the event-level timing, exposure, relatedness, or denominator details needed for a fuller assessment. The record’s posted results therefore support a bounded descriptive interpretation, not a complete reconstruction of trial conduct or a comprehensive evaluation of efficacy and safety.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Pembrolizumab in Combination With Epacadostat or Placebo in Cisplatin-ineligible Urothelial Carcinoma (KEYNOTE-672/ECHO-307) — NCT03361865.
• Registry record last updated 2025-08-22; status last verified 2025-08.
• Results first posted 2019-08-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT03361865 is a completed Phase 3 randomized parallel-group trial of pembrolizumab plus epacadostat versus pembrolizumab plus placebo in cisplatin-ineligible urothelial carcinoma. Enrollment was 93. The primary outcome was Week 9 objective response rate in the intention-to-treat population. The reported response estimates were 31.8% and 24.5%; the risk difference was 0.073, with a 95% confidence interval from -0.110 to 0.256 and a recalculated unadjusted p-value of 0.432.

The posted interval is wide and includes zero, leaving substantial uncertainty about the difference. Safety results list serious and other adverse event counts and deaths, but do not establish causation. The registry record does not report a detailed analysis plan, missing-data procedures, multiplicity methods, interim analyses, or the original sample-size rationale. The title’s double-blind wording also differs from the registry masking entry, which is listed as none.