Carboplatin-paclitaxel With Retifanlimab or Placebo in Participants With Locally Advanced or Metastatic Squamous Cell Anal Carcinoma (POD1UM-303/InterAACT 2).: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Carboplatin-paclitaxel With Retifanlimab or Placebo in Participants With Locally Advanced or Metastatic Squamous Cell Anal Carcinoma (POD1UM-303/InterAACT 2). (NCT04472429), a randomized phase 3 study. The primary outcome is Progression-free Survival (PFS).

2. Clinical Question

This is a comparison of treatment strategies that share the same chemotherapy backbone and differ by the addition of retifanlimab or placebo. Randomization supports a between-group comparison, while masking was recorded as quadruple. The registry identifies a parallel-group design and a phase 3 global, multicenter study. Its description concerns participants with inoperable disease who had not previously received systemic chemotherapy; it does not establish how results apply to people outside that eligibility description. The primary endpoint combines disease progression and death, so it is not a measure of tumor response alone. Response outcomes and overall survival are listed separately as secondary endpoints.

3. Trial Design

NCT04472429 is a completed phase 3, randomized, parallel-group study sponsored by Incyte Corporation. The registry describes a global, multicenter, placebo-controlled, double-blind study; the masking field records quadruple masking. Enrollment was 308. The intervention groups were retifanlimab 500 mg every four weeks plus carboplatin-paclitaxel and placebo plus carboplatin-paclitaxel. Each group had 154 participants in the primary endpoint results.

The trial enrolled participants with squamous cell carcinoma of the anal canal that was inoperable and locally recurrent or metastatic. Participants had not previously been treated with systemic chemotherapy. Both groups received carboplatin on Day 1 and paclitaxel on Days 1, 8, and 15; the assigned retifanlimab or placebo was given on Day 1 of each 28 day cycle. These details describe the treatment schedules recorded in the registry and do not provide further dose details for the chemotherapy.

The primary endpoint was progression-free survival, assessed up to 33.9 months. The registry defines it from randomization until centrally reviewed progression by RECIST v1.1 or death from any cause, whichever occurred first. The primary population was the Full Analysis Set, with participants analyzed according to randomized treatment and strata. The sponsor estimated median progression-free survival using Kaplan-Meier methods and reported a stratified log-rank comparison.

Secondary outcomes included overall survival, objective response rate, duration of response, disease control rate, and treatment-emergent adverse events during the randomized and open-label monotherapy periods. Overall survival was assessed up to 56.5 months; response outcomes were assessed up to 445 days. The registry record does not report the trial's original sample-size justification, detailed allocation procedures, or the complete statistical analysis plan. Those omissions limit how much can be inferred about design choices beyond the recorded features.

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.

Before assignment: This study randomized participants at 70 study centers in Australia, Belgium, Germany, Denmark, Spain, France, the United Kingdom, Italy, Japan, Norway, Puerto Rico, Sweden, and the United States.

Randomized Period

Reasons for not completing this period:

Optional Open-label Monotherapy Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: all randomized participants. Participants were analyzed according to the treatment and strata they had been assigned during randomization. Median PFS time was estimated using the Kaplan-Meier method. The confidence interval for median PFS time was calculated using the method of Brookmeyer and Crowley.

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.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival (PFS), measured over up to 33.9 months.

Progression-free survival (PFS) is the time from randomization until the first qualifying event: disease progression or death from any cause. In this study, progression was defined using RECIST v1.1 and assessed by a blinded independent central review committee. A target or non-target lesion could progress, or a new lesion could appear. Death counted as an event even if progression had not previously been documented. The endpoint was assessed up to 33.9 months.

PFS is used in clinical trials to measure how long participants remain alive without documented disease progression. Combining progression and death makes it a time-to-event endpoint, rather than a simple count of responses at a single visit. It also means the result reflects both components: the registry does not provide a separate primary analysis for progression alone in the record.

The sponsor estimated median PFS with the Kaplan-Meier method. The median is the estimated time by which half of the analyzed population has experienced the event, according to the survival curve; it is not the average time to progression or death. Comparing the full time-to-event experience can use information about when events occur and when follow-up ends, rather than reducing each participant's follow-up to an event/no-event status at a fixed time.

As a general statistical point, PFS can provide an earlier endpoint than overall survival, but its interpretation depends on how progression is assessed and on follow-up and censoring. Central review and a defined RECIST criterion give the endpoint a stated assessment framework. The registry record does not report all details needed to evaluate censoring procedures or the handling of missing assessments.

7. Results Posted in the Registry

• Retifanlimab 500 mg Q4W + Chemotherapy vs Placebo + Chemotherapy: hazard ratio 0.63 (95% CI 0.47–0.84), reported p < 0.001 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Overall Survival

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (stratified log-rank test); it was not recalculated.
• Result:
  • Retifanlimab 500 mg Q4W + Chemotherapy vs Placebo + Chemotherapy: hazard ratio 0.75 (95% CI 0.55–1.01), reported p = 0.030 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Retifanlimab 500 mg Q4W + Chemotherapy vs Placebo + Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate (ORR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Retifanlimab 500 mg Q4W + Chemotherapy: 55.8% (86/154) versus 44.2% (68/154) on control; risk difference 11.7 percentage points (95% CI 0.6 to 22.8), risk ratio 1.26 (1.01–1.59); unadjusted two-proportion z-test p = 0.040.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Retifanlimab 500 mg Q4W + Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Disease Control Rate (DCR)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Retifanlimab 500 mg Q4W + Chemotherapy: 87.0% (134/154) versus 79.9% (123/154) on control; risk difference 7.1 percentage points (95% CI -1.1 to 15.4), risk ratio 1.09 (0.99–1.20); unadjusted two-proportion z-test p = 0.092.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Retifanlimab 500 mg Q4W + Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the description beyond progression-free survival. Overall survival addresses time until death, while objective response and disease control describe tumor status. The posted point estimates generally have a direction consistent with the primary PFS comparison, but the strength and precision of the evidence vary by endpoint. They should be read as complementary outcomes rather than as repeated measurements of the same clinical question.

The registry reports a sponsor analysis for overall survival and a sponsor test for objective response. It does not post a sponsor comparison for disease control rate. The unadjusted recalculation for disease control has an interval that includes zero, while the response comparison has a narrower positive risk-difference interval. These results should not be collapsed into a single overall conclusion: each endpoint has its own definition, follow-up, uncertainty, and analysis method.

Secondary endpoints carry less inferential weight when many outcomes are examined and no multiplicity adjustment or hierarchical testing plan is reported. As a general statistical issue, testing many outcomes increases the chance of at least one apparently noteworthy result arising by chance. The registry record does not report a multiplicity procedure for the secondary outcomes, so their p-values should be treated as supportive or exploratory rather than as equivalent to the primary endpoint's test.

Other listed secondary outcomes concern treatment-emergent adverse events during the randomized and open-label monotherapy periods, including events leading to discontinuation. The registry record includes some safety summaries, but does not provide a complete set of comparative estimates for every listed safety outcome in the registry record reported. Those outcomes have a different purpose from efficacy endpoints: they describe harms and treatment tolerability, and their interpretation depends on exposure and the period being counted. The available results do not justify inferring an overall benefit-harm balance from selected endpoints alone.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Overall Survival
• Objective Response Rate (ORR)
• Duration of Response (DOR)
• Disease Control Rate (DCR)
• Number of Participants With Any Treatment-emergent Adverse Event (TEAE ) During the Randomized Period
• Number of Participants With Any TEAE Leading to Discontinuation of Study Drug During the Randomized Period
• Number of Participants With Any TEAE During the Open-label Monotherapy Period
• Number of Participants With Any TEAE Leading to Discontinuation of Study Drug During the Open-label Monotherapy Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome. A participant's follow-up contributes information until progression or death occurs, or until the recorded follow-up ends without such an event. The latter situation is generally handled through censoring in survival analysis. The registry identifies Kaplan-Meier estimation for median PFS, but details of censoring rules and missing assessments are not reported in the registry record.

What does the Kaplan-Meier median represent?

As a general statistical explanation, the Kaplan-Meier method estimates the probability of remaining event-free over time while accounting for participants whose event status is not observed through the end of follow-up. The estimated median is the time at which the estimated event-free probability reaches half. It is a summary of the survival curve, not an arithmetic average. The reported medians are therefore best read together with the time-to-event comparison and their confidence intervals, rather than as stand-alone measures of every participant's experience.

How should the hazard ratio be read?

The sponsor reported a hazard ratio for retifanlimab plus chemotherapy versus placebo plus chemotherapy, using a stratified log-rank test. In general, a hazard ratio compares the event rates at a given time between groups, conditional on remaining under observation and event-free up to that time. A value below 1 favors a lower estimated event hazard in the first-named group, while a value above 1 favors a higher estimated event hazard. It does not directly express a difference in median survival time or the probability that a participant will experience an event.

The interpretation of a single hazard ratio is clearest when the relative hazards are reasonably stable over time. The registry record does not report a test or assessment of that assumption. The stratified log-rank test incorporates the trial's recorded stratification in the comparison; the specific strata are not included in the posted details. No alternative time-varying effect analysis is reported in the registry record.

What do the binary-outcome methods add?

Objective response rate and disease control rate are proportions, not time-to-event measures. The posted arm estimates are accompanied by confidence intervals. The sponsor reported a Cochran-Mantel-Haenszel test for objective response rate. As a general explanation, this method can compare groups while accounting for strata; the registry record does not describe the particular strata used in that analysis. No sponsor comparison is posted for disease control rate.

The recalculated binary comparisons are simple unadjusted calculations from the posted summary statistics. They are not substitutes for the sponsor's analysis and do not incorporate any stratification unless that information is explicitly included. For objective response, the recalculated risk difference is 0.117, with a 95% confidence interval from 0.006 to 0.228 and unadjusted p = 0.04. The sponsor's reported test gives p = 0.013. For disease control, the recalculated risk difference is 0.071, with a 95% confidence interval from -0.011 to 0.154 and unadjusted p = 0.092; no sponsor test result is posted. These recalculations describe the proportions in the posted summaries, not adjusted treatment effects.

As a general statistical point, over-dispersion arises when observed variation is greater than a model assumes. It can make standard errors too small if ignored. The registry record does not report an over-dispersion model for these endpoints, so it would be inappropriate to assert that one was used or required. Likewise, the record does not report an imputation method for missing outcome data, a detailed analysis of censoring, or a complete model specification.

What role do confidence intervals and p-values play?

A confidence interval communicates precision by giving a range of values compatible with the data under the method used. A p-value describes how inconsistent the observed data are with a specified null hypothesis under the analysis assumptions; it is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an effect. The sponsor's reported time-to-event analyses use hazard ratios, confidence intervals, and stratified log-rank p-values. The binary outcome estimates and the sponsor tests answer related but not identical statistical questions.

Finally, reported analyses and planning illustrations answer different questions. The sample-size illustrations use fractions of observed effects and specified planning assumptions; they are not estimates of the trial's achieved power. The original design assumptions and sample-size justification are not reported in the registry record. No inference about interim monitoring or stopping rules can be made from the posted results.

11. Confidence Intervals and Precision

The primary PFS hazard ratio was 0.63, with a 95% confidence interval from 0.47 to 0.84. The interval lies below 1, consistent with the estimated direction of the reported comparison. It also conveys uncertainty: the point estimate is not known with exact precision, and the range includes a variety of effect sizes. The PFS median confidence intervals were 7.5 to 11.3 months for retifanlimab plus chemotherapy and 7.1 to 7.7 months for placebo plus chemotherapy.

As a general explanation, a confidence interval is generated by a statistical procedure that, over repeated use under its assumptions, has a stated coverage property. It is not a probability statement that the true value has a particular chance of lying in this already calculated interval. Wider intervals indicate less precision than narrower intervals, but interval width also depends on the outcome scale and analysis method. Precision alone does not determine clinical importance.

The OS hazard ratio was 0.75, with a 95% confidence interval from 0.55 to 1.01. That interval reaches slightly above 1, so it includes values on both sides of the no-difference reference for a hazard ratio. The registry also reports p = 0.030. The record does not explain the relationship between the reported interval and p-value, and both should be retained as reported rather than reconciled by assumption.

For response outcomes, the arm-specific intervals describe uncertainty in each estimated proportion, while the recalculated risk-difference intervals describe uncertainty in the unadjusted between-group contrast. The objective-response risk-difference interval runs from 0.006 to 0.228; the disease-control interval runs from -0.011 to 0.154. The latter includes zero. These are recalculated unadjusted intervals and are not the sponsor's adjusted comparison. The registry record does not provide enough detail to assess precision across every subgroup or alternative analysis.

12. 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 planning illustrations translate an assumed effect into a required amount of statistical information. For time-to-event outcomes, the entries are total events, using the Schoenfeld approach. For binary outcomes, the entries are participants per arm. They do not describe the number enrolled or analyzed in this completed trial.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The time-to-event planning values are based on total events; the binary-outcome values are based on participants per arm. The trial's original design assumptions and sample-size justification are not reported in the registry record, so these illustrations should not be taken as a reconstruction of the original protocol design.

The 80% power column gives the illustrative number of events or participants needed for an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column uses a higher target chance of detection and therefore requires more information under the same assumptions. These are design-planning concepts, not guarantees about a future study's result.

Rows that plan for a smaller fraction of the observed effect require more events or participants. Smaller effects are harder to distinguish from random variation, so more information is generally needed to detect them at the same significance and power targets. The values are planning illustrations based on the observed result, not observed power. Observed power is not a useful way to reinterpret the trial result after the data have been collected; the effect estimates and their uncertainty are more informative.

The illustrations also depend on their assumptions. Equal allocation, the normal approximation, and the assumed effect size may not match a future study's design or population. For time-to-event planning, an event target is not the same as an enrollment target because participants may have different follow-up and event experience. For binary planning, the per-arm figures are not totals across the study. Any intended use for a new design would require assumptions appropriate to that design, which are not specified in the registry record.

13. 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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.630, so ln(HR) = -0.4620.
2. d = 4 × (1.96 + 0.842)² / [ln(0.630)]² = 147.1, rounded up to 148 events in total 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
hr <- 0.63                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(4472429)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 148 (80% power), 197 (90% power)
 75% of observed effect: events = 262 (80% power), 351 (90% power)
 50% of observed effect: events = 589 (80% power), 788 (90% power)
Simulated power with 148 events: 0.814 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 231 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 308 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 7.4          # control-arm median, months (converted from the posted unit)
hr          <- 0.63          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis               Value Efficacy
   IA 1: 33%                   Z   3.7103
      N: 162         p (1-sided)   0.0001
  Events: 67        ~HR at bound   0.4012
   Month: 17    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.63   0.0338
   IA 2: 67%                   Z   2.5114
      N: 232         p (1-sided)   0.0060
 Events: 133        ~HR at bound   0.6459
   Month: 26    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.63   0.5603
       Final                   Z   1.9930
      N: 232         p (1-sided)   0.0231
 Events: 199        ~HR at bound   0.7533
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.63   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The sponsor's primary analysis reports a hazard ratio of 0.63 for retifanlimab plus chemotherapy versus placebo plus chemotherapy, with a 95% confidence interval from 0.47 to 0.84 and p < 0.001. The recorded method is a stratified log-rank test. This is the reported comparative analysis for the primary time-to-event endpoint; the posted median estimates are descriptive summaries of each group's PFS experience.

The posted secondary time-to-event analysis for overall survival also reports a sponsor hazard ratio and stratified log-rank p-value. Those are sponsor analyses, not recalculations from the arm medians. In this analysis, recalculated time-to-event comparisons are not used: the posted hazard ratios are the basis for the interpretation.

For objective response, the sponsor reports a Cochran-Mantel-Haenszel test with p = 0.013. The unadjusted recalculation from the posted summary statistics gives p = 0.04 for the risk difference. These analyses need not match because the recalculation is unadjusted and the sponsor method is a stratified test. The registry record does not identify the strata for that test. The registry record does not flag a discrepancy between sponsor results and recalculations.

For disease control rate, the registry record does not post a sponsor comparison. The displayed risk-difference calculation is unadjusted and should not be described as a sponsor analysis. Where a sponsor analysis is reported, it remains the appropriate reference for the trial's own inferential result; recalculations from summary statistics are supplementary descriptions, not replacements for the trial's analysis plan.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical conclusions are drawn from several endpoints, comparisons, subgroups, or repeated looks at accumulating data. As a general explanation, the more hypotheses tested, the greater the chance that at least one result appears statistically notable by chance if no adjustment or prespecified testing sequence is used. This matters especially for secondary outcomes, which include overall survival, response, disease control, and multiple adverse-event measures.

The registry record does not report a multiplicity adjustment, a hierarchical testing strategy, or another procedure controlling the overall type I error across secondary endpoints. It therefore does not establish that the secondary p-values were protected against the accumulation of tests. The primary PFS analysis is reported separately as the primary endpoint, but the available record does not provide the full prespecified testing hierarchy. Secondary findings should consequently be interpreted with more caution than the primary result.

The record identifies the Full Analysis Set for the primary endpoint as all randomized participants, analyzed according to assigned treatment and strata. It does not report detailed rules for missing outcome assessments, censoring, protocol deviations, or the treatment of participants with incomplete follow-up. Those procedures can affect time-to-event estimation and binary outcome denominators. The record does not provide enough information to evaluate whether missingness could have changed the estimates or how sensitivity analyses addressed it.

The original sample-size justification, planned power, and design assumptions are not reported in the registry record. Nor are interim analyses or stopping rules reported. The planning illustrations based on observed effects do not fill those gaps and should not be treated as evidence of the trial's original planning. These omissions constrain evaluation of the full statistical plan, but they do not change the interpretation of the sponsor's results as posted.

17. 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: urinary tract infection (3.3%), pulmonary embolism (3.2%), sepsis (3.2%), diarrhoea (2.6%), pneumonia (2.6%).

During the randomized period, the registry reports serious adverse events in 59 of 152 participants in the placebo-plus-chemotherapy group and 73 of 154 participants in the retifanlimab-plus-chemotherapy group. These counts are accompanied by the registry's at-risk denominators; they are not calculated percentages. The randomized-period total is recorded as 132 of 306. The record also lists participants with any treatment-emergent adverse event, but those broad counts should not be confused with serious events.

The registry's listed serious-event terms include urinary tract infection at 3.3%, pulmonary embolism at 3.2%, sepsis at 3.2%, diarrhoea at 2.6%, pneumonia at 2.6%, and abdominal pain at 2.6%. The posted list does not assign these term percentages to a particular treatment group in the details. They should therefore be read as listed event frequencies, not as direct between-group comparisons.

These safety summaries do not by themselves establish whether an event was caused by treatment or indicate its severity for an individual participant. The open-label monotherapy period is reported separately, and its figures should not be combined with randomized-period counts. The registry record does not provide a complete exposure-adjusted comparative safety analysis or detailed event-level context.

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

The primary result is a randomized comparison of PFS between two treatment strategies: retifanlimab plus carboplatin-paclitaxel and placebo plus carboplatin-paclitaxel. The sponsor's reported hazard ratio and confidence interval indicate that the estimated event hazard favored the retifanlimab group in this study population. The medians provide a familiar time scale for the estimated PFS distributions, while the hazard ratio summarizes the comparative time-to-event analysis.

This result does not mean that every participant experienced the same timing of progression or death, or that the median difference predicts the experience of an individual. It does not show the separate effect on progression and death because the primary endpoint combines them. Nor does it prove that the estimated hazard ratio remained constant over the full follow-up period; the registry record does not report an assessment of that assumption.

The study's eligibility description is specific: participants had inoperable locally recurrent or metastatic squamous cell carcinoma of the anal canal and had not previously received systemic chemotherapy. Statistical results from that population cannot automatically be generalized to people with different disease settings or treatment histories. The registry record also does not provide subgroup results that would establish how the effects varied across patient characteristics.

Secondary results add information but do not settle every question. Overall survival, response, disease control, and safety outcomes differ in definition and precision. The registry does not report a multiplicity procedure for secondary outcomes, and some sponsor comparisons are not posted. These limitations mean that secondary findings should not be interpreted as if each were an independently confirmed primary result.

Finally, statistical evidence is not the same as a complete clinical judgment. The posted efficacy estimates do not by themselves establish an overall benefit-harm balance, describe quality of life, or determine what treatment is appropriate for any person. The registry record is a source of trial design and posted outcomes; medical decisions require individual clinical assessment beyond these statistical summaries.

19. Why This Trial Matters Statistically

This study illustrates the role of a time-to-event endpoint in a randomized trial. PFS incorporates both the timing of documented progression and death, rather than relying only on a response assessment at a single visit. Its interpretation depends on endpoint definition, assessment procedures, follow-up, and survival-analysis methods. Here, the registry identifies RECIST v1.1, blinded independent central review, Kaplan-Meier estimation, and a stratified log-rank comparison, giving readers a defined framework for understanding the primary result.

It also shows why the effect estimate and its precision should be read together. The hazard ratio communicates a relative comparison, while median times and confidence intervals describe other aspects of the data. A p-value alone cannot convey the size or precision of an effect. The sponsor's reported time-to-event analysis is distinct from the unadjusted recalculations used for binary response summaries, which do not account for the sponsor's stratified method.

The registry record further highlights the importance of separating primary and secondary inference. Secondary endpoints can strengthen the clinical description by addressing survival, response, disease control, and safety, but multiple analyses require a stated multiplicity strategy if their p-values are to support confirmatory claims. Where that strategy is not reported, the primary outcome carries the clearest inferential role.

Finally, planning illustrations based on an observed effect are not a substitute for a prospective design justification. They show how assumed effect size and target power relate to required events or participants under stated assumptions. Keeping those planning quantities separate from observed trial results helps avoid confusing design scenarios with evidence about what the completed study achieved.

20. 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.

The registry record does not report the original sample-size justification, planned power, or complete design assumptions. The posted planning illustrations are based on observed effects and cannot establish what assumptions informed the trial's original design. Interim analyses and stopping rules are also not reported in the registry record.

The PFS definition is specific and centrally assessed, but detailed censoring rules, missing-assessment procedures, and sensitivity analyses are not reported. The registry identifies a Full Analysis Set and the assigned-treatment approach, but does not provide enough detail to evaluate the effects of incomplete follow-up or protocol deviations. The specific stratification factors used in the primary and secondary analyses are not reported in the details.

The OS result has a confidence interval reaching 1.01 while its reported p-value is 0.030. The record does not explain the relationship between these summaries, so this analysis does not resolve it. For binary endpoints, recalculated estimates are unadjusted; objective response has a sponsor-reported test, whereas no sponsor comparison is posted for disease control. Those differences limit direct comparison across endpoint analyses.

The registry does not report a multiplicity procedure for secondary outcomes, so their statistical evidence warrants caution. Safety summaries include event counts and selected event terms, but the available details do not provide a complete comparative account of exposure, event duration, severity, or causality. The posted results also do not establish treatment effects in subgroups or populations outside the eligibility description.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Carboplatin-paclitaxel With Retifanlimab or Placebo in Participants With Locally Advanced or Metastatic Squamous Cell Anal Carcinoma (POD1UM-303/InterAACT 2). — NCT04472429.
• Registry record last updated 2026-09-25; status last verified 2026-09.
• Results first posted 2025-05-23.
• 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.

24. Record Summary

NCT04472429 is a completed, phase 3 randomized, parallel-group study of retifanlimab plus carboplatin-paclitaxel versus placebo plus carboplatin-paclitaxel in participants with inoperable locally recurrent or metastatic squamous cell carcinoma of the anal canal who had not previously received systemic chemotherapy. The registry records quadruple masking and enrollment of 308.

The primary endpoint was PFS, defined as time from randomization to centrally reviewed RECIST v1.1 progression or death from any cause. The sponsor reported a stratified log-rank comparison with a hazard ratio of 0.63, a 95% confidence interval from 0.47 to 0.84, and p < 0.001. Secondary outcomes included overall survival, response, disease control, and treatment-emergent adverse events.

The registry record does not report the original sample-size justification, a complete statistical analysis plan, or a multiplicity procedure for secondary outcomes. Secondary findings and safety summaries therefore require interpretation in light of the methods and reporting limitations.