Trial of Nivolumab vs Therapy of Investigator's Choice in Recurrent or Metastatic Head and Neck Carcinoma (CheckMate 141): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Nivolumab vs Therapy of Investigator's Choice in Recurrent or Metastatic Head and Neck Carcinoma (CheckMate 141) (NCT02105636), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

This was an open-label randomized comparison, so the assigned treatments were not masked. The central statistical question is about the time-to-event outcome: how the observed survival distributions and the reported hazard ratio compare between the randomized arms. The registry record reports median overall survival and a hazard ratio with a confidence interval, along with a log-rank p-value. Those statistics describe the trial’s posted result; they do not by themselves establish how the result applies to people outside the trial population.

The trial also posted investigator-assessed progression-free survival and objective response rate as secondary outcomes. These outcomes address different aspects of the disease course than overall survival. They can add context, but they do not replace the prespecified primary question, and the registry record does not report whether any adjustment for multiple outcome testing was used.

3. Trial Design

CheckMate 141 (NCT02105636) was a phase 3, randomized, parallel-group, open-label clinical trial sponsored by Bristol-Myers Squibb. The registry lists enrollment of 361 and a completed status. The study started on 2014-05-29, and primary completion was recorded as 2015-11-06. Its official title describes a comparison of nivolumab with therapy of investigator’s choice in recurrent or metastatic platinum-refractory squamous cell carcinoma of the head and neck.

One arm received nivolumab 3mg/kg intravenously every 2 weeks until disease progression. The other arm allowed investigator’s choice among cetuximab, methotrexate, or docetaxel. The registry describes cetuximab as an intravenous solution, with a first dose of 400 mg/m2 followed by 250 mg/m2 weekly until disease progression. It describes methotrexate as an intravenous solution at 40 or 60 mg/m2 weekly until disease progression. The docetaxel description begins with 30 or 40 mg/m2 weekly, but the posted arm description is incomplete, so further dosing details are not reported in the registry record.

For the primary outcome, the posted analysis includes 240 participants in the nivolumab arm and 121 in the investigator’s choice arm. These are the analysis group sizes listed for overall survival, whose stated population is all randomized participants. The registry record does not report the rationale for the allocation proportions, the original sample-size justification, or the protocol’s planned statistical details beyond the posted endpoint and analyses.

The primary endpoint was overall survival, defined as time from randomization to death from any cause. The primary timeframe is described as up to approximately 18 months. The posted secondary outcomes were investigator-assessed progression-free survival and objective response rate; their timeframe descriptions extend to up to approximately 87 months. A longer listed timeframe does not by itself indicate how much follow-up was available for every participant.

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.

Pre-Treatment

Reasons for not completing this period:

Treatment

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 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.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over From date of randomization to date of death (Up to approximately 18 months).

Overall survival measures the time from randomization until death from any cause. In this trial, participants who were still known to be alive were censored at the date they were last known alive. Participants who were randomized but had no follow-up were censored at randomization. The registry states that median overall survival was calculated using the Kaplan-Meier method.

Overall survival is useful in a time-to-event comparison because it incorporates both the timing of events and the experience of participants who have not had an observed event by the end of their available follow-up. A median summarizes the estimated time by which half of the survival distribution has experienced the event, rather than describing the outcome for every participant. A hazard ratio offers a relative comparison of the event rates over follow-up, subject to the assumptions and interpretation of that measure.

Death from any cause is the event specified for this endpoint, rather than a cause-specific death category. This definition makes the endpoint distinct from progression-free survival, which counts disease progression or death, whichever occurs first. The posted primary outcome therefore addresses survival directly, while secondary outcomes provide information about progression and tumor response.

The endpoint’s stated timeframe is up to approximately 18 months. That wording does not mean that every participant was followed for that duration, and the registry record does not report participant-level follow-up distributions in the registry record presented. The event and censoring rules matter when interpreting the Kaplan-Meier median and its confidence interval, because estimates depend on the observed follow-up and censoring pattern.

7. Results Posted in the Registry

• Nivolumab 3mg/kg vs Investigators Choice: hazard ratio 0.70 (95% CI 0.53–0.92), reported p = 0.010 (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.

Investigator-Assessed Progression-Free Survival (PFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Nivolumab 3mg/kg vs Investigators Choice: hazard ratio 0.86 (95% CI 0.68–1.10) (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 Nivolumab 3mg/kg vs Investigators Choice and the control. The interval gives the range of effects that remain compatible with the data.

Investigator-Assessed 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:
  • Investigators Choice: 5.8% (7/121) versus 13.3% (32/240) on control; risk difference -7.5 percentage points (95% CI -13.5 to -1.6), risk ratio 0.43 (0.20–0.95); unadjusted two-proportion z-test p = 0.029.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Investigators Choice than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary endpoints broaden the clinical and statistical picture, but they do not all point to the same kind of measurement. Progression-free survival concerns time to progression or death, whereas objective response rate records whether a response was observed during the stated assessment period. These outcomes are related to disease course but are not equivalent to overall survival, the primary endpoint. Their results therefore add context rather than serving as direct replications of the primary survival comparison.

The posted progression-free survival comparison is less conclusive in its interval-based interpretation than the primary overall-survival comparison: its hazard-ratio confidence interval includes 1. The response outcome has a higher posted percentage in the nivolumab arm, but its estimates are based on a different endpoint and scale. This general pattern does not establish that one secondary endpoint confirms another; the questions, measurements, and statistical uncertainty differ.

Secondary analyses carry less confirmatory weight when the registry does not report whether multiplicity was addressed. Testing several outcomes can increase the chance that at least one appears statistically notable by chance. Adjustments or a prespecified testing hierarchy can manage that issue, but such procedures are not reported in the registry record. The response analyses also include more than one comparative measure, which reinforces the need to interpret each estimate in its stated context rather than select the most favorable result.

The primary endpoint remains the principal basis for evaluating the trial’s stated survival question. Secondary results can help describe other observed outcomes and identify questions for further study, but they should not be used to override the primary result or to claim broader certainty than the posted evidence supports. The registry does not report enough of the statistical plan to determine the intended confirmatory status of each secondary analysis.

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

• Investigator-Assessed Progression-Free Survival (PFS)
• Investigator-Assessed Objective Response Rate (ORR)

9. Statistical Interpretation

10. Statistical Methods Explained

Time-to-event outcomes require methods that account for when an event occurs and for participants whose event time is not observed during their available follow-up. In this trial, overall survival time began at randomization and ended at death from any cause. The registry specifies censoring at the last date known alive, or at randomization for participants with no follow-up. Censoring means that the event time is not observed after a participant’s last known status; it does not mean that the participant experienced the event at that time.

What does the Kaplan-Meier median represent?

The Kaplan-Meier method estimates the survival distribution while accounting for censored observations. The median is the time at which the estimated survival curve reaches the halfway point. It is an arm-specific summary, not a direct estimate of the comparative effect between arms. The posted medians should therefore be read alongside the hazard ratio and its confidence interval. The method relies on censoring being appropriately handled; the registry record does not report diagnostics or further detail about the censoring pattern.

How should the hazard ratio be read?

A hazard ratio compares event rates between groups over follow-up. The reported primary estimate is 0.70 for nivolumab versus investigator’s choice. A value of 1 corresponds to no relative difference in the hazard under this measure; values on either side indicate a lower or higher relative hazard for the numerator group, respectively. This is a general interpretation of hazard ratios, not a claim that the relative hazard is constant at every time. The registry reports a log-rank method for the primary analysis, but does not report further details about the model or proportional-hazards assessment. The analysis description also labels the result as a superiority analysis.

The confidence interval communicates uncertainty around the estimated hazard ratio. The reported 95% interval is 0.53 to 0.92. It is an interval for the comparative parameter under the analysis, not a range of individual outcomes. The p-value of 0.010 summarizes how compatible the observed data are with the null hypothesis under the reported test; it is not the probability that the null hypothesis is true, nor does it measure the clinical importance of the estimate.

Why can over-dispersion matter?

General statistical context: in count outcomes, over-dispersion means that variation is greater than a model assumes. Ignoring it can make uncertainty appear smaller than it is. The primary endpoint is a time-to-event outcome, and the registry does not report a count model for it. The posted methods information does not establish that over-dispersion was a concern or that a correction was used. It is therefore not appropriate to attribute a specific over-dispersion adjustment to this trial.

What do the secondary outcome methods add?

Progression-free survival is also a time-to-event endpoint, defined by progression or death, whichever occurs first. Its posted hazard ratio is 0.86, with a 95% confidence interval of 0.68 to 1.10. The registry does not state a method or p-value for that comparison. Objective response rate is a binary outcome reported as a percentage of participants, with arm-specific confidence intervals. The posted sponsor analyses also include a difference in response rates and a common odds ratio estimated by the CMH method. The record does not provide additional details about stratification variables or the specific adjustment strategy for that analysis.

A simple unadjusted recalculation from posted summary statistics is distinct from the sponsor’s full analysis. It can describe a basic contrast but cannot recreate unreported stratification, covariate adjustment, censoring methods, or other protocol-defined procedures. The primary comparison uses the sponsor’s reported hazard ratio and log-rank result, rather than a new estimate from summary data. For secondary outcomes, the posted sponsor estimates and the simpler recalculated contrasts should be understood according to their respective methods, not treated as interchangeable.

What can be inferred from the reported test?

The primary log-rank p-value evaluates the survival distributions under the test’s null hypothesis. A confidence interval and p-value address statistical uncertainty from different angles: the interval gives a range of parameter values compatible with the analysis, while the p-value measures evidence against the null under that analysis. Neither statistic provides a probability that a particular participant will experience an outcome, and neither substitutes for assessing design, follow-up, missing data, or generalizability.

The registry identifies the primary population as all randomized participants. It does not provide a full account of exclusions, treatment discontinuations, crossover, missing endpoint assessments, or sensitivity analyses. It also does not report whether interim analyses were planned or conducted, the original sample-size calculation, or the complete analysis plan. Those details are not reported in the registry record. The methods available support interpretation of the posted summary estimates, but not reconstruction of every analysis decision.

11. Confidence Intervals and Precision

The primary overall-survival hazard ratio is 0.70, with a 95% confidence interval from 0.53 to 0.92. This interval conveys uncertainty around the comparative estimate: the point estimate is not exact, and values across the interval remain compatible with the analysis at the stated confidence level. The interval lies below 1, the value corresponding to no relative difference under the hazard-ratio measure. It therefore aligns with the reported log-rank p-value of 0.010, while still allowing a range of possible effect sizes.

Confidence intervals are not ranges that contain a fixed fraction of participants’ outcomes. The arm-specific median overall survival estimates are 7.49 months and 5.06 months, with intervals of 5.49 to 9.1 months and 4.04 to 6.05 months, respectively. These intervals describe uncertainty in the estimated medians, not the spread of individual survival times. Overlap or lack of overlap between separate arm-specific intervals is not a substitute for the trial’s direct comparative analysis.

The secondary estimates have their own levels of precision. The progression-free survival hazard ratio is 0.86, with a 95% confidence interval of 0.68 to 1.10, which includes 1. The response percentages have arm-specific 95% confidence intervals of 9.3% to 18.3% and 2.4% to 11.6%. The registry also posts a response-rate difference and a common odds ratio, each with its own confidence interval. Different measures express comparisons on different scales, so their intervals should not be compared as if they estimated the same quantity.

Interval width reflects statistical uncertainty but does not by itself capture all limitations. Interpretation also depends on the analysis population, follow-up, censoring, outcome assessment, and the trial’s design. Several of those details are not reported in the registry record. The intervals support a careful reading of the posted estimates, rather than a claim of certainty about the true effect or about outcomes for individuals.

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 show the event counts or participant counts that would be needed under specified assumptions to detect a fraction of the observed effect. For the time-to-event outcomes, the figures are total events, not participants per arm. For objective response rate, the figures are participants per arm. The displayed planning scenarios use the observed effect, then consider 75% and 50% of that effect; those smaller effects require more information to detect.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect to detect is the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld method. The original trial’s own sample-size assumptions and justification are not reported in the registry record; these planning calculations are not a reconstruction of the trial’s design.

The 80% power column gives the illustrated total event count or participants per arm under which a study would have an 80% probability of detecting the assumed effect if that effect were the true one, under the listed assumptions. The 90% power column gives the corresponding planning quantity for a higher probability of detection. Greater power generally requires more information, and detecting a smaller effect requires more participants or events than detecting a larger one. These quantities are planning illustrations based on the observed estimates, not observed power.

For example, the overall-survival illustration lists 247 total events for planning at 100% of the observed effect and 80% power, and 331 total events for 90% power. For the response outcome, the corresponding 100%-effect illustrations are 238 participants per arm for 80% power and 317 participants per arm for 90% power. The additional rows show how those requirements rise when planning for 75% or 50% of the observed effect. These scenarios are sensitive to their assumptions and should not be read as proof that a future study will achieve the stated power.

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 = 0.700, so ln(HR) = -0.3567.
2. d = 4 × (1.96 + 0.842)² / [ln(0.700)]² = 246.8, rounded up to 247 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 <- 0.7                              # 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(2105636)
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 = 247 (80% power), 331 (90% power)
 75% of observed effect: events = 439 (80% power), 588 (90% power)
 50% of observed effect: events = 988 (80% power), 1,322 (90% power)
Simulated power with 247 events: 0.809 (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 365 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 361 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 <- 5.06          # control-arm median, months (converted from the posted unit)
hr          <- 0.7          # 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: 224        p (1-sided)   0.0001
 Events: 112       ~HR at bound   0.4947
   Month: 15   P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.7   0.0338
   IA 2: 67%                  Z   2.5114
      N: 358        p (1-sided)   0.0060
 Events: 223       ~HR at bound   0.7140
   Month: 24   P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.7   0.5603
       Final                  Z   1.9930
      N: 366        p (1-sided)   0.0231
 Events: 334       ~HR at bound   0.8039
   Month: 60   P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.7   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 reported primary analysis is a log-rank comparison with a hazard ratio of 0.70, a 95% confidence interval of 0.53 to 0.92, and p = 0.010. The posted arm-specific overall-survival medians are 7.49 months for nivolumab and 5.06 months for investigator’s choice. The sponsor’s reported hazard ratio is the appropriate comparative estimate to emphasize for the primary time-to-event outcome; a comparison of the two medians is not a substitute for that analysis.

The registry indicates no discrepancy between the reported primary analysis and the posted result. The sponsor’s own analysis therefore takes precedence over a simple recalculation from summary statistics. A recalculation using only arm-level summaries cannot reproduce the complete time-to-event analysis or any details not included in those summaries. In this case, the reported estimate and its stated method provide the primary inferential result.

For the secondary response outcome, the registry posts sponsor analyses of the difference in response rates and the CMH estimate of a common odds ratio. It also contains simple unadjusted recalculations based on summary counts. Those are different types of analysis and need not have identical estimates or uncertainty. The registry record does not report enough details to reconstruct every aspect of the sponsor’s secondary analyses, including any stratification details. The posted sponsor results should be interpreted as the trial’s reported analysis, while unadjusted recalculations remain descriptive checks rather than replacements for that analysis.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when multiple outcomes, comparisons, subgroups, or analyses are tested. If each is interpreted using an unadjusted significance threshold, the chance of a false-positive finding across the collection can increase. Statistical plans often address this through procedures such as adjustment, a testing hierarchy, or clear designation of exploratory analyses. These are general approaches; the registry record does not report which, if any, were used for this trial’s secondary outcomes.

The record lists investigator-assessed progression-free survival and objective response rate as secondary outcomes, and it posts analyses for both. It does not report a multiplicity adjustment or a prespecified hierarchy linking these outcomes to the primary endpoint. Consequently, the secondary findings should be interpreted with caution and should not be treated as having the same confirmatory status as the primary overall-survival analysis unless further protocol information establishes that status.

The primary analysis population is stated as all randomized participants. The record does not report detailed accounting of missing data, participant withdrawals, treatment discontinuations, crossover, or endpoint-specific analysis populations beyond the group counts shown for the outcomes. It also does not describe sensitivity analyses for missing or censored observations. For overall survival, the censoring rules are stated, but the registry does not provide further diagnostics about censoring or follow-up completeness.

The registry record also does not report the complete statistical analysis plan, interim-analysis procedures, subgroup analysis plan, or the original sample-size justification. These omissions limit the ability to assess whether all analyses followed prespecified procedures, how missing observations were handled beyond the endpoint definitions, and whether multiplicity was managed elsewhere in the protocol. Absence of these details in the registry record does not establish that the procedures were absent from the study; it means that they cannot be assessed from the record presented.

These uncertainties do not invalidate the reported primary comparison, but they define the limits of interpretation. The posted result can be described using its stated population, endpoint definition, method, and uncertainty interval. Claims about unreported analysis choices or about the behavior of missing data would go beyond what the registry record documents.

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: malignant neoplasm progression (49.5%), pneumonia (7.2%), dyspnoea (4.7%), pneumonia aspiration (4.2%), anaemia (3.6%).

The registry lists serious adverse events for each safety group, with 236 participants at risk in the nivolumab group and 111 at risk in the investigator choice group. Serious adverse events affected 165 and 87 participants, respectively. The figures for participants at risk differ from the primary outcome group counts, and the record does not explain the reason for that difference. These are safety summaries, not the primary efficacy analysis.

The most frequently listed serious event term is malignant neoplasm progression at 49.5%. Other listed terms are pneumonia at 7.2%, dyspnoea at 4.7%, pneumonia aspiration at 4.2%, anaemia at 3.6%, and pyrexia at 3.6%. The registry also reports other adverse events affecting 210 participants in the nivolumab group and 108 in the investigator choice group. It lists deaths for 220 and 119 participants, respectively. These death counts are reported in the safety data; the record does not identify them as treatment-caused deaths.

Event terms and participant counts do not, by themselves, establish causation or comparative risk. The registry record does not provide further detail about severity grading, exposure-adjusted rates, event timing, attribution, or how the listed percentages were calculated. The safety figures should therefore be read as descriptive summaries with those limits, not as a basis for inferring that treatment caused a particular event or that the arms differ in safety.

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

The posted data show that the sponsor’s primary analysis estimated a hazard ratio of 0.70 for overall survival, comparing nivolumab with investigator’s choice. Its 95% confidence interval is 0.53 to 0.92, and the reported log-rank p-value is 0.010. The arm-specific median estimates are 7.49 months and 5.06 months. Taken together, these are the trial’s reported statistical findings for the primary endpoint in the randomized population.

This result does not mean that every participant in one arm lived longer than every participant in the other arm, or that an individual’s outcome can be predicted from the group estimate. A median is a summary of a survival distribution, and a hazard ratio is a relative comparison over follow-up. Both are population-level measures. The confidence interval also makes clear that the estimated comparative effect has uncertainty.

The result does not resolve every question about treatment choice, safety, quality of life, or effects in populations not represented by the trial. The registry record identifies recurrent or metastatic platinum-refractory squamous cell carcinoma of the head and neck; conclusions should remain tied to that trial context. It does not provide all details needed to evaluate every subgroup, analysis assumption, or missing-data issue.

The secondary endpoints do not change the definition of the primary result. Progression-free survival and objective response address different outcomes, and the record does not report whether multiplicity was adjusted. Their estimates can add context, but should not be treated as independent confirmation of the primary finding. Similarly, the listed adverse-event summaries describe observed safety data but do not establish the cause of individual events.

Statistical evidence and clinical meaning are related but distinct. The reported p-value is not the probability that the null hypothesis is true, and statistical significance does not by itself measure the importance of an effect. The posted estimates, their intervals, the trial population, and the limits of the registry information all matter to a balanced interpretation. The data support describing the reported randomized comparison; they do not justify an unqualified claim about outcomes beyond the evidence recorded.

19. Why This Trial Matters Statistically

This trial is statistically notable for its clear primary time-to-event question and a reported comparative analysis rather than relying only on arm-specific summaries. Overall survival was defined from randomization to death from any cause, and the registry identifies the analysis population as all randomized participants. The sponsor reports a log-rank hazard ratio with a confidence interval and p-value, giving readers a direct estimate of the primary comparison alongside the Kaplan-Meier medians.

It also illustrates why endpoint choice matters. The primary endpoint measures survival, while progression-free survival combines progression and death and objective response measures a different clinical event. A result on one scale does not automatically predict the result on another. The secondary findings are informative context, but their statistical weight depends in part on the analysis plan and multiplicity procedures, which are not reported in the registry record.

The planning illustrations provide a separate statistical lesson: sample-size requirements depend on the effect a study aims to detect and the desired probability of detection under specified assumptions. Smaller effects require more information. Those illustrations use stated generic planning assumptions and the observed effects; they do not reveal the trial’s original design justification or show that the observed study had a particular power.

Finally, the record shows the value and limits of registry reporting. It supplies endpoint definitions, group estimates, confidence intervals, and selected adverse-event summaries, but leaves several analysis details unreported. Careful interpretation distinguishes the sponsor’s reported result from a simple recalculation and distinguishes descriptive safety counts from evidence of causation. This approach makes the statistical evidence useful without overstating what the record can establish.

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 complete statistical analysis plan, the original sample-size justification, or interim-analysis procedures. It also does not describe whether multiplicity was controlled for secondary outcomes, how secondary outcomes were prioritized, or whether subgroup analyses were prespecified. These omissions limit evaluation of the confirmatory status of analyses beyond the primary endpoint.

Although the primary endpoint definition includes censoring rules and the primary population is identified as all randomized participants, the record does not report detailed follow-up distributions, event counts, censoring diagnostics, or sensitivity analyses. The primary timeframe is stated as up to approximately 18 months, while secondary timeframes are stated as up to approximately 87 months. These descriptions do not establish that each participant had the same length of follow-up.

The study was open-label, and progression-free survival and response were investigator-assessed. The record does not provide enough information to assess how knowledge of treatment assignment may have affected those assessments or whether independent review was used. For the investigator’s choice arm, the registry lists several possible therapies, but does not provide complete details of how the choice was made or how many participants received each option. The docetaxel arm description is incomplete.

Safety summaries are limited to the counts and event terms posted. The registry record does not report the attribution, timing, exposure-adjusted rates, or complete detail needed to make causal comparisons from those summaries. These limitations call for restraint in interpreting secondary and safety findings, while the primary result can still be described according to its posted analysis and confidence interval.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Trial of Nivolumab vs Therapy of Investigator's Choice in Recurrent or Metastatic Head and Neck Carcinoma (CheckMate 141) — NCT02105636.
• Registry record last updated 2022-10-05; status last verified 2022-08.
• Results first posted 2017-01-11.
• 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

CheckMate 141 (NCT02105636) was a completed, randomized, open-label, parallel-group phase 3 trial sponsored by Bristol-Myers Squibb. It compared nivolumab with investigator’s choice of cetuximab, methotrexate, or docetaxel in recurrent or metastatic platinum-refractory squamous cell carcinoma of the head and neck. The registry lists enrollment of 361.

The primary endpoint was overall survival among all randomized participants. The sponsor reported a log-rank hazard ratio of 0.70, with a 95% confidence interval of 0.53 to 0.92 and p = 0.010. Median overall survival was 7.49 months for nivolumab and 5.06 months for investigator’s choice. Secondary outcomes were investigator-assessed progression-free survival and objective response rate.

Interpretation is limited by analysis details not reported in the registry record, including the complete statistical plan, multiplicity procedures, and original sample-size justification. The posted findings describe the randomized comparison and its uncertainty; they do not establish effects beyond the trial context or causation for the listed adverse events.