Study of Nivolumab Combined With Ipilimumab Versus Pemetrexed and Cisplatin or Carboplatin as First Line Therapy in Unresectable Pleural Mesothelioma Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Nivolumab Combined With Ipilimumab Versus Pemetrexed and Cisplatin or Carboplatin as First Line Therapy in Unresectable Pleural Mesothelioma Patients (NCT02899299), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This was a phase III randomized, open-label, parallel-group trial. The registry record reports enrollment of 605 and a completed status. The listed start date is 2016-11-29, and the primary completion date is 2020-03-25. These record dates describe the trial record; they do not, by themselves, provide information about the timing of individual analyses or the completeness of follow-up for each participant.

The two strategies were nivolumab plus ipilimumab and pemetrexed with cisplatin or carboplatin, used as first-line treatment for unresectable pleural mesothelioma. The registry describes the treatment schedules only as specified doses on specified days. Details such as the exact dosing schedule, treatment duration, dose modifications, and criteria for selecting cisplatin or carboplatin are not reported in the registry record.

There was no masking. In an open-label trial, participants and clinical teams know the assigned treatment. This can matter more for outcomes involving clinical judgment or reporting than for death, which is the primary endpoint. Randomization helps balance measured and unmeasured characteristics between groups on average, but the registry information does not give the allocation ratio, randomization procedure, stratification variables, or concealment details. Those design details are not reported in the registry record.

The primary analysis population is described as all randomized participants. The primary endpoint was overall survival, and the reported comparison used a stratified log-rank method. The registry does not state which factors were used for stratification. It lists objective response rate, disease control rate, progression-free survival, and outcomes by PD-L1 expression among secondary outcomes. Details of the full analysis plan, including analysis populations for each outcome, are not reported in the registry record.

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 randomization to the date of death (Up to 40 Months).

Overall survival measures the time from randomization until death from any cause. A participant who had not died was censored at the last known date alive. The registry states that the primary outcome was assessed from randomization to death, up to 40 Months. Censoring allows participants without an observed death by their last known follow-up to contribute information up to that point, rather than treating their follow-up as if death had occurred.

Overall survival is a time-to-event endpoint. It incorporates both whether deaths were observed and how long participants were followed before death or censoring. The reported median is a time point in the estimated survival distribution: it describes when the estimated proportion surviving has reached the midpoint. It is not the average survival time, and it does not describe the survival experience of every participant.

A hazard ratio compares the event rates over follow-up between groups under the analysis method. It is not a ratio of the two reported medians and does not directly state how many months an individual participant might gain or lose. The registry reports a hazard ratio for Treatment A versus Treatment B, alongside a confidence interval and a stratified log-rank p-value. The treatment labels attached to this comparison are not explicitly connected to named regimens in the posted outcome results.

Overall survival is used because death from any cause is a direct, clinically important event and does not require judgments about whether a tumor has progressed. Its interpretation still depends on follow-up, censoring, and the analysis assumptions. The registry does not report additional details about censoring rules, follow-up completeness, or checks of those assumptions.

7. Results Posted in the Registry

• Treatment A vs Treatment B: hazard ratio 0.74 (95% CI 0.60–0.91), reported p = 0.002 (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.

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:
  • Treatment B: 44.4% (134/302) versus 39.3% (119/303) on control; risk difference 5.1 percentage points (95% CI -2.8 to 12.9), risk ratio 1.13 (0.94–1.36); unadjusted two-proportion z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment B and the control. The interval gives the range of effects that remain compatible with the data.

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:
  • Treatment B: 85.8% (259/302) versus 76.6% (232/303) on control; risk difference 9.2 percentage points (95% CI 3.0 to 15.4), risk ratio 1.12 (1.04–1.21); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Treatment B than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

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:
  • Treatment A vs Treatment B: hazard ratio 0.93 (95% CI 0.77–1.13) (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 Treatment A vs Treatment B and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide a broader view of tumor response and disease control, alongside progression-free survival and outcomes analyzed by PD-L1 expression. Across the overall secondary results with numerical estimates, the direction is not uniform: the response and disease-control percentages are higher for Treatment B, while the progression-free survival medians and hazard-ratio estimate are close between groups. The primary overall-survival comparison, by contrast, favors Treatment A in the reported analysis. This difference in patterns means the secondary outcomes do not simply reproduce the primary result.

Each endpoint captures a different aspect of disease course. Response is based on observed tumor response, disease control includes a broader outcome category, and progression-free survival combines progression or death. Overall survival measures death from any cause. Their definitions, timing, and sensitivity to assessment procedures differ, so results need not align exactly. The registry describes the secondary assessment windows, but does not provide enough detail to evaluate all assessment procedures or the timing of each secondary analysis.

Unadjusted secondary findings carry less weight because several outcomes are examined, increasing the possibility that some comparisons appear noteworthy by chance. The multiplicity plan is not reported in the registry record. In addition, the binary endpoint comparisons are unadjusted recalculations rather than posted sponsor analyses. Their p-values should therefore be read as exploratory descriptions of the posted summaries, not as definitive confirmation of a treatment effect.

The registry lists results according to PD-L1 expression level for some outcomes, but the subgroup estimates and details are not reported in the registry record. No conclusion about consistency across PD-L1 groups can be drawn from the overall outcomes alone. In general, subgroup findings require caution because they can be less precise and because interpretation depends on prespecified hypotheses and multiplicity handling. Those elements are not reported for these outcomes.

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

• Objective Response Rate (ORR)
• Disease Control Rate (DCR)
• Progression Free Survival (PFS)
• Overall Survival (OS) According to PD-L1 Expression Level
• Progression Free Survival (PFS) According to PD-L1 Expression Level
• Objective Response Rate (ORR) According to PD-L1 Expression Level

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is analyzed as a time-to-event measure. In this setting, a participant contributes follow-up from randomization until death or censoring. Censoring occurs when a participant has not died by the last known date alive. It does not mean that the participant died at that time; it means that later survival time is not observed in the analysis record.

What does the hazard ratio describe?

The registry reports a hazard ratio of 0.74 for Treatment A versus Treatment B. A hazard ratio compares the event rates between groups over follow-up, rather than comparing only the median survival times. Under the usual interpretation, a value below the no-difference value points toward a lower event rate in the numerator group over the period represented by the model. This is a group-level summary. It does not mean that each participant’s risk is reduced by the same amount, and it is not a direct conversion into extra survival time.

The hazard-ratio interpretation is most straightforward when the relative event rates are reasonably stable over time. The registry record does not report whether that assumption was examined or whether the pattern of hazards changed during follow-up. The posted median survival values remain useful descriptive summaries, but they cannot establish the shape of the full survival curves on their own.

What does the stratified log-rank analysis do?

The registry identifies the primary comparison method as a stratified log-rank test. A log-rank analysis compares the timing of events across groups while using the follow-up information from participants who have events or are censored. Stratification allows comparisons to be made within specified strata and then combined. Which factors defined the strata is not reported in the registry record. The record also does not report the detailed model specification or whether any additional covariate adjustments were used.

The reported primary p-value is 0.002. A p-value describes how compatible the observed data are with a statistical null hypothesis under the test’s assumptions; it is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of the result. The hazard ratio and its confidence interval communicate the estimated direction and precision of the relative comparison, while the p-value addresses evidence against the null in the specified test.

How should the secondary comparisons be understood?

Objective response rate and disease control rate are binary outcomes: each participant is classified according to whether the defined outcome occurred. The registry reports percentages with confidence intervals for each treatment group. Simple unadjusted comparisons of those posted summary results are distinct from the sponsor’s analysis. The registry record does not include sponsor-reported analyses for these two outcomes. The unadjusted p-values therefore should not be mistaken for results from a reported, fully specified sponsor analysis.

Progression-free survival is another time-to-event outcome, defined as time from randomization to documented tumor progression or death from any cause, whichever occurs first. The registry reports medians and a hazard ratio, but does not report a p-value or method for that comparison. A missing p-value should not be inferred from the confidence interval or reconstructed as if it were an official result.

The registry lists secondary outcomes by PD-L1 expression level as well as overall response, disease control, progression-free survival, and overall survival. The subgroup results and their analysis details are not reported in the registry record. Subgroup comparisons generally have less information than overall comparisons and can be sensitive to how subgroup boundaries and tests are specified. Those issues cannot be assessed from the posted details.

Why does over-dispersion matter?

For a binary endpoint, a simple planning calculation typically relies on assumptions about how much variation is expected in the outcome. Over-dispersion means that the data vary more than the simple model anticipates, for example because outcomes are more heterogeneous than assumed. If over-dispersion is present but ignored, standard errors can be too small and confidence intervals too narrow. The registry record does not report whether over-dispersion was assessed or relevant to the analyses. This is a general statistical consideration, not a claim about this trial.

More broadly, interpretation depends on the prespecified endpoint definitions, handling of missing information, censoring rules, analysis populations, and multiplicity plan. Some endpoint definitions and the primary population are stated, but several of these implementation details are not reported in the registry record. The results can be described as posted; the absent details limit independent assessment of the complete analysis strategy.

11. Confidence Intervals and Precision

The confidence intervals communicate uncertainty around the estimates. For overall survival, the registry reports a 95% confidence interval of 16.82 to 21.45 months for Treatment A and 12.45 to 16.23 months for Treatment B. The primary hazard-ratio comparison is reported as 0.74, with limits of 0.60 and 0.91 in the sponsor analysis. The reported analysis identifies the interval as 96.6%, whereas the primary outcome description states 95% confidence intervals for the arm medians. These are different reported interval levels and should not be silently treated as identical.

A confidence interval is a range of values compatible with the data under the statistical procedure and its assumptions. It is not a guarantee that the true value lies within the particular interval, nor does it describe the range of individual participant outcomes. A narrower interval generally indicates greater precision for the estimate; a wider interval indicates more uncertainty. Precision is separate from whether an estimate is clinically important.

The median progression-free survival estimates have 95% confidence intervals of 5.59 to 7.36 months for Treatment A and 6.93 to 8.05 months for Treatment B. The reported hazard-ratio interval is 0.77 to 1.13. This interval extends across values on either side of the no-relative-hazard reference, so it does not precisely establish a direction for the relative comparison. The registry does not report a p-value for this endpoint.

For response and disease control, confidence intervals around each group percentage show uncertainty in those proportions. Their interpretation is not interchangeable with a confidence interval for a between-group contrast. The posted unadjusted risk-difference intervals address that contrast directly, but they do not account for unreported adjustments or multiplicity. All interval interpretations depend on the analysis assumptions and the amount of information available.

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 figures are illustrations based on the observed effect, not a record of the trial’s original sample-size justification. For time-to-event outcomes, the figures represent total events required. For the other outcomes, they represent participants per arm. The 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 the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column describes the planning number of events or participants that would give an 80% probability of detecting the stated effect under those assumptions, if the assumed effect and model were correct. The 90% power column uses a higher target probability of detection and therefore requires more information. These are planning probabilities under a hypothetical design, not probabilities that the observed trial result is correct. This is not observed power.

The entries for 100% of the observed effect use the full estimated effect as the planning target. The entries for 75% and 50% of the observed effect represent progressively smaller effects to detect. Smaller effects are harder to distinguish from random variation, so the planning requirement rises as the effect target becomes smaller. For example, the primary time-to-event planning figures are total events, while response and disease-control planning figures are participants per arm; the units matter when interpreting any entry.

These calculations use the observed effect as a starting point, which is itself uncertain. They should not be read as a recommendation for a future study or as evidence that the trial was planned around these values. The registry does not report the original sample-size justification, the assumptions used in it, or an original target number of events. The illustrations are useful for understanding how the required information changes with the target effect and power, but they cannot substitute for those missing design details.

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 = 0.740, so ln(HR) = -0.3011.
2. d = 4 × (1.96 + 0.842)² / [ln(0.740)]² = 346.3, rounded up to 347 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 <- 0.74                              # 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(2899299)
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 = 347 (80% power), 464 (90% power)
 75% of observed effect: events = 616 (80% power), 825 (90% power)
 50% of observed effect: events = 1,386 (80% power), 1,855 (90% power)
Simulated power with 347 events: 0.802 (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 635 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 605 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 <- 14.09          # control-arm median, months (converted from the posted unit)
hr          <- 0.74          # 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: 516         p (1-sided)   0.0001
 Events: 156        ~HR at bound   0.5520
   Month: 19    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.74   0.0338
   IA 2: 67%                   Z   2.5114
      N: 636         p (1-sided)   0.0060
 Events: 312        ~HR at bound   0.7524
   Month: 31    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.74   0.5603
       Final                   Z   1.9930
      N: 636         p (1-sided)   0.0231
 Events: 468        ~HR at bound   0.8317
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.74   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-reported primary analysis gives a hazard ratio of 0.74 for Treatment A versus Treatment B, with a confidence interval from 0.60 to 0.91, and p = 0.002 using a stratified log-rank analysis. The posted arm medians are 18.07 months and 14.09 months, with 95% confidence intervals reported separately for each arm. The sponsor’s result is the primary source for the trial’s inferential comparison; the medians are descriptive summaries and are not a replacement for that analysis.

The registry record does not flag a discrepancy between the sponsor analysis and the recalculated material. For the primary time-to-event endpoint, the posted interpretation uses the sponsor-reported hazard ratio rather than constructing a new estimate from the medians. That distinction matters because a hazard ratio cannot be recovered by subtracting or dividing the reported medians.

For binary secondary outcomes, simple unadjusted calculations based on the posted group summaries are not sponsor-reported analyses. The record lists no sponsor-reported analyses for objective response rate or disease control rate. Those calculations can help describe the raw group contrast, but they do not supersede a sponsor analysis and should not be presented as if they were prespecified or adjusted results. The sponsor’s own analysis takes precedence if a discrepancy is identified; no such discrepancy is flagged in the registry record.

The record does not report a sponsor p-value for progression-free survival. Its posted hazard ratio and confidence interval can be described, but additional inferential details should not be inferred or reconstructed as though they were sponsor findings.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when a trial evaluates several endpoints, subgroup comparisons, or statistical contrasts. The more opportunities there are to observe an apparently unusual result, the greater the chance that at least one finding could occur by chance even if there were no underlying effect for that comparison. A prespecified plan can control or otherwise account for this issue, but the registry record does not report a multiplicity strategy for the secondary outcomes or subgroup analyses.

The primary endpoint is identified as overall survival, and its sponsor-reported comparison is available. The registry also lists objective response rate, disease control rate, progression-free survival, and outcomes by PD-L1 expression level. It reports six secondary outcomes in total, but the statistical hierarchy among them, any adjustment procedure, and the status of subgroup testing are not reported in the registry record. Consequently, secondary p-values should not be interpreted as though their family-wise error or false discovery risk had been controlled.

The primary analysis population is described as all randomized participants. For overall survival, a participant not known to have died is censored at the last known date alive. The registry does not report further details about missing data, loss to follow-up, sensitivity analyses, or how participants with missing endpoint assessments were handled for the binary outcomes. It also does not report whether any participants were excluded from particular analyses or how analysis populations for the secondary endpoints were defined.

For time-to-event outcomes, censoring is informative only under assumptions about the relationship between censoring and the event process. The registry provides the basic censoring definition for overall survival, but not enough detail to assess those assumptions or follow-up completeness. For response and disease control, missing assessments can affect the estimated proportions, but the registry entries do not specify the missing-outcome rules. These are limitations in the information available for independent statistical appraisal, not evidence that a particular handling method was used.

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 (17.0%), pyrexia (5.3%), pneumonia (4.7%), anaemia (3.2%), colitis (3.0%).

The safety summary reports serious adverse events for groups titled Nivolumab 3mg/kg Plus Ipilimumab 1mg/kg and Pemetrexed Plus Cisplatin or Carboplatin. Among those at risk for serious adverse events, 188 of 300 were reported as affected in the nivolumab-plus-ipilimumab group, and 106 of 284 in the chemotherapy group. The registry lists malignant neoplasm progression at 17.0%, pyrexia at 5.3%, pneumonia at 4.7%, anaemia at 3.2%, colitis at 3.0%, and dyspnoea at 3.0% among the most frequent serious terms.

These figures describe reported serious adverse events in the registry record. They do not, by themselves, indicate whether each event was caused by treatment, how long participants were at risk, or how event severity and duration compared. The group denominators listed for serious events differ from the denominators listed for other adverse events. The record does not provide the reason for this difference in the summarized information.

The counts should not be interpreted as a complete safety comparison or as a measure of overall benefit and harm. The record also lists deaths in each group, but the safety summary does not establish that those deaths were treatment-related. Detailed definitions, exposure-adjusted rates, timing, and attribution procedures are not reported in the registry record.

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

The registry’s primary analysis reports a statistically significant overall-survival comparison favoring Treatment A over Treatment B: the hazard ratio is 0.74, with a confidence interval from 0.60 to 0.91 and p = 0.002. The arm-specific median estimates are 18.07 months and 14.09 months. These results describe the randomized groups under the reported analysis. The labels Treatment A and Treatment B are not explicitly mapped to named regimens in the outcome results, so the outcome comparison should not be assigned to a named regimen without additional documentation.

The result does not mean that every participant in one group survived longer than every participant in the other. Group medians and a hazard ratio summarize distributions across participants; individual outcomes vary. Nor does the hazard ratio state a specific number of months gained. The confidence interval expresses uncertainty in the relative estimate under the analysis assumptions, and does not describe a range of effects for individual patients.

The primary result also does not settle all questions about treatment response, disease control, progression-free survival, safety, or outcomes within subgroups. Those outcomes measure different features and have their own uncertainties. Secondary comparisons are less definitive where the analysis plan and multiplicity adjustments are not reported. Safety figures likewise describe reported events, but do not by themselves establish treatment causation or quantify a net balance of benefit and harm.

The registry record does not report enough detail to reconstruct the complete protocol or statistical analysis plan. Information about allocation procedures, stratification factors, missing-data handling, multiplicity, and subgroup methods is not reported in the registry record. Those gaps limit what can be concluded about all aspects of the trial, even though the primary sponsor-reported comparison is available. The posted data are statistical evidence about group outcomes, not medical advice and not a prediction for an individual.

19. Why This Trial Matters Statistically

This trial is statistically notable because it has a time-to-event primary endpoint and reports both arm-specific median survival estimates and a sponsor-reported hazard ratio. These summaries answer related but different questions. The medians describe points in each group’s estimated survival distribution, while the hazard ratio compares event rates across follow-up. Reading both avoids reducing the result to a single number or treating a relative comparison as a direct difference in months.

The open-label design is also relevant to interpretation. Knowledge of assigned treatment can affect care processes, reporting, or the assessment of outcomes that require judgment. Overall survival is less dependent on subjective outcome classification than response or progression, though follow-up and censoring still matter. Randomization supports a comparative interpretation, but the registry record does not include all details needed to evaluate the allocation process or analysis choices.

The secondary results illustrate why endpoint hierarchy and multiplicity matter. Outcomes can differ in direction because they measure distinct aspects of disease, and testing several endpoints raises the importance of prespecified interpretation. The registry provides a primary comparison but does not report a multiplicity plan for the secondary outcomes. Distinguishing sponsor-reported analyses from unadjusted recalculations also helps prevent descriptive comparisons from being mistaken for the trial’s formal inferential results.

Finally, the planning illustrations show how assumptions about effect size and desired power influence required information. They are not the trial’s original design rationale. Keeping those illustrations separate from observed results avoids confusing hypothetical planning performance with evidence generated by the randomized comparison. The record’s limits on analysis details are therefore part of the statistical interpretation, not merely administrative omissions.

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 outcome results use generic labels Treatment A and Treatment B, while the safety groups are identified by regimen. The registry record summarized for these results does not explicitly map the outcome labels to the named treatment regimens. This limits direct interpretation of which named regimen corresponds to the reported primary hazard ratio and secondary arm estimates.

The primary endpoint description states that overall survival was assessed up to 40 Months, while secondary outcome descriptions include assessment windows up to 76 months. The registry does not provide detailed follow-up distributions or explain the relationship between these windows. The available summary therefore does not allow a full assessment of maturity of follow-up or whether the analysis included all planned follow-up information.

Several design and analysis details are not reported in the registry record: the original sample-size justification, randomization and allocation procedures, stratification variables, detailed statistical plan, multiplicity strategy, and methods for missing data and secondary analysis populations. The record also does not report a p-value for progression-free survival or sponsor analyses for the binary secondary outcomes. The subgroup results by PD-L1 expression are not reported in the registry record.

The safety summary is limited to serious adverse events and selected frequent serious terms. The summarized information does not provide exposure-adjusted rates, full event listings, attribution, duration, or timing. Counts of affected participants should not be treated as a causal comparison without those details. These limitations do not negate the posted primary result, but they restrict how fully the whole trial can be independently evaluated from the registry information alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of Nivolumab Combined With Ipilimumab Versus Pemetrexed and Cisplatin or Carboplatin as First Line Therapy in Unresectable Pleural Mesothelioma Patients — NCT02899299.
• Registry record last updated 2024-05-21; status last verified 2024-04.
• Results first posted 2021-04-14.
• 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

The registry record describes a completed, randomized, open-label, phase III parallel-group trial of first-line treatment for unresectable pleural mesothelioma. The stated comparison is nivolumab plus ipilimumab versus pemetrexed with cisplatin or carboplatin. Enrollment was 605. The primary endpoint was overall survival among all randomized participants, defined from randomization to death from any cause, with censoring at last known date alive for those not known to have died.

The sponsor-reported primary analysis gives a hazard ratio of 0.74 for Treatment A versus Treatment B, with a confidence interval from 0.60 to 0.91 and p = 0.002 by stratified log-rank analysis. The posted outcome labels are not explicitly mapped to named regimens. Secondary outcomes include response, disease control, progression-free survival, and measures by PD-L1 expression. Important details about multiplicity, missing data, and the original design assumptions are not reported in the registry record.