Study of Durvalumab With Tremelimumab Versus SoC as 1st Line Therapy in Metastatic Non Small-Cell Lung Cancer (NSCLC) (NEPTUNE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Durvalumab With Tremelimumab Versus SoC as 1st Line Therapy in Metastatic Non Small-Cell Lung Cancer (NSCLC) (NEPTUNE) (NCT02542293), a randomized phase 3 study. The primary outcome is Overall Survival (OS); Global Cohort: Blood Tumor Mutational Burden (bTMB) ≥20 Mutations Per Megabase (Mut/Mb) Analysis Set.

2. Clinical Question

The primary endpoint is time-to-event: it concerns how long participants remained alive after randomization, while accounting for participants whose survival time was censored at analysis. The focus on a biomarker-defined subset means this result addresses a narrower question than the overall trial enrollment alone might suggest. Other registry outcomes examine survival, progression-free survival, response, and duration of response across additional biomarker and cohort groups. Their results are not part of the primary comparison.

3. Trial Design

This was a Phase III randomized, open-label, parallel-group, multicenter, global study of durvalumab combined with tremelimumab versus platinum-based standard-of-care chemotherapy for first-line treatment of advanced or metastatic NSCLC. The registry lists enrollment of 953 and describes participants as having EGFR and ALK wild-type disease. The study began on 2015-11-03, and primary completion was recorded as 2020-09-21. Its status is active, not recruiting.

Random allocation assigns participants to treatment groups by chance, which is intended to make groups comparable on average at the start of a trial. It does not ensure that every measured or unmeasured characteristic is balanced in a particular subset. The endpoint result is restricted to the global-cohort bTMB at-least-20 Mut/Mb analysis set, rather than the entire enrollment. The primary analysis set included 69 participants assigned to durvalumab plus tremelimumab and 60 assigned to standard-of-care chemotherapy.

The trial was open-label, meaning treatment assignment was not masked to participants or investigators. The registry record does not report further details about how outcome assessment or other trial procedures addressed the lack of masking. For overall survival, the endpoint is death from any cause, an event that is less dependent on subjective assessment than outcomes such as symptom scoring. Nonetheless, open-label status remains relevant context when considering the trial as a whole.

The chemotherapy arm could include several platinum-based regimens: paclitaxel plus carboplatin, gemcitabine plus cisplatin, gemcitabine plus carboplatin, pemetrexed plus cisplatin, or pemetrexed plus carboplatin. The registry describes these as standard-of-care options, not as a single uniform drug combination. The record does not report the original design assumptions or the rationale for selecting the primary biomarker-defined analysis set.

The registry lists additional analyses by blood or tissue tumor mutational burden, PD-L1 status, and global or China cohort. It reports 20 outcome measures and 61 analyses. The primary finding should therefore be read as one specified analysis within a broader program of comparisons, rather than as a summary of every outcome or subgroup in the trial.

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: 823 participants in Global cohort and 160 participants in China cohort were randomized in 1:1 ratio to receive durvalumab + tremelimumab or SoC chemotherapy. China cohort comprised participants from mainland China (30 from Global cohort and 130 randomized after end of Global cohort recruitment). Thus, 953 unique participants were randomized in the study overall. Participants included in both cohorts for Started, Completed and Reasons for Not Completed are not double-counted for participant flow.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The bTMB ≥20 mut/Mb analysis set included the subset of participants in the FAS whose blood TMB status was ≥20 mut/Mb at baseline as defined by the GuardantOMNI CDx assay. Only participants randomized in Global cohort were analyzed as bTMB and tissue tumor mutational burden (tTMB) testing was not performed in China cohort.

5. Baseline Characteristics

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

Population: Global Cohort: The full analysis set (FAS) included all randomized participants prior to the end of global recruitment. Any participants recruited in China, after global recruitment had ended, were not included in the FAS. China Cohort: The China FAS included all randomized participants in the China cohort and were used for all China only efficacy analyses. Participants included in both cohorts are not double-counted for the baseline characteristics analysis represented by 'All participants'.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS); Global Cohort: Blood Tumor Mutational Burden (bTMB) ≥20 Mutations Per Megabase (Mut/Mb) Analysis Set, measured over From baseline (Day 1, Week 0) until death due to any cause, assessed up to the Global cohort DCO date (a maximum of approximately 44 months)..

Overall survival (OS) measures the time from randomization until death from any cause. In the registry definition, a participant’s OS time ends at death or is censored using the last recorded date on which the participant was known to be alive. The endpoint is assessed from baseline, Day 1, Week 0, through the global-cohort data cut-off, with follow-up described as a maximum of approximately 44 months. Median OS is estimated using the Kaplan-Meier technique.

Time-to-event outcomes are useful when participants have different follow-up durations or when some are still alive at the time the data are analyzed. Censoring allows their observed follow-up to contribute information up to the last date they were known to be alive, without treating that date as a death. The Kaplan-Meier method estimates the survival experience over follow-up while accounting for censoring.

The median is the time at which the estimated survival curve reaches the point where half of the population is estimated to have experienced the event. It is one summary of the survival distribution, not a description of every participant’s experience. For the bTMB-defined primary analysis, the reported medians were 11.7 months for durvalumab plus tremelimumab and 9.1 months for standard-of-care chemotherapy. These summaries do not show the full shape of the survival curves or explain how survival differed at every point in follow-up.

Overall survival is a clinically meaningful endpoint because it counts death from any cause rather than relying on a judgment about whether a particular cause of death is related to treatment. The registry record does not report details about the independent adjudication of deaths or any additional endpoint assessment procedures.

7. Results Posted in the Registry

• Global: Durvalumab + Tremelimumab vs Global: SoC Chemotherapy: hazard ratio 0.71 (95% CI 0.48–1.04), reported p = 0.081 (as reported in the registry).

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a time-to-event endpoint. Each participant contributes follow-up from randomization until death or censoring. Censoring occurs when a participant is not known to have died by the analysis time; the registry says such participants were censored at their last recorded date known alive. Censoring is not the same as a death or a statement that follow-up continued indefinitely. It indicates that the exact event time is not observed within the available follow-up.

What does the Kaplan-Meier method estimate?

As a general statistical explanation, the Kaplan-Meier method estimates the probability of remaining event-free over time while incorporating the timing of events and censoring. It uses the information available at each event time, so participants who are censored contribute information while they are under observation. The method relies on assumptions about censoring, including that censoring does not selectively remove people with a different future event experience in a way that distorts the estimate. The registry record does not report diagnostic checks of those assumptions.

The registry states that median OS was calculated using the Kaplan-Meier technique. The median is read from the estimated survival curve at the point where estimated survival reaches one half. It condenses a time-to-event distribution into one value, but discards information about the timing and shape of the curve. The median estimates were 11.7 months and 9.1 months in the two groups. Their confidence intervals describe uncertainty around each median; they are not a confidence interval for the difference between medians.

What does the hazard ratio represent?

The trial reports a hazard ratio using the log-rank method. As a general statistical explanation, a hazard is the instantaneous event rate among people who have not yet experienced the event, at a particular point in follow-up. A hazard ratio compares hazards between groups. It is not a comparison of cumulative percentages, a direct comparison of medians, or an estimate of how long each individual will live.

The reported hazard ratio was 0.71, with a 95% confidence interval of 0.485 to 1.045. The value below 1 indicates a lower estimated hazard in the combination group relative to the chemotherapy group under the reported analysis. The interval describes uncertainty and includes 1, the value corresponding to no relative difference in hazard. The registry does not report whether proportional hazards were assessed or whether a different model was used to address any departure from that assumption. As a general point, if relative hazards change substantially over time, a single hazard ratio may not fully describe the pattern.

How should the p-value be read?

The reported p-value was 0.081. As a general statistical explanation, a p-value is calculated under a null hypothesis and the assumptions of a statistical test; it describes how compatible the observed data are with that null model. It does not give the probability that the null is true, and it does not quantify the clinical importance of an effect. The registry identifies the method as log-rank and the analysis as a superiority comparison. Further detail about the test implementation is not reported in the registry record.

Statistical significance is not a substitute for examining the estimate and its precision. The hazard ratio gives the direction and relative scale of the reported comparison, while the confidence interval shows a range of values compatible with the data under the interval’s assumptions. The p-value and confidence interval address related features of the same comparison but communicate them differently. Neither can establish whether an estimate is important for a particular clinical decision.

What is the analysis population?

The primary analysis set was a subset of the full analysis set: participants whose baseline blood tumor mutational burden was at least 20 Mut/Mb according to the named assay, and who were randomized in the global cohort. The registry explicitly notes that bTMB and tissue tumor mutational burden testing was not performed for the China cohort in this analysis context. The primary results therefore should not be generalized automatically to the China cohort or to participants with other biomarker values.

The registry lists analyses involving other bTMB and tTMB thresholds, PD-L1 categories, and global and China cohorts. Having multiple analyses can raise questions about multiplicity: when many hypotheses are tested, the chance of at least one apparently notable result can increase. Whether and how the trial controlled multiplicity for these analyses is not reported in the registry record. It is therefore not possible to infer a multiplicity adjustment from the list of analyses alone.

General statistical interpretation also depends on the analysis plan, follow-up, missingness, and censoring rules. The endpoint definition describes censoring at the last known date alive, but the registry record does not report the broader missing-data strategy, details of sensitivity analyses, or interim-analysis procedures. These omissions limit how fully an outside reader can reconstruct the analysis, without changing the values that the registry reports.

10. Confidence Intervals and Precision

The hazard ratio estimate is 0.71, and its 95% confidence interval runs from 0.485 to 1.045. A confidence interval is a range constructed by a statistical procedure to reflect uncertainty in an estimate. Under the procedure’s assumptions, intervals formed repeatedly in this way would cover the underlying value at the stated rate. It is not a statement that there is a 95% probability that this particular interval contains the true value.

The interval is important because it includes values below and above 1. Values below 1 correspond to a lower estimated hazard in the durvalumab plus tremelimumab group; values above 1 correspond to a higher estimated hazard, relative to chemotherapy. The reported data therefore do not pin down the comparative hazard with high precision. The point estimate alone would give an incomplete account of the uncertainty.

The median OS estimates also have confidence intervals: 11.7 months (8.6 to 15.2) for the combination group and 9.1 months (7.8 to 12.6) for chemotherapy. These intervals express uncertainty in each group’s median. They should not be treated as a direct interval for the difference between medians, and their overlap is not itself the test of the treatment comparison.

Precision depends on the amount and distribution of time-to-event information, not only on the number assigned to each group. The primary analysis set included 69 participants in one group and 60 in the other, but the registry does not report the number of deaths in this analysis set. The overall adverse-event record lists deaths for broader groups; those figures should not be substituted for the primary-set event count. The registry record does not report further precision measures for the primary comparison.

These intervals describe statistical uncertainty under the analysis assumptions; they do not account for every source of uncertainty, such as limitations in the population definition or the multiplicity of related analyses. They also do not indicate the range of outcomes expected for an individual participant.

11. Planning a Similar Trial: Sample Size

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

The planning display expresses time-to-event sample-size illustrations as total events, not participants per arm. Its entries are total events for 80% or 90% power under specified planning assumptions. For example, planning for 100% of the observed effect gives 268 total events for 80% power and 359 total events for 90% power. Planning for 75% of the observed effect gives 476 total events for 80% power and 637 total events for 90% power. Planning for 50% of the observed effect gives 1,071 total events for 80% power and 1,434 total events for 90% power.

As a general explanation, power is the chance that a study would detect an effect of the specified size under the assumed conditions, if that effect were present. The 80% power column describes a design with an 80% chance of detecting the assumed effect; the 90% column describes a design with a 90% chance. These are planning targets, not observed results. For a time-to-event endpoint, the stated figures concern the total number of events required, not the total enrollment or participants in each group.

The planning assumptions listed 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 figures are planning illustrations computed from the observed effect, not the trial’s original design assumptions; those original assumptions are not reported in the registry record. The planning values are not observed power.

Smaller effects are harder to distinguish from random variation, so the illustration requires more events when planning for a smaller fraction of the observed effect. The displayed event requirements do not say how many participants or how much follow-up would be needed to produce those events; that depends on event occurrence and follow-up. No conversion to participant counts is reported for these time-to-event figures.

12. How the Sample Size Is Derived

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

Formula

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 = 0.710, so ln(HR) = -0.3425.
2. d = 4 × (1.96 + 0.842)² / [ln(0.710)]² = 267.7, rounded up to 268 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 <- 0.71                              # 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(2542293)
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 = 268 (80% power), 359 (90% power)
 75% of observed effect: events = 476 (80% power), 637 (90% power)
 50% of observed effect: events = 1,071 (80% power), 1,434 (90% power)
Simulated power with 268 events: 0.779 (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.

13. 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 434 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 953 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 <- 9.1          # control-arm median, months (converted from the posted unit)
hr          <- 0.71          # 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: 316         p (1-sided)   0.0001
 Events: 121        ~HR at bound   0.5085
   Month: 17    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.71   0.0338
   IA 2: 67%                   Z   2.5114
      N: 434         p (1-sided)   0.0060
 Events: 241        ~HR at bound   0.7235
   Month: 28    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.71   0.5603
       Final                   Z   1.9930
      N: 434         p (1-sided)   0.0231
 Events: 362        ~HR at bound   0.8108
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.71   0.9000



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

14. Analyses Reported by the Sponsor

The primary hazard ratio and its confidence interval are reported as the sponsor’s analysis, using the log-rank method. The reported estimate is 0.71, with a 95% confidence interval from 0.485 to 1.045 and p=0.081. The registry record does not report an alternative recalculated hazard ratio for this time-to-event result. Accordingly, the sponsor’s reported analysis is the relevant comparative estimate to interpret.

The record does not flag a discrepancy between the sponsor analysis and a recalculation. The sample-size illustrations use the observed effect as an input, but they are planning calculations and do not replace or independently validate the sponsor’s outcome analysis. They address hypothetical design requirements under stated assumptions, not the trial’s observed survival comparison.

These distinctions matter because a reported analysis and a planning illustration answer different questions. The hazard ratio estimates the comparison in the analyzed subset; the planning exercise considers event requirements for detecting fractions of that estimated effect under specified assumptions. Neither converts the other into proof of a treatment effect, and the planning display should not be read as evidence that the trial was designed with those particular assumptions.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 20 outcome measures and 61 analyses. Secondary outcomes include overall survival, progression-free survival, objective response rate, and duration of response across biomarker-defined groups and cohorts. Analyses include multiple bTMB and tTMB thresholds, PD-L1 categories, the full analysis set, and global and China cohorts. This breadth provides several views of outcomes, but it also means the primary result is part of a larger collection of planned or posted analyses.

When many statistical comparisons are made, the chance of obtaining at least one apparently unusual result by chance can increase. As a general statistical principle, multiplicity procedures can adjust the interpretation of p-values or confidence intervals when multiple hypotheses are considered together. Whether the trial used such a procedure for the secondary or subgroup analyses, and which testing family it might have covered, is not reported in the registry record. No multiplicity adjustment should be assumed from the number or ordering of the analyses.

The primary outcome definition does describe one aspect of incomplete follow-up: participants not known to have died were censored at their last recorded date known alive. This is a standard feature of time-to-event analysis, but does not explain all possible missingness. The registry record does not report the extent of missing endpoint information, the handling of missing biomarker results beyond the named analysis-set definitions, or sensitivity analyses for missing data and censoring.

The registry also does not report interim-analysis procedures, stopping boundaries, or the original statistical analysis plan in enough detail to assess them. These details should not be inferred from the reported p-value or the study’s status. The record names the log-rank method for the primary comparison and describes the OS endpoint and censoring rule, but additional analytic specifications are not reported in the registry record.

The population definition is especially relevant to interpretation. The primary analysis concerns global-cohort participants in the bTMB-at-least-20 Mut/Mb set, not all randomized participants or every listed biomarker group. The registry record does not report the sample-size justification for this subset or the basis for selecting its threshold as the primary analysis population. These limitations constrain assessment of how confirmatory the subset result was intended to be.

16. 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: pneumonia (6.6%), pleural effusion (5.2%), pneumonitis (3.9%), pyrexia (3.9%), dyspnoea (3.9%).

The serious adverse-event summaries list global-cohort and China-cohort groups separately. In the global cohort, the registry lists 410 participants at risk and 193 with a serious adverse event in the durvalumab plus tremelimumab group, and 399 at risk and 112 with a serious adverse event in the standard-of-care chemotherapy group. In the China cohort, the corresponding figures are 77 at risk and 32 affected for durvalumab plus tremelimumab, and 78 at risk and 22 affected for standard-of-care chemotherapy.

The most frequently listed serious adverse-event terms include pneumonia (6.6%), pleural effusion (5.2%), pneumonitis (3.9%), pyrexia (3.9%), dyspnoea (3.9%), and bone marrow failure (3.8%). These terms and percentages are registry summaries; the record does not provide additional detail about event timing, severity grades, or whether each event was judged related to treatment.

The registry also lists deaths in the safety groups: 328 in the global combination group, 329 in the global chemotherapy group, 50 in the China combination group, and 62 in the China chemotherapy group. These are safety-group figures and should not be substituted for the number of OS events in the primary bTMB-defined analysis set. The record does not establish from these figures the cause of death or a causal relationship to treatment. Serious adverse events and deaths should be interpreted as distinct summaries.

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

The result describes a randomized comparison of durvalumab plus tremelimumab with standard-of-care chemotherapy for overall survival in a particular global-cohort biomarker subset. The reported median OS values were 11.7 months and 9.1 months, respectively. The hazard ratio was 0.71, with a 95% confidence interval from 0.485 to 1.045 and p=0.081. Together, these statistics show the direction and uncertainty of the reported comparison, not a definitive account of every participant’s experience.

The estimate is not a direct prediction for an individual. A group median is not a guaranteed survival time, and a hazard ratio is not a personal risk ratio or a measure of the amount of time an individual gains or loses. The confidence interval indicates that the relative hazard estimate remains uncertain; it includes values both below and above 1. The p-value is not the probability that the treatments are equivalent, nor the probability that the result occurred by chance.

The analysis population is also central to the result’s meaning. The primary estimate applies to the specified bTMB-at-least-20 Mut/Mb subset in the global cohort. It does not automatically apply to people with different biomarker results, the China cohort, or the entire trial population. The registry lists other biomarker and cohort analyses, but their results are not part of this primary comparison.

The posted result does not by itself establish a treatment recommendation or determine the balance of benefits and harms. The safety summaries report serious adverse events and deaths across broader safety groups, but they do not establish event causality, timing, or how those summaries relate to the primary analysis population. The registry record also does not report the original design assumptions, the multiplicity strategy, or all details needed to independently reconstruct the analysis.

In statistical terms, the result is an estimate with a reported uncertainty interval and a log-rank p-value. It should be read alongside the population definition, open-label design, endpoint and censoring rules, and wider set of analyses. It cannot answer questions that the registry does not report, such as whether the finding is consistent across every subgroup or how the original sample-size rationale was set.

18. Why This Trial Matters Statistically

This trial illustrates why the population attached to an endpoint estimate matters. The registry records enrollment of 953, while the primary OS comparison concerns a narrower bTMB-defined global-cohort analysis set with 69 participants in the combination group and 60 in the chemotherapy group. Those figures describe different parts of the trial and answer different questions. Treating the primary subset as if it represented the full enrollment would obscure the scope of the result.

It also demonstrates the value of reading a hazard ratio with its confidence interval rather than focusing on the point estimate alone. The estimate of 0.71 points below 1, while the 95% confidence interval extends from 0.485 to 1.045. The interval communicates uncertainty that the point estimate cannot. The p-value of 0.081 provides another summary of the comparison under the log-rank method, but does not replace consideration of the estimate, interval, or analysis population.

The registry’s many biomarker and cohort analyses raise a broader statistical issue: multiple comparisons can complicate interpretation. A list of analyses does not establish that multiplicity was controlled, and the registry does not report whether it was. This is a reminder that statistical conclusions depend not only on a numerical estimate, but also on the analysis plan and how results across endpoints and subgroups are interpreted.

Finally, the sample-size illustrations distinguish event requirements for planning from observed trial results. Time-to-event planning depends on events, not simply on enrollment, and the illustrative requirements are based on stated assumptions that are not the original trial design assumptions. Understanding that distinction helps prevent planning figures from being mistaken for evidence about the outcome comparison or the power actually achieved.

19. 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 primary result is restricted to the global-cohort bTMB-at-least-20 Mut/Mb analysis set. It should not be generalized automatically to the full trial population, other bTMB or tTMB thresholds, PD-L1 groups, or the China cohort. The registry describes the assay and baseline biomarker definition, but does not report the original rationale for this analysis set or its sample-size justification.

The study was open-label, and the registry does not describe further procedures to reduce possible effects of unmasked treatment assignment on trial conduct or outcome assessment. Overall survival is based on death from any cause, but the registry does not report additional details about death ascertainment or independent review. The endpoint definition explains how censoring was handled for participants known to be alive at analysis; diagnostics and sensitivity analyses for censoring assumptions are not reported in the registry record.

The primary analysis set was relatively limited in size, and the registry does not report its number of deaths. The reported confidence interval for the hazard ratio extends from 0.485 to 1.045, indicating uncertainty around the comparative estimate. The broader safety-group death counts cannot serve as primary-set event counts because they refer to different analysis populations.

The registry lists numerous outcomes and subgroup analyses, but does not report the multiplicity strategy, interim-analysis procedures, or the original statistical analysis plan in sufficient detail. It also does not report all missing-data procedures or sensitivity analyses. These omissions restrict an independent assessment of the analysis choices and the broader family of statistical conclusions.

Finally, the listed chemotherapy options include different platinum-based regimens. The registry record does not provide the distribution of those regimens in the primary analysis set or further details about how treatment choices were made. The primary comparison is therefore between the assigned combination strategy and the registry’s standard-of-care chemotherapy arm, rather than a separately reported comparison against each individual chemotherapy regimen.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Durvalumab With Tremelimumab Versus SoC as 1st Line Therapy in Metastatic Non Small-Cell Lung Cancer (NSCLC) (NEPTUNE) — NCT02542293.
• Registry record last updated 2026-08-06; status last verified 2026-08.
• Results first posted 2022-05-24.
• 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.

23. Record Summary

The registry describes NCT02542293, NEPTUNE, as a Phase III randomized, open-label, parallel-group, global study of durvalumab plus tremelimumab versus platinum-based standard-of-care chemotherapy in first-line advanced or metastatic NSCLC. Enrollment is listed as 953; the study status is active, not recruiting. Primary completion is recorded as 2020-09-21.

The primary outcome is overall survival in the global-cohort bTMB-at-least-20 Mut/Mb analysis set. Median OS was 11.7 months with durvalumab plus tremelimumab and 9.1 months with standard-of-care chemotherapy. The reported hazard ratio was 0.71 (95% confidence interval 0.485 to 1.045), with p=0.081 by the log-rank method. The result is specific to the stated analysis population and should be interpreted with its uncertainty and the registry’s broader analysis context in mind.