Durvalumab Alone or in Combination With Novel Agents in Subjects With NSCLC: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Durvalumab Alone or in Combination With Novel Agents in Subjects With NSCLC (NCT03822351), a randomized phase 2 study. The primary outcome is Objective Response (OR) Rate as a Measure of Antitumor Activity of Durvalumab Alone vs Durvalumab in Combination With Novel Agents.

2. Clinical Question

3. Trial Design

COAST, registered as NCT03822351, was a phase 2, randomized, open-label, multicenter, multidrug platform study in people with locally advanced, unresectable stage III non-small cell lung cancer. Its official title describes durvalumab alone or in combination with novel agents. The listed interventions were durvalumab monotherapy, durvalumab plus oleclumab, and durvalumab plus monalizumab.

The design was parallel-group: participants were assigned to a treatment group and analyzed according to that randomized assignment for the primary endpoint. There was no masking. The record reports enrollment of 189 and a completed status. The study start date was 2018-12-19, and primary completion was 2023-07-18. These dates describe the registry record; they do not provide details about recruitment timing, follow-up completeness, or the duration each participant was observed.

The stated purpose was to compare clinical activity of durvalumab alone with durvalumab combined with novel agents. The study summary says participants had not progressed after concurrent chemoradiotherapy. The primary endpoint was objective response at 16 weeks after randomization. Secondary outcomes included safety measures and measures of disease control, response duration, progression-free survival, a progression-free survival landmark, and overall survival.

The registry record does not report the original sample-size justification or the trial’s original statistical design assumptions. It lists no reported analyses for the secondary outcomes addressed in the posted results summarized in the record. Details such as stratification factors, treatment discontinuation rules, and the exact randomization procedure 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent-to-treat (ITT) population included participants who were randomized and were analyzed according to their randomized treatment group

5. Baseline Characteristics

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

Population: The Intent-to-treat (ITT) population included participants who were randomized and were analyzed according to their randomized treatment group

6. Primary Endpoint

The registry lists the primary outcome as Objective Response (OR) Rate as a Measure of Antitumor Activity of Durvalumab Alone vs Durvalumab in Combination With Novel Agents, measured over ORR at 16 weeks after randomization is the timing for radiologic assessment of the primary endpoint.

The primary endpoint was objective response rate, expressed as the percentage of participants with at least one visit response of complete response or partial response under RECIST 1.1. The record defines complete response as disappearance of all target lesions and partial response as a decrease of at least 30% in the sum of the longest diameters of target lesions. The assessment timing was 16 weeks after randomization.

Objective response is a binary outcome at the participant level: a participant either met the response definition during the specified assessment period or did not. Reporting the proportion meeting the definition gives a readily interpretable summary of tumor response. In general, a radiologic response endpoint can indicate whether measurable target lesions meet specified response criteria, but it does not by itself describe how long a response lasts or establish effects on survival.

The intent-to-treat population included participants who were randomized and analyzed according to randomized group. This preserves the randomized comparison in the analysis definition, even if a participant’s treatment after assignment differed. The registry record does not describe how missing or unevaluable 16-week assessments were handled, so the impact of those circumstances cannot be assessed from the information reported.

7. Results Posted in the Registry

• Arm A (Durvalumab + Oleclumab): 35.0% (21/60) versus 23.9% (16/67) on control; risk difference 11.1 percentage points (95% CI -4.7 to 26.9), risk ratio 1.47 (0.85–2.54); unadjusted two-proportion z-test p = 0.169.
• Arm B (Durvalumab + Monalizumab): 40.3% (25/62) versus 23.9% (16/67) on control; risk difference 16.4 percentage points (95% CI 0.5 to 32.4), risk ratio 1.69 (1.00–2.85); unadjusted two-proportion z-test p = 0.045.

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.

Disease Control (DC) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents

• 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:
  • Arm A (Durvalumab + Oleclumab): 80.0% (48/60) versus 58.2% (39/67) on control; risk difference 21.8 percentage points (95% CI 6.2 to 37.3), risk ratio 1.37 (1.08–1.75); unadjusted two-proportion z-test p = 0.008.
  • Arm B (Durvalumab + Monalizumab): 79.0% (49/62) versus 58.2% (39/67) on control; risk difference 20.8 percentage points (95% CI 5.3 to 36.4), risk ratio 1.36 (1.07–1.73); unadjusted two-proportion z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm A (Durvalumab + Oleclumab) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm B (Durvalumab + Monalizumab) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Progression-Free Survival 12 Month Landmark Rate (PFS-12) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents

• 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:
  • Arm A (Durvalumab + Oleclumab): 63.3% (38/60) versus 37.3% (25/67) on control; risk difference 26.0 percentage points (95% CI 9.2 to 42.8), risk ratio 1.70 (1.18–2.45); unadjusted two-proportion z-test p = 0.003.
  • Arm B (Durvalumab + Monalizumab): 72.6% (45/62) versus 37.3% (25/67) on control; risk difference 35.3 percentage points (95% CI 19.2 to 51.3), risk ratio 1.95 (1.38–2.75); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm A (Durvalumab + Oleclumab) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm B (Durvalumab + Monalizumab) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the questions beyond whether participants met the primary response definition at 16 weeks. They include disease control, duration of response, progression-free survival, a 12-month progression-free survival landmark, overall survival, and safety measures. These outcomes may describe other aspects of disease course and tolerability, but they are not interchangeable with the primary response endpoint.

Among the posted secondary results described in the registry record, the disease-control and 12-month progression-free survival estimates are higher in each combination group than in the monotherapy group. That overall directional pattern is consistent with the direction of the primary response percentages. However, the endpoints have different definitions and assessment timeframes, and this shared direction does not establish that they measure the same effect or provide independent confirmation of the primary result.

The record lists no reported analyses for these secondary results. The comparisons included with the summaries are unadjusted. In general, testing many outcomes or treatment contrasts increases the chance of seeing apparently noteworthy results by chance unless the analysis plan accounts for multiplicity. The registry record does not report such an adjustment or a hierarchy that would distinguish confirmatory from exploratory tests. Consequently, secondary findings carry less weight than a prespecified, multiplicity-controlled primary analysis would carry.

Some listed secondary outcomes, including duration of response, progression-free survival, and overall survival, are time-to-event measures. Their interpretation depends on follow-up, censoring, event definitions, and the analysis method. Those details and corresponding reported analyses are not available in the registry record. The posted landmark estimate addresses status at a specified time, rather than providing the full time-to-event picture. The secondary outcome pattern can therefore add descriptive context, but it should not be used to claim a confirmed treatment effect across endpoints.

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

• Presence of Adverse Events as a Measure of Safety and Tolerability of Durvalumab Alone and in Combination With Novel Agents
• Presence of Clinically Significant Laboratory Values as a Measure of Safety and Tolerability of Durvalumab Alone and in Combination With Novel Agents
• Presence of Abnormalities in Vital Signs as a Measure of Safety and Tolerability of Durvalumab Alone and in Combination With Novel Agents
• Duration of Response (DoR) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents
• Disease Control (DC) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents
• Progression-Free Survival (PFS) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents
• Progression-Free Survival 12 Month Landmark Rate (PFS-12) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents
• Overall Survival (OS) as a Measure of Efficacy of Durvalumab Alone vs Durvalumab in Combination With Novel Agents

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because response is classified as present or absent under the registry’s definition. The posted percentages estimate the proportion meeting that definition in each treatment group. A risk difference compares two such proportions by subtraction. The comparison estimates are reported as 0.111 for durvalumab plus oleclumab versus monotherapy and 0.164 for durvalumab plus monalizumab versus monotherapy. Their intervals describe uncertainty in each estimated difference.

What does a confidence interval describe?

In general, a confidence interval is a range of values compatible with the observed data under the statistical method used. It conveys precision as well as the estimate’s direction and magnitude. Wider intervals indicate less precision; narrower intervals indicate greater precision. A confidence interval is not a guarantee that the true value lies inside the particular reported interval, and it does not describe the range of individual participant outcomes. The registry identifies the arm-level dispersion as a 95% confidence interval.

The arm-level outcome percentages have their own confidence intervals. Those intervals quantify uncertainty about the response proportion in each group, rather than the uncertainty in a between-group difference. For the direct comparisons, the risk-difference intervals are the relevant reported intervals. Whether an interval includes zero is one way to assess compatibility with no difference; it should be read alongside the estimate, interval width, and analysis context rather than treated as a complete interpretation by itself.

How should p-values be read?

A p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be under the statistical model, if that null hypothesis and model were appropriate. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The reported p-values for the primary comparisons are unadjusted. The registry record does not report whether or how the study addressed multiple comparisons, so these p-values should not be interpreted as multiplicity-controlled evidence.

The risk difference is not the only possible summary of a binary comparison. The posted comparison information also includes relative risk and odds ratio estimates with intervals. These measures express comparisons on different scales: relative risk compares proportions as a ratio, while odds ratio compares odds. In general, relative measures can look different from absolute differences, particularly when the underlying outcome proportion is not small. None should be read without considering the endpoint definition and observed group proportions.

Why distinguish analysis populations?

The primary population is described as intent-to-treat: randomized participants were analyzed in their assigned group. In general, this approach maintains the comparison defined by randomization and avoids regrouping participants according to post-randomization treatment received. The registry record does not report further details about missing outcome handling or whether additional analysis populations were used. It is therefore not possible to assess from this record whether missing assessments, protocol deviations, or other analysis decisions altered the endpoint estimates.

The primary assessment occurred at 16 weeks after randomization. A fixed assessment time makes the endpoint a comparison of response status at a defined point, but it does not summarize the timing or duration of response over the full course of follow-up. The secondary outcome list includes duration of response and time-to-event outcomes, which address different questions. The record does not post reported analyses for those secondary outcomes in the information.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variability is greater than expected under a model’s assumptions. For binary outcomes, a simple model may assume a particular pattern of independent participant outcomes. If responses are more variable than that model allows, estimated uncertainty can be understated. This is a general statistical concern, not a claim that over-dispersion occurred in this study. The registry record does not report a model assessment or method addressing over-dispersion.

The posted comparisons are simple, unadjusted comparisons of the reported group summaries. The registry record does not describe covariate adjustment, stratification in the analysis, a prespecified hierarchy of tests, or a multiplicity correction. Those methods should not be inferred from the randomized design alone. Randomization supports a treatment-group comparison in principle, but the credibility and precision of a particular estimate also depend on the analysis plan, missing data, adherence, and outcome ascertainment. Some of those details are not reported in the registry record.

11. Confidence Intervals and Precision

The 95% confidence intervals show that the response estimates are not exact measurements of a fixed underlying proportion. For monotherapy, the interval is 14.3% to 35.9%; for durvalumab plus oleclumab, it is 23.1% to 48.4%; and for durvalumab plus monalizumab, it is 28.1% to 53.6%. These ranges overlap. Overlap of separate group intervals is not itself a formal test of the difference, so the posted risk-difference intervals are more directly relevant to comparing each combination with monotherapy.

The risk-difference interval for oleclumab, -0.047 to 0.269, is broad and includes zero. Its estimate is 0.111. The interval therefore allows a range that includes a difference favoring either group, as well as larger positive differences. For monalizumab, the estimate is 0.164 and its interval is 0.005 to 0.324. This range is also broad; its lower bound is close to zero, and its upper bound allows a substantially larger difference than the point estimate.

In general, confidence interval width depends on the amount of information and the variability of the outcome. The registry reports group sizes of 67.0, 60.0, and 62.0 for the primary endpoint. With estimates based on groups of this scale, uncertainty remains meaningful, as reflected in the intervals. The precision of a percentage and the precision of a between-group difference are separate: the latter depends on uncertainty in both groups.

Intervals do not resolve questions about clinical importance, bias, or multiplicity. A narrow interval can still concern an endpoint that is not clinically decisive, while a wider interval may leave important effects plausible in more than one direction. The registry record does not provide a prespecified threshold for a clinically important difference. The primary result should therefore be read as a set of estimated response proportions and uncertain contrasts, not as a definitive ranking of treatment strategies.

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 for a future two-group comparison, not the original design justification for COAST. For these binary outcomes, the figures are participants per arm, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column gives the corresponding planning size for a 90% chance. These are design calculations conditional on the assumed effect and method; they are not probabilities that the trial result is correct.

The rows use the full observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller assumed effects require more participants to distinguish them from no difference with the same target power and significance level. The figures vary by comparison because the observed effects used as planning inputs differ. They are sensitive to those inputs: an observed effect from a phase 2 study may not be the effect a later study should expect.

This is not observed power. Observed power would use the effect estimated from the completed study and is not a useful substitute for reading the estimates and their confidence intervals. The planning illustrations are best treated as conditional scale checks, not as a recommendation for a future study size. They do not incorporate assumptions beyond those listed in the registry record.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.239; treatment proportion p₁ = 0.350; average p̄ = 0.294.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6446 = 1.2633.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6397 = 0.5384.
4. n = (1.2633 + 0.5384)² / (0.1112)² = 262.6, rounded up to 263 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.238805970149254                          # control proportion
p1 <- 0.35                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

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

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3822351)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 263 (80% power), 351 (90% power)
 75% of observed effect: n per arm = 455 (80% power), 608 (90% power)
 50% of observed effect: n per arm = 992 (80% power), 1,328 (90% power)
power.prop.test: 262.6 
Simulated power at n = 263 per arm: 0.802 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The trial compared two combination strategies with a shared monotherapy group and included a range of primary and secondary outcomes. When several hypotheses are tested, the probability of at least one result appearing noteworthy by chance can increase. In general, multiplicity procedures can control that risk by adjusting thresholds or by specifying an order in which hypotheses are tested. The registry record does not report a multiplicity strategy, a testing hierarchy, or adjusted p-values. The posted primary comparison p-values are explicitly unadjusted, and the secondary comparisons are also unadjusted.

This omission matters for interpretation, especially when a result is near a conventional threshold. A nominal p-value does not establish that a finding would remain statistically notable after accounting for the number of comparisons. At the same time, the registry record alone does not establish that no multiplicity procedures were used outside the record; it establishes only that such procedures are not reported in the registry record. The appropriate conclusion is that the posted results do not allow assessment of multiplicity control.

Missing-data methods are also not reported in the registry record. The primary endpoint is defined at a radiologic assessment at 16 weeks, but the record does not describe how participants without an evaluable assessment were classified or handled. It does not report the amount or pattern of missing outcome data. Without that information, the potential influence of missing assessments on the response estimates cannot be evaluated.

The registry states that the primary population was intent-to-treat, with randomized participants analyzed in their assigned groups. This describes the assigned-group principle, but does not by itself explain the handling of missing outcomes or all analysis exclusions. Details of any per-protocol or other analysis population are not reported in the registry record. The number of posted secondary outcomes is 12, while the record lists no reported analyses for the secondary outcomes summarized. These gaps limit the ability to reconstruct the full statistical plan or judge the robustness of findings across alternative analyses.

15. 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: pneumonitis (10.2%), pneumonia (7.6%), radiation pneumonitis (3.4%), seizure (3.0%), acute respiratory failure (3.0%).

The registry reports serious adverse-event counts among participants at risk: 23 of 66 in the durvalumab monotherapy group, 20 of 59 in the durvalumab plus oleclumab group, and 17 of 61 in the durvalumab plus monalizumab group. Counts for other adverse events were 61 of 66, 52 of 59, and 58 of 61, respectively. The registry also lists deaths by group: 27, 23, and 24. These are descriptive counts, not adjusted comparisons, and the record does not state that the listed deaths were caused by treatment.

The most frequently listed serious-event terms include pneumonitis (10.2%), pneumonia (7.6%), radiation pneumonitis (3.4%), seizure (3.0%), acute respiratory failure (3.0%), and pleural effusion (3.0%). The record does not provide, in the information, a full event-by-event breakdown by treatment group or the derivation of these term percentages. Serious-event counts do not convey severity, duration, relatedness, or the number of recurrent events. They should be read as a limited safety summary rather than as a causal comparison of regimens.

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

The posted primary results show higher observed objective response percentages in both combination groups than in the durvalumab monotherapy group at the specified assessment. The comparison estimates and confidence intervals convey how uncertain those differences are. For the oleclumab comparison, the interval includes zero; for the monalizumab comparison, the interval is just above zero. Both intervals remain broad enough to allow a range of possible effect sizes. The p-values are unadjusted.

These findings do not establish that either combination is superior in a confirmatory sense. The record does not report multiplicity control, the original sample-size justification, missing-data handling, or the trial’s full statistical analysis plan. The study is described as phase 2 and as aiming at early identification of combinations with greater clinical activity. That context supports treating the results as exploratory signals requiring cautious interpretation, not as definitive proof.

Objective response at 16 weeks is not the same as response duration, disease control, progression-free survival, or overall survival. A response classification does not by itself show how long a response persists or what happens after the assessment. Although the record lists several secondary endpoints, reported analyses are absent for the secondary outcomes described. The summary of secondary outcomes therefore cannot establish a treatment effect on survival or other later outcomes.

Nor do these data establish the cause of adverse events or deaths. The registry provides group-level safety counts and selected serious-event terms, but not a causal assessment. The findings apply to the population and setting described in the record; they should not be generalized to other stages, clinical settings, or treatment sequences without evidence. No medical recommendation follows from these registry results alone.

17. Why This Trial Matters Statistically

Statistically, the trial illustrates the distinction between an estimate and the evidence supporting it. The response percentages describe observed outcomes in each randomized group, while risk differences summarize the contrasts of interest. Confidence intervals show that those contrasts remain uncertain. Reporting both estimates and intervals is more informative than focusing on a p-value alone.

The study also highlights the challenges of a multidrug platform comparison. Two combinations are compared with a shared monotherapy group, and the registry lists numerous additional outcomes. Such a setting raises questions about multiplicity, endpoint hierarchy, and whether findings are exploratory or confirmatory. The registry record does not report the procedures needed to resolve those questions. This makes clear why a nominally small unadjusted p-value should not be interpreted in isolation.

The planning illustrations demonstrate how assumed effect size affects design. Their participant requirements increase as the targeted fraction of the observed effect gets smaller. This is a general feature of planning binary-outcome comparisons, not evidence that the trial was designed around those figures. Keeping planning assumptions distinct from the original study design prevents a calculated illustration from being mistaken for an observed trial property.

Finally, the record shows why endpoint scope matters. A radiologic response at a fixed assessment, disease control, a landmark survival rate, and time-to-event outcomes answer different questions. Separating these measures helps avoid treating a favorable pattern in one outcome as proof of a broader clinical benefit. Clear reporting of analysis populations, missing data, multiplicity, and event handling would further support independent interpretation.

18. Limitations

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

The registry record leaves several trial-specific details unreported. The original sample-size justification and design assumptions are not available, so the posted planning illustrations cannot be used to infer the study’s intended power or design target. The record does not describe multiplicity control, a testing hierarchy, or adjusted results. This limits interpretation of the unadjusted p-values across multiple comparisons and outcomes.

Missing outcome handling is also not described. The primary endpoint depends on radiologic assessment at 16 weeks, but the record does not state how unevaluable assessments were classified, how much data were missing, or whether sensitivity analyses were conducted. Details of response assessment procedures beyond the RECIST 1.1 definitions are not reported in the registry record.

The analysis information is limited for secondary endpoints. Although the record lists secondary outcomes, it gives no reported analyses for the outcomes described. Follow-up and analysis details needed to interpret time-to-event outcomes are not reported in the registry record. The secondary summaries therefore do not establish the reliability or completeness of results for those endpoints.

The study was open-label, and the record does not describe procedures that might address potential assessment or performance influences. The registry information also does not provide a complete treatment exposure account, event attribution, or detailed safety breakdown by event and group. These limitations do not negate the posted estimates, but they restrict what can be concluded from them. The available record supports descriptive interpretation of response estimates and safety counts, not a comprehensive evaluation of efficacy, long-term outcomes, or comparative safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Durvalumab Alone or in Combination With Novel Agents in Subjects With NSCLC — NCT03822351.
• Registry record last updated 2024-10-08; status last verified 2024-10.
• Results first posted 2024-10-08.
• 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.

22. Record Summary

NCT03822351 is a completed, randomized, open-label, phase 2 parallel-group study of durvalumab alone or with oleclumab or monalizumab in unresectable stage III non-small cell lung cancer. The primary endpoint was objective response at 16 weeks after randomization, assessed under RECIST 1.1 in the intent-to-treat population.

The posted response percentages were 23.9% for monotherapy, 35.0% with oleclumab, and 40.3% with monalizumab. The unadjusted risk-difference intervals were broad; the oleclumab interval included zero, and the monalizumab interval was just above zero. Secondary summaries show a generally higher direction for combination groups on the outcomes reported, but the registry lists no reported secondary analyses. Multiplicity procedures, missing-data handling, and the original sample-size justification are not reported in the registry record. Safety information is descriptive and does not establish event causation.