A Study of Durvalumab as Consolidation Therapy in Non-Small Cell Lung Cancer Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Durvalumab as Consolidation Therapy in Non-Small Cell Lung Cancer Patients (NCT03706690), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS) (Modified Intent-to-Treat [mITT] Set).

2. Clinical Question

3. Trial Design

This is a Phase III randomized, double-blind, placebo-controlled, multicentre, parallel-group study sponsored by AstraZeneca. Its title describes the use of durvalumab as consolidation therapy in patients with locally advanced, unresectable non-small cell lung cancer who had not progressed following definitive platinum-based chemoradiation. The registry lists an enrollment of 407 and a status of active, not recruiting.

Participants were assigned to durvalumab or matching placebo. The durvalumab regimen was 1500 mg intravenously every 4 weeks; the placebo was also infused every 4 weeks. The registry describes treatment continuing until clinical progression or deterioration, or confirmed radiological progression. Masking is recorded as quadruple, but the registry record does not identify each masked role in the information available for this result.

The primary endpoint was progression-free survival in a modified intent-to-treat population. This population included randomized participants without sensitizing EGFR mutations or ALK rearrangements. A separate intent-to-treat progression-free survival result is also posted. The record lists overall survival, response outcomes and other time-to-event outcomes among the secondary measures, but their individual results are not all reported in the registry record.

The study start date is 2018-11-27, and the primary completion date is 2024-06-23. The posted primary assessment used a data cutoff date of 23-Jun-2024. The registry identifies the study as active, not recruiting; it does not establish from that status alone that every listed outcome is final or that follow-up has ended.

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: The study consisted of a screening period (Day -84 to Day -1), randomization (Day 1), treatment period commencing on Day 1 and a survival follow-up period until protocol-specified discontinuation criteria were met. A total of 407 participants were randomized in a 2:1 ratio to receive either durvalumab or placebo in this study. Results are presented up to data cut-off (DCO) date of 23-Jun-2024.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The mITT set included all randomized participants who were without sensitizing epidermal growth factor receptor (EGFR) mutations or anaplastic lymphoma kinase (ALK) rearrangements.

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 ITT set included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS) (Modified Intent-to-Treat [mITT] Set), measured over Tumor scans performed at screening, every 8 weeks ±1 week up to 48 weeks, and then every 12 weeks ±1 week thereafter until confirmed PD. Assessed up to the DCO date 23-Jun-2024 (a maximum of approximately 2035 days).

The primary endpoint is progression-free survival, or PFS, in the modified intent-to-treat set. It measures the time from randomization until objective disease progression or death from any cause when progression has not occurred. The definition applies regardless of whether a participant stopped study treatment or received another anti-cancer therapy before progression. Progression was assessed using RECIST 1.1, with blinded independent central review.

For target lesions, the registry defines progression as at least a 20% increase in the sum of diameters and an absolute increase of at least 5 mm, using the smallest sum of diameters since treatment began as the reference, including the baseline measurement. PFS is a time-to-event endpoint: each participant contributes information about the time until progression or death, or about their observed follow-up if neither event has been recorded by the analysis cutoff.

Median PFS describes the time by which half of the population’s estimated event-time distribution has experienced progression or death. The registry states that medians were estimated with the Kaplan-Meier technique. PFS is used to summarize how long participants remain alive without a recorded progression event; it does not, by itself, describe overall survival, symptoms, quality of life or the experience of every participant.

Tumor scans were scheduled at screening, every 8 weeks ±1 week up to 48 weeks, and every 12 weeks ±1 week thereafter until confirmed progression. The assessment was conducted up to the 23-Jun-2024 data cutoff.

7. Results Posted in the Registry

• Durvalumab vs Placebo: hazard ratio 0.75 (95% CI 0.58–0.99), reported p = 0.038 (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.

Progression-Free Survival (PFS) (Intent-to-Treat [ITT] Set)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Durvalumab vs Placebo: hazard ratio 0.74 (95% CI 0.57–0.97), reported p = 0.026 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Durvalumab vs Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists a range of secondary outcomes, including overall survival, intent-to-treat PFS, response, duration of response, landmark survival and progression measures, and time to distant metastases. The posted intent-to-treat PFS result points in the same direction as the primary modified intent-to-treat PFS result. This similarity is a coherence check across related populations, but the estimates are not independent confirmations: the populations overlap in definition and the endpoint is closely related.

The record lists 12 secondary outcomes, but the result details for the full set are not reported in the registry record. The available information therefore does not support a broad claim that every secondary endpoint followed the same pattern. The listed outcomes also address different questions: some concern survival, some tumor response, and others subsequent disease events. A result on one endpoint cannot be assumed to determine the result on another.

Secondary analyses generally carry less confirmatory weight when many outcomes are examined and no adjustment for multiple comparisons is reported. With repeated testing, the chance of obtaining at least one apparently notable result can increase even when no corresponding underlying effect exists. This is a general statistical concern, not a claim about the result of any unreported test in this study. A multiplicity strategy is not reported in the registry record, so the degree of statistical protection for the secondary findings cannot be determined from the posted information.

The primary endpoint remains the principal result for the stated main question. Secondary outcomes can add context, but their interpretation depends on which results were prespecified, how testing was ordered or adjusted, and how complete their reporting is. Those details are not reported for the full secondary set.

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

• Overall Survival (OS)
• Progression-Free Survival (PFS) (Intent-to-Treat [ITT] Set)
• Percentage of Participants Alive at 24 Months (OS24)
• Objective Response Rate (ORR)
• Duration of Response (DoR)
• Percentage of Participants Alive and Progression-Free at 12 and 18 Months (PFS12 and PFS18)
• Time From Randomization to Second Progression (PFS2)
• Time to Death or Distant Metastases (TTDM)

9. Statistical Interpretation

10. Statistical Methods Explained

How is progression-free survival defined?

Progression-free survival is a time-to-event measure. For each participant, the event is the first of objective disease progression or death in the absence of progression. The clock begins at randomization. The endpoint definition allows the event to count even if a participant withdrew from therapy or received another anti-cancer therapy before progression. This definition is important because it states which events contribute to the analysis and when follow-up begins.

Progression was determined under RECIST 1.1 using blinded independent central review. The registry specifies a lesion-based rule involving an increase in the sum of target-lesion diameters, together with an absolute increase threshold. Central review is intended to apply a common assessment process across treatment groups. The record states the assessment approach but does not report all operational details of image review or adjudication.

What does the Kaplan-Meier method contribute?

Kaplan-Meier estimation is a way to estimate the distribution of time to an event while accounting for participants whose event time is not observed during the available follow-up. Such observations are commonly described as censored: the participant contributes information up to the last time their event status is known, without being treated as if an event occurred at that point. This is a general explanation of the method. The registry says the median PFS was calculated using Kaplan-Meier, but does not report all censoring rules or details for handling missing assessments.

The median is the time at which the estimated event-free proportion reaches one half. It is a single summary of the estimated curve and does not show the curve’s complete shape. The confidence interval around a median reflects uncertainty in locating that point. In the posted results, the median estimates and their intervals are reported separately for each treatment group.

How should the hazard ratio be read?

The hazard ratio compares the estimated instantaneous event hazard between groups over follow-up. The registry reports the durvalumab-versus-placebo hazard ratio and identifies Log Rank as the comparison method. A hazard ratio below 1 points toward a lower estimated hazard in the durvalumab group for the endpoint as defined. It is not a ratio of median times, does not directly state the probability that an individual will experience an event, and should not be converted into an absolute reduction using the posted medians.

A hazard ratio is most readily interpreted as a single relative summary when the relative event rate is reasonably stable over time. The registry record does not report a test of proportional hazards or other diagnostics establishing that condition. The estimate should therefore be read as the sponsor-reported summary, with its confidence interval, rather than as a complete description of how group differences may vary during follow-up.

What do the confidence interval and p-value add?

A confidence interval gives a range of values compatible with the data under the statistical procedure, and conveys uncertainty about the estimate. For a hazard ratio, 1 represents no relative difference in event hazard. The primary interval extends from 0.578 to 0.986. The reported p-value is 0.038. The p-value describes how unusual the data would be under a specified null model and analysis assumptions; it is not the probability that the null hypothesis is true or the probability that the result arose by chance.

The record identifies the primary comparison as a Log Rank analysis and reports a hazard ratio with a 95% confidence interval. It does not report the full statistical analysis plan, the method used to calculate the confidence interval, or whether additional model checks were performed. Those details should not be inferred from the results alone.

Why do the analysis populations matter?

The primary result uses the modified intent-to-treat set, defined as randomized participants without sensitizing EGFR mutations or ALK rearrangements. The secondary PFS result uses the intent-to-treat set. These populations differ by definition, and the registry reports separate group counts and estimates for each. Results from the two populations are related but are not interchangeable. The primary population definition determines the population to which the main estimate directly applies.

The record also lists secondary outcomes including overall survival, response measures and later progression-related outcomes. The presence of an outcome in the registry does not mean that its result or full analysis details are reported. The registry does not report every secondary result in the information summarized for these findings.

What does the planning illustration represent?

The planning illustration uses an observed treatment effect as its reference and considers smaller fractions of that effect. Its assumptions are a two-sided significance level of 0.05, equal allocation between two arms and a normal approximation. For time-to-event outcomes, the quantities are total events required, not participants per arm. The illustration is not the original trial design calculation: the registry record does not report the trial’s original sample-size assumptions or justification. It also is not observed power. It is a planning aid showing how the event requirement changes under the stated hypothetical assumptions.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: a narrower interval indicates less statistical uncertainty about the parameter than a wider interval, under the same method and assumptions. The primary median PFS estimate for durvalumab is 14.0 months, with an interval from 10.9 to 18.0 months. The placebo median is 6.5 months, with an interval from 5.4 to 13.8 months. The intervals overlap, but overlap between separate group-specific intervals is not itself the formal test of the treatment comparison. The registry’s reported comparison is the hazard ratio and its confidence interval.

The primary hazard ratio is 0.75, and its 95% confidence interval ranges from 0.578 to 0.986. This interval includes values indicating a more pronounced relative difference as well as values close to no difference. Its upper endpoint remains below 1, though close to it. The associated p-value is 0.038. Together, these quantities indicate evidence against a hazard ratio of 1 under the reported analysis, while showing that the precise magnitude remains uncertain.

For the secondary intent-to-treat PFS result, the reported hazard ratio is 0.74, with a 95% confidence interval from 0.575 to 0.966. Its endpoints also indicate uncertainty in the magnitude, and the interval remains below 1. The estimates are close in direction and size to the primary result, but the populations differ.

Confidence intervals are not guarantees that the true value lies inside the particular reported range, nor do they capture all sources of uncertainty. They do not address possible bias, limitations in endpoint measurement, missing-data handling or the effects of multiple statistical comparisons. The record does not report all those methodological details. Precision should therefore be understood as statistical uncertainty around the reported estimates, not as a complete assessment of certainty about the trial’s broader implications.

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 illustration is based on time-to-event comparisons, so its figures are total events across the two arms, not participants per arm. Its assumptions are a two-sided significance level of 0.05, equal allocation between the two arms and a normal approximation. The effect being targeted is expressed as a stated fraction of the observed effect. The displayed scenarios consider 100%, 75% and 50% of that observed effect.

For each scenario, the 80% power column gives the total number of events that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect, if that effect and the stated assumptions applied. The 90% power column gives the corresponding event requirement for a 90% chance. Power is a design-stage probability defined under a statistical model; it is not the probability that the observed finding is correct.

Smaller effects are harder to distinguish from random variation, so the planning calculation requires more events when the effect to detect is reduced. The figures are event counts, not a direct count of participants, because participants can have different follow-up times and not all will experience the event during follow-up. The number of participants needed to accrue a target number of events depends on event occurrence and follow-up, details that this illustration does not estimate.

This is not observed power. It is a planning illustration computed from the observed effect, rather than the trial’s original design calculation. The original design assumptions and sample-size justification are not reported in the registry record. The equal-allocation assumption in the illustration should not be taken as a description of the trial’s actual allocation.

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 = 0.750, so ln(HR) = -0.2877.
2. d = 4 × (1.96 + 0.842)² / [ln(0.750)]² = 379.4, rounded up to 380 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 <- 0.75                              # 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(3706690)
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 = 380 (80% power), 508 (90% power)
 75% of observed effect: events = 675 (80% power), 903 (90% power)
 50% of observed effect: events = 1,518 (80% power), 2,032 (90% power)
Simulated power with 380 events: 0.788 (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 575 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 407 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 <- 6.5          # control-arm median, months (converted from the posted unit)
hr          <- 0.75          # 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: 378         p (1-sided)   0.0001
 Events: 171        ~HR at bound   0.5669
   Month: 16    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.75   0.0338
   IA 2: 67%                   Z   2.5114
      N: 576         p (1-sided)   0.0060
 Events: 342        ~HR at bound   0.7621
   Month: 25    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.75   0.5603
       Final                   Z   1.9930
      N: 576         p (1-sided)   0.0231
 Events: 513        ~HR at bound   0.8386
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.75   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 comparison is the Log Rank hazard ratio of 0.75, with a 95% confidence interval from 0.578 to 0.986 and p = 0.038. The posted results include this sponsor analysis, and no discrepancy between the reported result and the displayed result is flagged. Accordingly, the sponsor’s own analysis is the relevant reported comparison; a simple recalculation from summary statistics would not replace it.

A hazard ratio and p-value cannot generally be reconstructed exactly from group medians and their confidence intervals. The Log Rank comparison uses event-time information across follow-up, whereas medians compress each group’s estimated time distribution into a single point. A calculation based only on those summaries would not reproduce the participant-level analysis or its handling of censoring.

The same distinction applies to the secondary intent-to-treat result: the sponsor reports a hazard ratio of 0.74, with a 95% confidence interval from 0.575 to 0.966 and p = 0.026. These are the reported time-to-event analyses. Any planning illustration derived from an observed effect serves a different purpose and should not be mistaken for a second analysis of the trial outcome.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses or endpoints are tested. Even if each test uses a conventional threshold, repeated testing can increase the overall chance of at least one result appearing statistically notable by chance. This is a general statistical principle. A trial can address it through a prespecified testing sequence, adjustment procedures or a clearly defined distinction between confirmatory and exploratory analyses.

The registry lists multiple secondary outcomes, while the primary outcome is PFS in the modified intent-to-treat set. The registry record does not report a multiplicity adjustment, a testing hierarchy or another strategy governing interpretation across the endpoints. Consequently, the reported secondary p-values, where available, should not automatically be read as if they had the same confirmatory status as the primary comparison. The record does not provide enough information to determine whether a strategy was specified elsewhere in the study documentation.

Missing-data and censoring details also affect the interpretation of time-to-event results. Kaplan-Meier estimation can use participants’ observed follow-up when an event is not recorded, but its interpretation depends on appropriate censoring assumptions. The registry provides the endpoint definition, scan schedule and analysis cutoff, but detailed rules for censoring, missed scans and other missing assessments are not reported in the registry record. It is therefore not possible to assess those procedures from the posted information alone.

The primary analysis population is defined as randomized participants without sensitizing EGFR mutations or ALK rearrangements. The separate secondary PFS result uses the intent-to-treat population. These definitions are reported, but the registry does not give a complete accounting of all exclusions, missing observations or analysis-set construction beyond the stated population descriptions.

The original sample-size rationale, the trial’s original power assumptions, interim-analysis procedures and a full statistical analysis plan are not reported in the registry record. Their absence from the posted information should not be filled in by inference. The planning illustration based on the observed effect is not evidence about what the trial originally planned.

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: radiation pneumonitis (9.0%), pneumonia (7.7%), pneumonitis (5.5%), pneumonia bacterial (2.2%), covid-19 (1.8%).

The registry reports serious adverse event counts for the groups in a safety listing. For durvalumab, 104 participants were affected among 271 at risk; for placebo, 45 were affected among 134 at risk. These are the registry’s affected and at-risk counts. They should be read in their recorded safety context, rather than assumed to use the same populations as the primary PFS analysis.

The most frequently listed serious adverse event terms include radiation pneumonitis at 9.0%, pneumonia at 7.7% and pneumonitis at 5.5%. Other listed terms are pneumonia bacterial at 2.2%, COVID-19 at 1.8% and hepatic function abnormal at 1.5%. These percentages describe the posted terms; they do not establish that a particular event was caused by study treatment.

The registry also lists deaths as 143 for durvalumab and 75 for placebo. The field is reported as deaths, without further detail in the registry record about attribution or cause. Counts and event-term percentages alone do not capture timing, severity patterns, exposure duration or the full benefit-risk context. They should be interpreted as descriptive registry safety information, not as a causal comparison.

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

The posted primary result shows a difference in estimated PFS between durvalumab and placebo in the modified intent-to-treat population. The group medians, hazard ratio, confidence interval and p-value describe the comparison under the endpoint definition and the reported analysis. The secondary intent-to-treat PFS result has a similar direction. These findings provide statistical evidence about progression or death during the recorded follow-up; they are not a complete account of every outcome relevant to the study.

The result does not mean that every participant in one group had a longer PFS time than every participant in the other group. A median is a population-level summary, and the hazard ratio is a relative time-to-event summary. Individual outcomes vary, and the posted statistics do not predict a particular person’s course. Nor do these statistics alone establish an effect on overall survival, quality of life, symptoms or other outcomes.

The registry lists overall survival and several other outcomes as secondary measures, but full results for all those measures are not reported in the registry record. PFS and overall survival are distinct endpoints. A PFS result should not be treated as a substitute for an unreported overall-survival result.

The findings apply to the analysis populations and study context described in the record: locally advanced, unresectable non-small cell lung cancer after definitive platinum-based chemoradiation, with the primary population excluding participants with sensitizing EGFR mutations or ALK rearrangements. The results do not automatically generalize to populations with different characteristics, treatments or clinical settings. They also do not determine the balance of potential benefits and harms for an individual. The posted safety counts are descriptive and do not by themselves establish causation.

19. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint, analysis population and comparison method rather than through a single headline statistic. PFS is a time-to-event outcome with progression and death incorporated into a defined event. Its interpretation depends on the event definition, scan schedule, follow-up and handling of participants without an observed event.

The primary analysis reports both Kaplan-Meier medians and a hazard ratio. These summaries answer related but different questions: medians describe a point in each estimated event-time distribution, while the hazard ratio compares event hazards across follow-up. Confidence intervals are essential because they show the uncertainty around both kinds of estimate. The primary hazard-ratio interval remains below the null value of 1, but its upper endpoint is close to 1, making the precision and scale of the estimate important to discuss alongside its p-value.

The separate intent-to-treat PFS result also demonstrates how analysis populations matter. Its direction is similar to the primary finding, but it is a distinct analysis with a different population definition. That distinction should remain visible rather than blending the estimates into one result.

Finally, the registry record separates reported outcomes from planning illustrations. Event-based sample-size planning depends on assumptions about the effect to detect and the number of events required; it is not observed power and does not reveal the trial’s original design rationale. Careful reading therefore requires distinguishing the sponsor’s outcome analysis, the scope of posted secondary results, and hypothetical planning calculations.

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.

A key limitation is that the primary PFS population is modified intent-to-treat rather than all randomized participants: it excludes participants with sensitizing EGFR mutations or ALK rearrangements. The posted result therefore answers the primary question for that specified population. The intent-to-treat PFS analysis is reported separately, but it does not change the primary population definition.

PFS depends on the timing and assessment of progression. Scans were scheduled at screening, every 8 weeks ±1 week up to 48 weeks, then every 12 weeks ±1 week thereafter until confirmed progression. The registry reports blinded independent central review and the data cutoff, but detailed information about missing scans, censoring rules and sensitivity analyses is not reported in the registry record. Those details matter when interpreting an endpoint whose event time is established through repeated assessments.

The hazard ratio is a compact summary of the time-to-event comparison. The registry does not report diagnostics for whether the relative hazard is stable over follow-up, so the estimate should not be assumed to describe every time period equally. The full shape of the survival curves and the timing of any changes are not conveyed by the medians and hazard ratio alone.

The posted information includes only some secondary results, while many secondary outcomes are listed without result details. A multiplicity strategy is not reported. This limits how strongly secondary findings can be interpreted as confirmatory evidence. In addition, original trial sample-size assumptions, interim-analysis procedures and the full statistical plan are not reported in the registry record. These omissions restrict assessment of the design rationale and some analytic choices; they do not establish that such procedures were absent from other study documents.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Durvalumab as Consolidation Therapy in Non-Small Cell Lung Cancer Patients — NCT03706690.
• Registry record last updated 2026-08-06; status last verified 2026-08.
• Results first posted 2025-02-12.
• 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

NCT03706690 is a Phase III randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by AstraZeneca. It evaluates durvalumab as consolidation therapy after definitive platinum-based chemoradiation in locally advanced, unresectable non-small cell lung cancer. The registry lists enrollment of 407 and status as active, not recruiting.

The primary endpoint is PFS by blinded independent central review in the modified intent-to-treat set, defined to exclude participants with sensitizing EGFR mutations or ALK rearrangements. The reported primary hazard ratio is 0.75, with a 95% confidence interval from 0.578 to 0.986 and p = 0.038. The registry also reports a secondary intent-to-treat PFS comparison with a hazard ratio of 0.74 and p = 0.026.

The primary completion date is 2024-06-23, and the reported assessment uses a 23-Jun-2024 data cutoff. The record lists additional secondary outcomes and safety information, but results and analysis details for every listed outcome are not reported in the registry record.