Durvalumab Treatment in Combination With Chemotherapy and Bevacizumab, Followed by Maintenance Durvalumab, Bevacizumab and Olaparib Treatment in Advanced Ovarian Cancer Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Durvalumab Treatment in Combination With Chemotherapy and Bevacizumab, Followed by Maintenance Durvalumab, Bevacizumab and Olaparib Treatment in Advanced Ovarian Cancer Patients (NCT03737643), a randomized phase 3 study. The primary outcome is Progression-free Survival (PFS) by Investigator Assessment Using Modified RECIST 1.1 - Full Analysis Set.

2. Clinical Question

The clinical question is about the time until progression or death, not simply whether a tumor response occurred. The registry describes assessments beginning at baseline and continuing after chemotherapy, with scheduled follow-up during the study. The primary outcome is a time-to-event measure, so its interpretation depends on both the event pattern and the period of observation. It should be read alongside the hazard ratio and confidence interval, rather than from the median alone.

3. Trial Design

DUO-O is a Phase III, randomized, double-blind, placebo-controlled, multicentre study with a parallel-group design. The registry lists quadruple masking. The study evaluates durvalumab in combination with platinum-based chemotherapy and bevacizumab, followed by maintenance treatment. The listed interventions include carboplatin plus paclitaxel, bevacizumab, durvalumab, olaparib and matching placebos.

The registry describes three global non-tBRCAm treatment groups: standard of care with placebo, standard of care plus durvalumab with olaparib placebo during maintenance, and standard of care plus durvalumab and olaparib during maintenance. A separate tBRCAm cohort is also described. In that cohort, bevacizumab is optional according to local practice. The primary comparison is the global non-tBRCAm standard-of-care group against the global non-tBRCAm group receiving durvalumab and olaparib. The durvalumab-without-olaparib comparison is reported separately as a secondary endpoint.

The primary endpoint is investigator-assessed progression-free survival using modified RECIST 1.1. The reported Full Analysis Set includes randomized patients in the global enrolment, with the registry specifying how China participants are included. China results are also presented as a distinct cohort. The primary outcome timeframe describes assessment from baseline, within 3 weeks of the last chemotherapy dose, then every 12 weeks for 3 years and thereafter every 24 weeks. The record gives differing analysis cutoffs for the global and China cohorts.

The registry lists enrollment of 1407 and status as active, not recruiting. The study start and primary completion dates are recorded, but those dates do not by themselves describe how long any individual participant was followed. Details of the trial's original sample-size justification, randomization procedure, and full statistical analysis plan 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.

Before assignment: This study planned to allocate/randomise approximately 1254 patients with newly-diagnosed advanced ovarian cancer patients. In addition, a China cohort of approximately 120 non-tBRCAm patients with newly-diagnosed advanced ovarian cancer patients was planned to be randomised.

Only the first 6 of 7 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) consisting of all patients randomised as part of global enrolment including patients from China who were randomised before the global recruitment was closed (up to and including 17 June 2021). China FAS includes all patients who were randomised at sites in China.

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: 1 patient in the China cohort is also included in the Global cohort. Patient is randomised to SoC+Durvalumab.

Only the first 6 of 8 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival (PFS) by Investigator Assessment Using Modified RECIST 1.1 - Full Analysis Set, measured over At baseline, within 3 weeks of last dose of chemotherapy, then every 12 weeks for 3 years and thereafter every 24 weeks. Assessed until primary analysis - (05DEC2022 for Global cohort, 17MAR2025 for China cohort) - upto 46 months.

Progression-free survival is a time-to-event endpoint: it measures the time until disease progression or death, according to the endpoint definition and assessment process. In this study, progression was evaluated by investigators using modified RECIST 1.1. The registry describes repeated assessments during follow-up rather than a single evaluation at one fixed visit.

Time-to-event outcomes are useful when the timing of an event matters and participants may be followed for different lengths of time. They can use information from participants who have not yet experienced the event by the analysis cutoff, provided their follow-up is appropriately handled. Such observations are generally censored: the event time is not known beyond the last relevant observation. This is a general feature of survival analysis, not a claim about a particular participant in this trial.

The registry reports median progression-free survival in months with 95% confidence intervals, as well as hazard ratios for comparisons. The median describes the time by which the estimated event-free proportion has reached the midpoint; it does not describe every participant's experience. The hazard ratio compares event rates over follow-up under the model or analysis used. It is not a ratio of medians, and a hazard ratio should not be interpreted as a direct difference in months.

Progression-free survival is used because it captures both disease progression and death within a defined follow-up framework. It is distinct from overall survival, response rate, and duration of response. It also depends on the definition and timing of assessments, which matter when progression is established through scheduled investigator evaluations.

7. Results Posted in the Registry

• Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D+O: hazard ratio 0.63 (95% CI 0.52–0.76), reported p < 0.001 (as reported in the registry).
• China Non-tBRCAm: SoC vs China Non-tBRCAm: SoC+D+O: hazard ratio 0.47 (95% CI 0.25–0.86) (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) by Investigator Assessment Using Modified RECIST 1.1 - Full Analysis 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:
  • Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D: hazard ratio 0.87 (95% CI 0.74–1.03), reported p = 0.113 (as reported in the registry).
  • China Non-tBRCAm: SoC vs China Non-tBRCAm: SoC+D: hazard ratio 0.80 (95% CI 0.45–1.40) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between China Non-tBRCAm: SoC vs China Non-tBRCAm: SoC+D and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival - Full Analysis 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:
  • Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D+O: hazard ratio 0.92 (95% CI 0.75–1.11), reported p = 0.378 (as reported in the registry).
  • Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D: hazard ratio 0.97 (95% CI 0.80–1.18) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D+O and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D and the control. The interval gives the range of effects that remain compatible with the data.

Overall Survival - (Full Analysis Set, HRD-positive)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D+O: hazard ratio 0.80 (95% CI 0.54–1.18) (as reported in the registry).
  • China Non-tBRCAm: SoC vs China Non-tBRCAm: SoC+D+O: hazard ratio 0.41 (95% CI 0.12–1.30) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Global Non-tBRCAm: SoC vs Global Non-tBRCAm: SoC+D+O and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between China Non-tBRCAm: SoC vs China Non-tBRCAm: SoC+D+O and the control. The interval gives the range of effects that remain compatible with the data.

The registry includes secondary measures of progression-free survival, overall survival, PFS2, objective response rate and duration of objective response. These add information about disease control, subsequent progression, response and survival, but they do not answer exactly the same question as the primary investigator-assessed progression-free survival comparison. Their analysis populations and follow-up periods also differ in some cases.

Across the posted secondary estimates, precision is uneven. Some intervals include the no-difference value for a hazard ratio, while other estimates are less precise or have limits that are not reported. The overall pattern is therefore not a single uniform signal across every endpoint and cohort. A point estimate in a favorable direction is not, by itself, sufficient evidence of a reproducible effect, especially when its interval is broad or a p-value is absent.

The primary result is the prespecified focus identified in the registry description. Secondary outcomes can support, qualify or add context to that result, but they should not be combined informally into one overall conclusion. Overall survival is particularly distinct from progression-free survival because it concerns death rather than progression or death; response outcomes describe still different features of the disease course.

Multiple secondary outcomes and subgroup comparisons create a multiplicity issue: the more inferential tests considered, the greater the chance that some appear noteworthy by chance. Adjustments or a prespecified testing hierarchy can address this concern, but a complete procedure is not reported in the registry record. Consequently, unadjusted secondary findings carry less confirmatory weight than the primary comparison and should be read as supporting or exploratory evidence unless their formal testing status is reported elsewhere in the registry record.

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

• Progression-free Survival (PFS) by Investigator Assessment Using Modified RECIST 1.1 - Full Analysis Set
• Overall Survival - Full Analysis Set
• Overall Survival - (Full Analysis Set, HRD-positive)
• Time to Second Progression or Death Based on Local Standard Clinical Practice (PFS2) - Full Analysis Set
• Time to Second Progression or Death Based on Local Standard Clinical Practice (PFS2) - (Full Analysis Set, HRD-positive)
• Objective Response Rate Based on Investigator Assessment (Full Analysis Set)
• Objective Response Rate Based on Investigator Assessment (Full Analysis Set, HRD-positive)
• Duration of Objective Response Based on Investigator Assessments (Full Analysis Set)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time-to-event data. The registry reports median progression-free survival and a hazard ratio, with a 95% confidence interval. These summaries answer related but different questions. The median gives a point on the estimated event-time distribution. The hazard ratio summarizes the relative event hazard between groups over the observed follow-up, subject to the assumptions and analysis method used.

What does a hazard ratio describe?

In general, a hazard is the instantaneous rate of an event among participants still being followed and still at risk at a given time. A hazard ratio compares that rate between groups. A value below 1 indicates a lower estimated event hazard in the first-named comparison direction, while a value above 1 indicates a higher estimated hazard. The value is not a probability, a percent change, or a difference in median survival time. If the relative event rate changes over time, one hazard ratio may not fully describe that pattern. The registry record does not report a proportional-hazards diagnostic or a time-varying effect analysis.

Why report a median as well?

The median provides a time-scale summary that many readers can relate to, while the hazard ratio compares event rates using information across follow-up. A median does not show the entire survival curve, and it can be uncertain when few participants remain under observation near the midpoint. For that reason, the confidence interval and the hazard ratio are important companions to the median. The reported medians should not be subtracted to create an unreported treatment effect; that would be a different statistic from the sponsor's analysis.

What is the role of the Log Rank method?

The registry identifies Log Rank as the method for the global primary comparison. In general, the Log Rank test compares event-time patterns between groups while taking account of censoring. It is commonly used in time-to-event analysis. Its interpretation relies on the information available over follow-up and does not itself explain whether an effect is clinically important. The method is not listed for the China primary comparison, so it is not reported in the registry record for that comparison.

The primary comparison also has a reported hazard ratio and confidence interval. The registry does not provide enough detail in the listed results to reconstruct the complete model or test implementation. It does not state in this outcome record whether stratification, covariate adjustment, or other specific modeling choices were used. Those details should not be inferred from the fact that a Log Rank method is named.

Why do confidence intervals matter?

A confidence interval describes the range of values reasonably compatible with the data and the statistical procedure, under its assumptions. It reflects sampling uncertainty, not the range of outcomes for individual participants. A narrower interval indicates greater precision than a wider one, but precision does not resolve possible bias or shortcomings in measurement, follow-up, or analysis. A 95% confidence interval is a procedure with a long-run coverage interpretation; it is not a statement that the particular interval has a 95% probability of containing the true effect.

The primary global interval for the hazard ratio is entirely below 1, while the reported China interval is also below 1 but wider. In general, whether an interval excludes 1 is a useful way to assess the compatibility of the estimate with no relative hazard difference. It should be considered with the p-value where one is reported, the analysis population, and the design. A p-value is not the probability that the null hypothesis is true, nor a measure of effect size.

What does the analysis population mean?

The registry defines the primary Full Analysis Set as randomized patients in the global enrolment, including patients from China randomized before global recruitment closed. It separately defines the China Full Analysis Set as patients randomized at sites in China. Analysis populations matter because estimates describe the participants included under those definitions. They should not be assumed to include every randomized participant in every cohort. Detailed handling of missing outcome assessments, withdrawals, and deviations is not reported in the registry record.

In general, over-dispersion is a concern for count outcomes when variability exceeds what a simple model assumes. It is not the primary issue for this time-to-event endpoint, for which censoring, event definition, follow-up, and the validity of the hazard-ratio summary are more central. This general distinction does not imply that any particular diagnostic was performed in DUO-O.

The registry also posts secondary time-to-event outcomes and response outcomes. Each requires interpretation according to its own definition and analysis population. Multiple outcomes and comparisons can increase the chance of a seemingly notable result arising by chance if many tests are interpreted without adjustment. The registry record does not report a complete multiplicity procedure, so the degree of confirmatory status for the full collection of analyses is not reported in the registry record.

11. Confidence Intervals and Precision

The global primary hazard ratio is 0.63, with a 95% confidence interval from 0.52 to 0.76. The interval is wholly below 1, and its endpoints indicate the range of relative hazard values compatible with the analysis at the stated confidence level. The point estimate is more informative when read with that range than when treated as an exact effect.

The China primary estimate is 0.47, with a 95% confidence interval from 0.25 to 0.86. This interval is wider than the global interval, indicating less precision in the China estimate. A wider interval means the data are compatible with a broader range of relative hazard values; it does not by itself show that the underlying effect differs between cohorts. The registry does not report a formal interaction test comparing cohort effects.

Confidence intervals describe sampling uncertainty under the analysis assumptions. They do not cover every source of uncertainty. For example, they do not account automatically for possible differences in how outcomes were assessed, missing data, or whether the model is appropriate. Those considerations require design and analysis details that are not all reported in the registry record.

The medians are also estimates, and the registry reports confidence intervals for them. Some upper confidence limits are not reported in the record. In those cases, the missing limit should not be interpreted as evidence of no uncertainty or as a complete interval. The median and hazard ratio summarize distinct aspects of follow-up, and their confidence intervals should not be compared as though they represented the same quantity.

Precision is not the same as clinical importance. An estimate can be precise yet have limited practical importance, or be imprecise despite a potentially important point estimate. The confidence intervals help show what effect sizes are compatible with the posted data, but the registry record alone does not define a threshold for clinical importance.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial's original design calculations. For these time-to-event comparisons, the values are total event counts, not participants per arm. The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The registry record does not report the trial's original sample-size justification or its design assumptions.

The 80% power column represents the event count estimated to give an 80% chance of detecting the specified effect under those planning assumptions, if that effect and assumptions were correct. The 90% power column represents a higher target chance of detecting that effect, and therefore generally requires more events. These are design-planning quantities, not findings about the chance that the completed trial detected an effect.

Rows for fractions of the observed effect show how the planning requirement changes when the target effect is smaller. A smaller effect is harder to distinguish from random variation and needs more events to reach the same target power. The displayed curve illustrates the relationship between the assumed effect and the event requirement; it is not a second trial result. No participant-per-arm figure should be read from these time-to-event event counts without additional assumptions about event occurrence and follow-up. This is not observed power.

13. How the Sample Size Is Derived

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

Formula

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.630, so ln(HR) = -0.4620.
2. d = 4 × (1.96 + 0.842)² / [ln(0.630)]² = 147.1, rounded up to 148 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 <- 0.63                              # 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(3737643)
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 = 148 (80% power), 197 (90% power)
 75% of observed effect: events = 262 (80% power), 351 (90% power)
 50% of observed effect: events = 589 (80% power), 788 (90% power)
Simulated power with 148 events: 0.819 (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 322 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 1,407 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 <- 19.3          # control-arm median, months (converted from the posted unit)
hr          <- 0.63          # 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: 282         p (1-sided)   0.0001
  Events: 67        ~HR at bound   0.4016
   Month: 21    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.63   0.0338
   IA 2: 67%                   Z   2.5114
      N: 322         p (1-sided)   0.0060
 Events: 133        ~HR at bound   0.6462
   Month: 34    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.63   0.5603
       Final                   Z   1.9930
      N: 322         p (1-sided)   0.0231
 Events: 199        ~HR at bound   0.7536
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.63   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 primary hazard ratio, confidence interval and p-value are reported in the registry record as the sponsor's analysis. The record identifies the Log Rank method for the global primary comparison and labels the analysis as superiority. No discrepancy is flagged between the posted estimate and the analysis recorded as reported.

Recalculation from summary statistics, when available, is an unadjusted check and is not a replacement for the sponsor's analysis. In this case, the primary interpretation should follow the sponsor-reported hazard ratio and confidence interval rather than treating a summary-statistic calculation as an alternative adjusted result. The registry record does not provide the individual participant data needed to reproduce the full analysis independently.

The China comparison has a reported hazard ratio and confidence interval, but its method and p-value are not reported in the registry record. Accordingly, the global primary method and p-value should not be attributed to the China result. The absence of those details does not invalidate the estimate, but it limits the amount of analysis that can be checked from the registry information alone.

16. Multiplicity, Missing Data and Analysis Populations

The registry record lists 24 outcome measures and 44 analyses, with multiple endpoints, treatment comparisons and analysis populations. Considering many statistical tests raises the general risk of false-positive findings: even when there is no underlying difference for a particular question, a large collection of tests can produce some small p-values by chance. This is why trials often specify which endpoint is primary and describe a testing hierarchy or multiplicity adjustment.

The primary progression-free survival comparison is clearly identified, and its reported p-value is available. However, a complete multiplicity strategy covering the primary and secondary endpoints, cohorts, and treatment comparisons is not reported in the registry record. It is therefore not possible from the posted record alone to determine which secondary tests were controlled for family-wise error, whether a gatekeeping procedure was used, or which analyses were intended to be formally confirmatory. These details should not be guessed.

Missing data are also important for time-to-event outcomes. Participants may stop attending assessments, withdraw, or reach the analysis cutoff without a recorded event. General survival methods can account for follow-up that ends before an event through censoring, but the validity of that approach depends on assumptions about why follow-up ended. The detailed rules for censoring, handling missed assessments, and addressing other missing outcome information are not reported in the registry record.

The analysis populations are described at a high level. The primary Full Analysis Set includes randomized patients in the defined global enrolment, and the record specifies a separate China cohort. The registry does not fully report the handling of all randomized participants across each endpoint or explain the missing-data strategy for each analysis. It also does not report a full account of protocol deviations or sensitivity analyses in the outcome information presented.

These gaps do not change the reported estimates, but they limit independent evaluation of their robustness and the strength of claims across many outcomes. The primary result can be described as reported, while broader claims should remain cautious unless the missing analysis details are available in the registry record.

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: anaemia (12.2%), covid-19 (7.3%), intestinal obstruction (7.3%), pneumonia (7.0%), febrile neutropenia (5.9%).

The serious adverse event figures are counts of participants affected within the listed safety groups and the corresponding numbers at risk. For example, in the global non-tBRCAm standard-of-care group, 132 of 376 participants at risk were reported with serious adverse events. In the global non-tBRCAm group receiving standard of care plus durvalumab and olaparib, the corresponding figures are 152 of 378. The registry also reports deaths and counts for other adverse events; these are separate measures and should not be combined.

The most frequently listed serious adverse event terms include anaemia at 12.2%, Covid-19 at 7.3%, intestinal obstruction at 7.3%, pneumonia at 7.0%, febrile neutropenia at 5.9%, and hepatic function abnormal at 5.0%. These term-specific percentages do not describe every serious adverse event or establish that a treatment caused an event. Participants may experience more than one event, and the registry excerpt does not provide all details needed to interpret event duration, severity grading, or attribution.

Safety counts should be considered alongside the treatment groups, population definitions and exposure period. Differences in counts alone do not establish a causal difference in risk, particularly without a comparative safety analysis and fuller follow-up information. Detailed definitions and handling of safety data beyond the posted figures are not reported in the registry record.

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

The primary result describes a lower estimated progression-or-death hazard in the global non-tBRCAm group receiving durvalumab and olaparib with standard-of-care treatment, compared with the standard-of-care group, under the sponsor-reported analysis. The confidence interval gives a measure of statistical precision, and the reported p-value describes compatibility with a no-difference hypothesis under the analysis. Together, these statistics support a description of the posted comparison, not a guarantee of a particular outcome for an individual.

The estimate does not mean that every participant experienced a longer period without progression, or that the hazard ratio is the amount of time gained. It is not a direct comparison of medians. Nor does a p-value tell the probability that the treatment effect is real. A statistical result must be interpreted in light of the trial design, outcome definition, analysis population, follow-up and uncertainties.

The result is specific to the reported population and regimen. It should not automatically be extended to the tBRCAm cohort, other cancer populations, or treatment schedules that differ from the study. The primary comparison is in the global non-tBRCAm group; the registry reports a separate China cohort estimate with less precision and does not report its p-value or analysis method.

The primary endpoint is progression-free survival, not overall survival. The secondary outcomes provide additional evidence but have varying precision and incomplete reported multiplicity details. The record also does not provide all information needed to assess missing data, model assumptions, or the full statistical plan. Thus the posted result is informative about the designated endpoint while leaving important questions about broader generalization and robustness open.

No medical recommendation follows from these statistics. Treatment decisions require clinical context and a broader assessment of benefits, harms and individual circumstances; the registry results alone do not supply that assessment.

19. Why This Trial Matters Statistically

DUO-O illustrates several central issues in clinical trial statistics. First, the primary endpoint is time-to-event, so interpretation requires more than comparing two median values. The hazard ratio summarizes event rates across follow-up, while the medians give a complementary time-based description. Reading both alongside confidence intervals helps prevent a point estimate from being mistaken for an exact or universal effect.

Second, the trial contains multiple treatment groups, cohorts and endpoints. The primary comparison has a clearly identified role, while separate analyses examine durvalumab without olaparib and outcomes such as overall survival and response. That structure makes multiplicity and the hierarchy of evidence important. Without a fully reported testing strategy, statistical significance across secondary results should not be treated as equivalent to confirmation on the primary endpoint.

Third, the global and China results demonstrate why estimates must be read with their precision. A point estimate alone does not show how much uncertainty surrounds it, and cohort-specific estimates should not be compared as though their differences were formally tested. The record does not report an interaction analysis for those cohorts.

Finally, the planning illustrations distinguish event requirements from participant counts and from observed power. They show how assumptions about target effect and desired power affect planning, but they are not the original trial design calculation. Together, these features make the study a useful case for separating the sponsor's reported analysis, statistical uncertainty, secondary evidence and planning scenarios.

20. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the complete statistical analysis plan, including all details of the primary model, its assumptions, or the full multiplicity procedure. Although Log Rank is named for the global primary comparison, the method is not reported for the China comparison. The record also does not report a proportional-hazards assessment, which would help assess whether a single hazard ratio adequately summarizes the comparison over time.

Detailed methods for missing assessments, censoring, withdrawals and protocol deviations are not reported in the registry outcome information. These matter for time-to-event analysis because follow-up can end before progression or death is observed. The reported confidence intervals reflect statistical uncertainty under the analysis but do not address every possible source of bias or model misfit.

Some reported median confidence limits are incomplete, and some secondary comparisons lack p-values or named methods. The registry has multiple endpoints and analyses, yet the full role of each test in a confirmatory hierarchy is not reported. These limitations particularly affect interpretation of secondary and subgroup results, rather than changing the numerical primary estimate.

The primary comparison concerns the global non-tBRCAm population and a specific treatment sequence. Results should not be assumed to apply equally to the tBRCAm cohort or to other settings. The registry describes an optional use of bevacizumab in the tBRCAm cohort, and that is not the primary comparison. The posted record also cannot establish whether differences in cohort estimates reflect treatment-effect variation or sampling uncertainty; a formal comparison between cohorts is not reported.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Durvalumab Treatment in Combination With Chemotherapy and Bevacizumab, Followed by Maintenance Durvalumab, Bevacizumab and Olaparib Treatment in Advanced Ovarian Cancer Patients — NCT03737643.
• Registry record last updated 2026-07-07; status last verified 2026-07.
• Results first posted 2026-06-09.
• 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

DUO-O is a Phase III randomized, double-blind, placebo-controlled, multicentre study in newly diagnosed advanced ovarian cancer. Its primary outcome is investigator-assessed progression-free survival using modified RECIST 1.1. The registry reports the global non-tBRCAm comparison of standard of care with standard of care plus durvalumab and olaparib, with median estimates, a hazard ratio, a confidence interval and a p-value.

The primary global estimate is reported as a hazard ratio of 0.63 with a 95% confidence interval from 0.52 to 0.76 and p < 0.001. The China cohort has a separately reported hazard ratio of 0.47 with a 95% confidence interval from 0.25 to 0.86; its p-value and method are not reported in the registry record. Secondary outcomes cover survival, progression and response. Multiplicity, detailed missing-data procedures and the complete analysis plan are not reported in the registry record.