A Study to Examine Olaparib Maintenance Retreatment in Patients With Epithelial Ovarian Cancer.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Examine Olaparib Maintenance Retreatment in Patients With Epithelial Ovarian Cancer. (NCT03106987), a randomized phase 3 study. The primary outcome is Efficacy: Progression-free Survival (PFS).

2. Clinical Question

3. Trial Design

This was a Phase IIIb, randomised, double-blind, placebo-controlled, multicentre, parallel-group study of olaparib maintenance retreatment. The registry reports an enrollment of 220 and lists epithelial ovarian cancer as the condition. The study status is completed. The recorded start date is 2017-06-08 and the primary completion date is 2021-02-15.

Participants were assigned to olaparib or matching placebo. Both were described as 300mg tablets taken orally twice daily continuously. The double-blind design means that treatment assignment was intended to be masked; details about how masking was maintained or assessed are not reported in the registry record. The allocation ratio and the method used to generate or conceal the random sequence are not reported in the registry record.

The primary outcome was progression-free survival (PFS), assessed using RECIST 1.1 and reported as a median with a 95% confidence interval. Assessments were scheduled at randomization and every 12 weeks (+/- 7 days) until investigator-assessed objective radiological progression or other discontinuation criteria, with assessment listed as extending up to 3.8 years. The registry reports results for BRCA1/2-positive and BRCA1/2-negative groups separately.

Listed secondary outcomes include overall survival, time to progression by GCIG criteria, time to subsequent treatments, time to treatment discontinuation, health-related quality of life and adverse events. The registry record describes nine outcome measures and two analyses. Details of the original sample-size justification, planned interim analyses, allocation ratio, and the 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: Patients were randomised into 1 of 2 cohorts depending on their known BRCA1/2 status (BRCA1/2 +ve or BRCA1/2-ve). Within each cohort, patients were randomised in a 2 Olaparib:1 placebo ratio. Randomisation was stratified by prior use of bevacizumab and number of prior regimens of platinum-containing chemotherapy.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) consisted of all randomised patients analysed on an intent-to-treat (ITT) basis

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: Full analysis set (FAS) consisted of all randomised patients analysed on an intent-to-treat (ITT) basis.

6. Primary Endpoint

The registry lists the primary outcome as Efficacy: Progression-free Survival (PFS), measured over At randomization visit and at every 12 weeks (+/- 7 days) until objective radiological disease progression as determined by the investigator or other discontinuation criteria are met (assessed upto 3.8 years).

Progression-free survival measures the time from randomisation until investigator-assessed objective radiological disease progression or death from any cause in the absence of progression. The registry defines progression according to RECIST 1.1. Its description includes a specified increase in the sum of target-lesion diameters, progression of a non-target lesion, or a new lesion. Patients without recorded progression or death at the analysis were censored at the latest date of an evaluable RECIST assessment.

PFS is a time-to-event endpoint: it incorporates both whether an event occurred and how long participants remained event-free during follow-up. It is used in trials where progression is an important outcome and may be observed before overall survival is fully established. That is a general reason for using PFS, not a claim about the choice made in this trial; the registry’s rationale for selecting the primary endpoint is not reported in the registry record.

The registry reports median PFS and 95% confidence intervals for each treatment group within the BRCA1/2 subgroups. It also reports a sponsor analysis comparing time-to-event outcomes with hazard ratios. The median and hazard ratio describe different aspects of the event-time data, so they should be read together rather than treated as interchangeable summaries.

7. Results Posted in the Registry

• Olaparib (BRCA1/2 +ve) vs Placebo (BRCA1/2 +ve): hazard ratio 0.57 (95% CI 0.37–0.87), reported p = 0.022 (as reported in the registry).
• Olaparib (BRCA1/2 -ve) vs Placebo (BRCA1/2 -ve): hazard ratio 0.43 (95% CI 0.26–0.71), reported p = 0.002 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Efficacy: Change From Baseline in Health-related Quality of Life (HRQoL)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Olaparib (BRCA1/2 +ve): mean -1.27 versus 1.67 on control; difference -2.94 (95% CI -4.99 to -0.89), standardized effect d = -0.62; z-test p = 0.005.
  • Olaparib (BRCA1/2 -ve): mean -2.08 versus 1.67 on control; difference -3.75 (95% CI -5.85 to -1.65), standardized effect d = -0.78; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Olaparib (BRCA1/2 +ve) 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 mean is statistically lower for Olaparib (BRCA1/2 -ve) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The listed secondary outcomes broaden the assessment beyond progression-free survival. They include overall survival, time to progression under GCIG criteria, time to first and second subsequent treatment, time to study treatment discontinuation, health-related quality of life, and adverse-event measures. Together, these outcomes address later clinical events, treatment course, reported quality of life and safety, but they are not interchangeable with the primary PFS endpoint.

The posted secondary information is less complete than the primary comparison. Health-related quality-of-life results are available as mean changes, with unadjusted recalculated comparisons, while sponsor-reported analyses for that outcome are not listed. Numerical results for the other listed secondary outcomes are not reported in the registry record in the information available for these analyses. The registry lists eight secondary outcomes and nine outcome measures overall.

Secondary findings can provide context for the primary result, but they do not automatically confirm or contradict it. They may address different outcomes, use different populations or follow-up, and carry different amounts of uncertainty. Because multiple outcomes and comparisons create more opportunities for chance findings, unadjusted secondary results carry less weight than a prespecified primary analysis unless the testing strategy and adjustment for multiplicity are known. The registry record does not report a multiplicity plan for the secondary outcomes.

The overall pattern should therefore be read as a set of distinct pieces of evidence rather than as a single combined verdict. The available secondary results are not enough to characterize every listed outcome or to establish how the primary PFS findings relate to longer-term outcomes.

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

• Efficacy: Overall Survival (OS)
• Efficacy: Time to Progression by Gynecologic Cancer Intergroup (GCIG) Criteria
• Efficacy: Time to First Subsequent Treatment Commencement (TFST)
• Efficacy: Time to Second Subsequent Treatment Commencement (TSST)
• Efficacy: Time to Study Treatment Discontinuation (TDT)
• Efficacy: Change From Baseline in Health-related Quality of Life (HRQoL)
• Number of Patients With Adverse Events (AEs), and Serious Adverse Events (SAEs)
• Number of Patients With Adverse Event of Special Interest (AESI).

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a median-time primary endpoint and a sponsor-reported time-to-event comparison. The medians summarize the observed event-time distributions within each treatment group, while the hazard ratios summarize the relative event rates over follow-up as estimated by the specified analysis. These summaries answer related but different questions.

What does a median PFS represent?

A median is the point in the estimated event-time distribution at which half of the group is estimated to have experienced the event and half has not yet experienced it. In practice, censoring is important: a participant who has not had a recorded progression or death by their last evaluable assessment contributes information up to that time, rather than being treated as if an event occurred then. The registry says such participants were censored at their latest evaluable RECIST assessment.

The median is a useful plain-language summary, but it does not describe the full shape of the event-time distribution. Two groups can have the same median and different patterns at other follow-up times, or different medians while having substantial uncertainty. A confidence interval around a median communicates uncertainty in its estimate; it is not a range containing a fixed proportion of individual participants’ PFS times.

How should the hazard ratio be read?

A hazard ratio compares estimated event rates over time between groups. General interpretation: a value of 1 corresponds to equal estimated rates, a value below 1 to a lower estimated rate in the first group, and a value above 1 to a higher estimated rate in the first group. This interpretation concerns the relative event rate, not an absolute difference in months, the chance that a particular participant will progress, or the fraction of participants who benefit.

The registry reports stratified log-rank analyses for the PFS comparisons. A log-rank method compares event-time experience while accounting for the timing of events and censoring. Stratification means the analysis incorporates strata, but the registry record does not report which factors were used to form them. The hazard ratio is reported by the sponsor; the analysis details needed to assess proportional hazards or other assumptions are not reported in the registry record.

What does a confidence interval add?

A 95% confidence interval conveys the statistical uncertainty around an estimate under the analysis method. In general, it is a procedure that would cover the underlying parameter in 95% of repeated studies conducted under the same assumptions. It is not a statement that there is a 95% probability that the fixed parameter lies in this particular interval. A wider interval indicates less precision than a narrower interval, all else equal.

For a hazard ratio, an interval that includes 1 is compatible with no difference in the relative event rate under the analysis, while an interval excluding 1 indicates that the range of values supported by the interval does not include equal rates. This is a general statistical interpretation. It does not account for multiple testing, subgroup selection, bias or limitations in the analysis plan. Those issues require separate consideration.

Why can censoring and over-dispersion matter?

Censoring is expected in time-to-event analyses when follow-up ends before an event is observed. Such analyses rely on assumptions about the censoring process; general interpretation requires that censoring not systematically conceal different event patterns in ways that distort the comparison. The record describes the censoring rule for PFS but does not provide enough information to evaluate censoring patterns or sensitivity analyses.

Over-dispersion is a general concern when data vary more than a statistical model expects. It can make standard errors and confidence intervals too optimistic if the extra variation is ignored. The posted primary endpoint is analysed as a time-to-event outcome, and the registry does not report an over-dispersion assessment. The term is relevant as a general statistical issue, not as a reported problem in this trial.

The registry describes the primary analysis population as the full analysis set, including all randomised patients analysed on an intent-to-treat basis. This approach generally retains participants in their assigned groups and helps preserve the comparability created by randomisation. The record’s description does not provide all details about exclusions, protocol deviations, or handling of missing outcome assessments. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The PFS estimates have differing degrees of precision, reflected in their confidence intervals. For BRCA1/2-positive participants, the median was 4.3 months for olaparib, with a 95% confidence interval from 2.79 to 5.49 months; for placebo, the median was 2.8 months, with a 95% confidence interval from 2.73 to 4.96 months. The hazard-ratio interval for this comparison runs from 0.372 to 0.868 around the estimate of 0.566.

For BRCA1/2-negative participants, the median was 5.3 months for olaparib, with a 95% confidence interval from 2.89 to 5.55 months; for placebo, the median was 2.8 months, with a 95% confidence interval from 2.79 to 2.89 months. The hazard-ratio interval runs from 0.264 to 0.708 around the estimate of 0.430. The interval widths show that the estimates are not exact; the underlying effect remains uncertain even where the reported interval excludes 1.

Group sizes were 74 and 38 in the BRCA1/2-positive comparison, and 72 and 36 in the BRCA1/2-negative comparison. The unequal subgroup arm sizes and finite numbers of participants contribute to uncertainty, although event counts and detailed follow-up distributions are not reported in the registry record. Confidence intervals quantify sampling uncertainty under the analysis; they do not capture every possible source of uncertainty, such as bias, population differences or choices made in the analysis plan.

As a general principle, a confidence interval for a median and one for a hazard ratio refer to different estimands and should not be compared as if they measured the same quantity. Precision should be considered alongside the study population, endpoint definition and analysis details that are available in the registry record.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For the time-to-event comparisons, the figures are total numbers of events required, not participants per arm. For the health-related quality-of-life comparisons, the figures are participants per arm.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld approach. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the illustrated number of events or participants needed for an 80% chance of detecting the specified effect under those assumptions, if that effect is real. The 90% power column gives the corresponding planning quantity for a 90% chance. These are design concepts, not guarantees about what a particular study will detect. Smaller effects need more participants or events to detect reliably than larger effects, which is why the illustrations include planning for 75% and 50% of the observed effect as well as the full observed effect.

These figures are not observed power. They do not tell whether the trial was adequately powered under its original plan, because that plan is not reported in the registry record. Read them as conditional planning illustrations tied to the posted effect estimates and stated assumptions, not as a reanalysis of the trial’s achieved 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 = 0.566, so ln(HR) = -0.5692.
2. d = 4 × (1.96 + 0.842)² / [ln(0.566)]² = 96.9, rounded up to 97 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 <- 0.566                              # 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(3106987)
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 = 97 (80% power), 130 (90% power)
 75% of observed effect: events = 173 (80% power), 231 (90% power)
 50% of observed effect: events = 388 (80% power), 519 (90% power)
Simulated power with 97 events: 0.770 (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 139 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 220 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 <- 2.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.566          # 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: 74         p (1-sided)   0.0001
  Events: 44        ~HR at bound   0.3252
   Month: 13    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.57   0.0338
   IA 2: 67%                   Z   2.5114
      N: 122         p (1-sided)   0.0060
  Events: 88        ~HR at bound   0.5842
   Month: 21    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.57   0.5603
       Final                   Z   1.9930
      N: 140         p (1-sided)   0.0231
 Events: 131        ~HR at bound   0.7059
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.57   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

For the primary time-to-event comparisons, the sponsor’s reported analyses take precedence over any simple re-calculation from posted summary statistics. The registry reports stratified log-rank hazard ratios of 0.566 for the BRCA1/2-positive comparison and 0.430 for the BRCA1/2-negative comparison, with their 95% confidence intervals and p-values. These are the analyses to use when describing the posted primary comparisons.

The registry record does not flag a discrepancy between the posted sponsor results and the available summary data. The primary comparisons are therefore presented as reported, rather than replaced by an unadjusted reconstruction. A summary-statistic calculation would not recreate the underlying time-to-event analysis, which uses event timing and censoring information not contained in the medians alone.

The health-related quality-of-life comparisons have recalculated unadjusted estimates, but no corresponding sponsor analyses are listed in the record. Those calculations should be treated as exploratory summaries, not as substitutes for an adjusted or protocol-specified sponsor analysis. Whether an adjusted analysis was performed, or what model and covariates it might have used, is not reported in the registry record.

16. Multiplicity, Missing Data and Analysis Populations

The primary PFS results are reported separately for BRCA1/2-positive and BRCA1/2-negative groups. Testing more than one subgroup or outcome raises a multiplicity question: when several hypotheses are tested, the chance of at least one apparently notable result can increase. This is a general statistical concern, not evidence that the reported results are false. The registry record does not report whether the subgroup analyses were prespecified, whether they were part of a formal hierarchy, or whether any adjustment for multiple testing was used.

The record also lists multiple secondary outcomes. It does not report a comprehensive statistical analysis plan, the planned order of testing, or any multiplicity adjustment for those outcomes. Consequently, secondary p-values or unadjusted estimates should not be interpreted as if they necessarily had the same confirmatory status as the primary endpoint. The registry record does not report interim analyses or stopping rules.

The primary analysis population is described as the full analysis set, consisting of all randomised patients analysed on an intent-to-treat basis. This supports interpretation according to assigned treatment, but the registry record does not give detailed counts of exclusions from each analysis or describe all protocol deviations. For PFS, participants without progression or death at the time of analysis were censored at their latest evaluable RECIST assessment. Additional details about missing assessments, sensitivity analyses or alternative censoring approaches are not reported in the registry record.

For health-related quality of life, the record gives the time frame and group summaries but does not describe how missing questionnaires were handled or whether analyses used a particular repeated-measures model. The original sample-size justification, interim monitoring plan and full statistical analysis plan are also not reported in the registry record. These omissions limit assessment of prespecification, robustness and the intended inferential scope of the reported analyses.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: incarcerated hernia (2.8%), hepatic haematoma (2.8%), covid-19 pneumonia (2.7%), anaemia (1.4%), neutropenia (1.4%).

The registry reports serious adverse events in 5 of 74 participants receiving olaparib and 0 of 38 receiving placebo in the BRCA1/2-positive groups. In the BRCA1/2-negative groups, serious adverse events were reported in 11 of 72 participants receiving olaparib and 2 of 36 receiving placebo. These are counts of participants with serious adverse events, not event rates adjusted for follow-up or a comparison of severity across groups.

Other adverse events were reported in 64 of 74, 33 of 38, 65 of 72 and 30 of 36 participants across the respective olaparib-positive, placebo-positive, olaparib-negative and placebo-negative groups. Death counts are also listed, but the registry information does not establish that those deaths were caused by treatment. Serious adverse-event terms listed among the most frequent include incarcerated hernia, hepatic haematoma, COVID-19 pneumonia, anaemia, neutropenia and febrile neutropenia, with the percentages recorded in the registry.

These safety summaries are descriptive. The record does not provide enough detail to assess event timing, exposure duration, attribution, recurrence, or statistical comparisons. Counts should be read with their group sizes and alongside the registry’s definitions and full safety reporting, rather than as a causal estimate of treatment harm.

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

The posted primary results show median PFS estimates and sponsor-reported hazard ratios for two BRCA1/2 subgroups. In both comparisons, the estimated hazard ratio is below 1, and the reported 95% confidence interval excludes 1. These statistics describe the observed time-to-event comparisons under the analysis used by the sponsor. They do not mean that every participant had the same experience or that an individual outcome can be predicted from the group estimate.

The findings do not establish a treatment effect for all people with ovarian cancer. The study population was selected: participants had epithelial ovarian cancer, prior PARPi treatment and a response to repeat platinum chemotherapy. The record does not provide a direct statistical test comparing the treatment effect between BRCA1/2-positive and BRCA1/2-negative groups. The separate subgroup estimates should not be used as that test.

A hazard ratio is not a percentage improvement, a difference in median months, or an estimate of the probability that a participant will benefit. The registry results also do not resolve uncertainty about longer-term outcomes, because the information available for this analysis does not include numerical results for all listed secondary outcomes. Safety counts are descriptive and do not by themselves establish causation or an overall benefit-risk balance.

Interpretation depends on the analysis plan, missing-data handling, follow-up and potential multiplicity. Several of those details are not reported in the registry record. The results are therefore best understood as estimates from the recorded trial population and analyses, with uncertainty expressed by their confidence intervals, rather than as a universal conclusion about treatment.

19. Why This Trial Matters Statistically

This trial raises a statistical question about retreatment: whether the time-to-event pattern after prior PARPi exposure can be compared between olaparib and placebo in a population selected for response to repeat platinum chemotherapy. Randomisation and masking are important design features for interpreting that comparison, while the subgroup reporting makes it important to distinguish within-subgroup findings from a formal test of differences between subgroups.

The primary endpoint is time-to-event, so its interpretation depends not only on how many events occurred but also on when they occurred and how censoring was handled. The registry’s sponsor-reported hazard ratios retain that comparative time-to-event framing; medians offer a more accessible summary of each group’s event-time distribution. Confidence intervals are essential because the point estimates alone do not show the amount of uncertainty.

The results also illustrate why a statistically notable primary result is not the same as a complete account of a trial. Secondary outcomes cover survival, subsequent treatment, quality of life and safety, but the registry information does not supply numerical results for every listed measure. Multiplicity and the absence of a reported analysis plan limit how confidently the full set of findings can be treated as confirmatory.

Finally, planning illustrations based on observed effects can help readers understand how assumptions about effect size and power shape sample-size requirements. They cannot recover the trial’s original design rationale or replace the sponsor’s time-to-event analysis. Keeping these distinctions clear helps separate the posted evidence from what remains unreported.

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 primary comparisons are reported within BRCA1/2 subgroups, but the registry does not report a direct test of whether the treatment effect differs between those subgroups. Nor does the record state whether the subgroup analyses were prespecified or how they were incorporated into the study’s testing strategy. That makes it difficult to determine their intended confirmatory role.

The registry describes the PFS population as the full analysis set and gives a censoring rule, but detailed event counts, follow-up distributions and missing-assessment information are not reported in the registry record. The full analysis methods, including stratification factors and assessments of model assumptions, are also not reported. These details matter for evaluating how robust the time-to-event estimates are.

The registry lists multiple secondary outcomes, while numerical results available for this analysis are incomplete. Sponsor-reported secondary analyses for health-related quality of life are not listed, and handling of missing questionnaire data is not reported. A complete multiplicity plan is also not reported, limiting interpretation of any unadjusted secondary comparisons.

The safety figures are counts of participants with events, not exposure-adjusted comparisons. The registry information does not give enough detail to evaluate event timing, attribution or duration of treatment exposure. Finally, planning illustrations are based on observed effects and stated assumptions rather than the trial’s original design. The original sample-size justification and interim-analysis plans are not reported in the registry record.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study to Examine Olaparib Maintenance Retreatment in Patients With Epithelial Ovarian Cancer. — NCT03106987.
• Registry record last updated 2022-10-07; status last verified 2022-06.
• Results first posted 2022-04-19.
• 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

NCT03106987 is a completed Phase IIIb, randomised, double-blind, placebo-controlled, multicentre study of olaparib maintenance retreatment in epithelial ovarian cancer. The registry reports enrollment of 220, a start date of 2017-06-08 and a primary completion date of 2021-02-15. Olaparib 300mg tablets and matching placebo 300mg tablets were administered orally twice daily continuously.

The primary endpoint was RECIST 1.1 progression-free survival, reported by BRCA1/2 subgroup as median time and by sponsor-reported stratified log-rank hazard ratios. The registry also lists secondary outcomes covering survival, subsequent treatment, quality of life and safety. Important details about multiplicity, the original sample-size plan, interim analyses and some secondary analyses are not reported in the registry record.