Olaparib Treatment in BRCA Mutated Ovarian Cancer Patients After Complete or Partial Response to Platinum Chemotherapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Olaparib Treatment in BRCA Mutated Ovarian Cancer Patients After Complete or Partial Response to Platinum Chemotherapy (NCT01874353), a randomized phase 3 study. The primary outcome is Progression Free Survival (PFS) Using Investigator Assessment According to Modified Response Evaluation Criteria In Solid Tumours (RECIST 1.1).

2. Clinical Question

This is a maintenance-treatment question: the comparison concerns treatment after a complete or partial response to platinum-based chemotherapy, rather than treatment during that chemotherapy. Progression-free survival captures the time until disease progression or death under the endpoint definition; it is intended to describe how long patients remain alive without a recorded progression. The registry’s primary endpoint is based on investigator assessment using modified RECIST 1.1. Its primary population is described as all randomized patients in the global enrollment, excluding China, with a distinct China Full Analysis Set for patients randomized at sites in China.

The registry also lists overall survival, progression defined using RECIST or CA-125 or death, time to second progression, quality of life, and subsequent-treatment timing among secondary outcomes. These outcomes address different aspects of the course after randomization and should not be treated as interchangeable with the primary endpoint. The primary comparison and the separate cohort results are therefore the central statistical focus.

3. Trial Design

The registry describes a Phase III, randomized, double-blind, placebo-controlled, parallel-group study with quadruple masking. The study summary describes it as multicentre and assesses olaparib maintenance monotherapy in patients with relapsed high-grade serous ovarian cancer, including primary peritoneal and/or fallopian tube cancer, or high-grade endometrioid cancer, with a deleterious or suspected deleterious BRCA mutation and a complete or partial response after platinum-based chemotherapy. The recorded enrollment is 327.

Participants were assigned to olaparib 300 mg tablets or matching placebo tablets, both taken orally twice daily. The primary endpoint was investigator-assessed progression-free survival according to modified RECIST 1.1. The registry gives a global primary analysis population that excludes China and identifies a separate China Full Analysis Set. Results are consequently reported for the global cohort and the China cohort, rather than as one combined treatment comparison.

The primary endpoint timeframe describes radiologic scans at baseline and then at roughly 12-week intervals up to 72 weeks, followed by roughly 24-week intervals thereafter until objective radiologic disease progression. The record identifies an assessment cutoff for the global analysis and a separate cutoff for the China cohort, and specifies a maximum follow-up of 36 months for this endpoint. The study record’s current status is active, not recruiting.

The registry lists 10 outcome measures and 16 analyses. Its posted results include the primary endpoint, several secondary outcomes, and safety counts. The original statistical design details—including the trial’s own sample-size justification and other prespecified analysis-plan details—are not reported in the registry record. Planning illustrations based on observed effects should therefore be read separately from the study’s original design rationale.

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: It was planned that approximately 264 women from the Global Cohort and 33 women from the China Cohort, with BRCA mutated relapsed ovarian cancer who are in complete or partial response following platinum based chemotherapy, were to receive olaparib 300 mg bd or matching placebo in a 2:1 ratio.

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 randomized as part of global enrolment, excluding China \[Primary analysis\] China Full Analysis Set (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: Global Cohort: 196 Olaparib, 99 Placebo China Cohort: 22 Olaparib, 10 Placebo

6. Primary Endpoint

The registry lists the primary outcome as Progression Free Survival (PFS) Using Investigator Assessment According to Modified Response Evaluation Criteria In Solid Tumours (RECIST 1.1), measured over Radiologic scans performed at baseline then every ~12 weeks up to 72 weeks, then every ~ 24 weeks thereafter until objective radiological disease progression. Assessed until 19 Sep 2016 DCO (16 Jan 2017 DCO for China Cohort); up to a maximum of 36 months..

Progression-free survival (PFS) is the primary endpoint. In this study, it is defined through investigator assessment using modified Response Evaluation Criteria in Solid Tumours (RECIST 1.1). The registry describes radiologic assessment beginning at baseline, followed by scheduled scans, and continuing until objective radiologic disease progression. PFS is a time-to-event outcome: the analysis considers both whether an event has occurred and the time until it occurs. The registry reports median PFS with a 95% confidence interval and a Cox-model hazard ratio for the treatment comparison.

As a general statistical concept, PFS is used in oncology trials to describe the time patients remain alive without recorded progression. It can capture disease-course information before all participants have experienced the endpoint, which is useful when follow-up lengths differ or some observations are censored. A median summarizes the time by which the estimated event-free proportion has reached the midpoint; it does not describe every participant’s experience or the shape of the entire time-to-event distribution.

Investigator assessment is the stated assessment approach for this primary endpoint. The registry record does not report further detail about how assessment disagreements were handled or whether a blinded independent review was also used. The primary endpoint’s stated maximum follow-up is 36 months, with the global and China cohorts having separate assessment cutoffs.

7. Results Posted in the Registry

• Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort): hazard ratio 0.30 (95% CI 0.22–0.41), reported p < 0.001 (as reported in the registry).
• Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort): hazard ratio 0.44 (95% CI 0.17–1.19) (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 in Patients Following Platinum Based Chemotherapy by Assessment of Overall Survival

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort): hazard ratio 0.74 (95% CI 0.54–1.00), reported p = 0.054 (as reported in the registry).
  • Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort): hazard ratio 0.93 (95% CI 0.38–2.49) (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 Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort) 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 Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort) and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy in Patients Following Platinum Based Chemotherapy by Assessment of Time to Earliest Progression by RECIST or Cancer Antigen (CA-125) or Death

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort): hazard ratio 0.30 (95% CI 0.23–0.41), reported p < 0.001 (as reported in the registry).
  • Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort): hazard ratio 0.41 (95% CI 0.18–1.03) (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 Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort) and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy in Patients Following Platinum Based Chemotherapy by Assessment of Time From Randomization to Second Progression

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort): hazard ratio 0.50 (95% CI 0.34–0.72), reported p < 0.001 (as reported in the registry).
  • Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort): hazard ratio 0.84 (95% CI 0.22–3.97) (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 Olaparib 300mg Tablets (Global Cohort) vs Placebo Tablets (Global Cohort) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Olaparib 300mg Tablets (China Cohort) vs Placebo Tablets (China Cohort) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes broaden the assessment beyond investigator-assessed PFS. They include overall survival, time to earliest progression by RECIST or CA-125 or death, time from randomization to second progression, health-related quality of life, and time to subsequent therapy or treatment discontinuation. These measure different events and aspects of follow-up, so agreement across them can add context but does not make them interchangeable or turn them into additional primary endpoints.

For the global cohort, the reported progression-related comparisons generally point in the same direction as the primary PFS result. The reported time-to-second-progression comparison also favors a lower event hazard for olaparib, while the overall-survival estimate is less definitive by its confidence interval and reported p-value. The China estimates are less precise, with broad intervals. The individual secondary results and their numerical details are stated with the corresponding outcome statistics; the key interpretive point is that their evidential weight is subordinate to the primary analysis.

As a general statistical concern, testing many outcomes increases the chance that some results will appear noteworthy by chance, particularly when outcomes or analyses are not adjusted for multiplicity. The registry record does not report whether a multiplicity procedure was used for the secondary outcomes. Accordingly, secondary p-values and confidence intervals should be treated as exploratory or supportive unless a prespecified hierarchy or adjustment is documented. The registry record does not report such a hierarchy or adjustment.

Secondary measures can still be informative: they may show whether findings are coherent across related endpoints, whether survival follow-up gives a different picture from progression measures, and whether patient-reported outcomes were assessed. But each outcome has its own definition, observation schedule, missingness, and analysis population. The posted results should therefore be interpreted outcome by outcome, with the primary result retaining the central confirmatory role.

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

• Efficacy in Patients Following Platinum Based Chemotherapy by Assessment of Overall Survival
• Efficacy in Patients Following Platinum Based Chemotherapy by Assessment of Time to Earliest Progression by RECIST or Cancer Antigen (CA-125) or Death
• Efficacy in Patients Following Platinum Based Chemotherapy by Assessment of Time From Randomization to Second Progression
• Change From Baseline in Health-Related Quality of Life (HRQoL) as Assessed by the the Trial Outcome Index (TOI) of the Functional Assessment of Cancer Therapy - Ovarian (FACT-O)
• Efficacy of Olaparib by Time to First Subsequent Therapy or Death (TFST)
• Efficacy of Olaparib by Time to Second Subsequent Therapy or Death (TSST)
• Efficacy of Olaparib by Time From Randomization to Study Treatment Discontinuation or Death (TDT)
• Efficacy in Patients With a Deleterious or Suspected Deleterious Variant in Either of the BRCA Genes by Assessment of PFS.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure, so its analysis must account for both the event times and participants whose event time is not observed during the available follow-up. The registry reports median PFS and a Cox regression hazard ratio. These are complementary summaries: the median gives a time point on the estimated event-time distribution, while the hazard ratio compares event rates over the follow-up represented in the model.

What does a median time-to-event value represent?

As a general statistical explanation, the median event time is the point at which the estimated proportion remaining event-free reaches one half. It is not the average follow-up time, nor does it mean that all participants experience an event at that time. Participants’ event times vary, and some may be censored because their event has not been recorded by the end of observation or because observation ends for another reason. A median can be unavailable or not estimable when the estimated event-free curve does not reach its midpoint in the relevant analysis. The registry reports no median value for some listed secondary comparisons, so no such value should be inferred.

How should the hazard ratio be understood?

The sponsor’s reported treatment comparisons use Cox regression. As a general statistical explanation, the Cox model relates the event hazard between treatment groups while accounting for event timing and censored observations. A hazard ratio below one indicates a lower estimated event hazard in the first named group relative to the comparator under the model; it is not a ratio of median times, a probability that an individual will benefit, or a direct measure of how many months an individual gains. The model’s interpretation also depends on its assumptions. The registry record does not report diagnostics or detailed modeling covariates for these analyses.

The hazard ratio and its confidence interval should be read together. The point estimate gives one best-fitting value under the analysis, while the interval conveys uncertainty in that estimate. An interval that spans one is compatible with no relative hazard difference as well as values on either side; a narrower interval indicates greater precision than a wider one. Statistical significance is not the same as clinical importance, and neither the interval nor the p-value describes the full range of individual outcomes.

Why are the cohorts reported separately?

The registry defines the primary global Full Analysis Set as randomized patients from global enrollment, excluding China, and separately defines a China Full Analysis Set for patients randomized at sites in China. The posted treatment effects are consequently cohort-specific. The China estimates are based on smaller listed group sizes than the global cohort estimates, and their intervals are wider. This is a precision distinction, not evidence that the populations should be pooled or that an unreported pooled result can be reconstructed. No combined cohort estimate should be inferred.

The registry describes random allocation, a parallel-group design, and double blinding, which support a comparative interpretation of the assigned groups. Randomization helps balance measured and unmeasured baseline factors on average, while masking can limit the influence of treatment knowledge on care or assessment. The record also labels masking as quadruple. It does not specify which four roles were masked, and that detail is not reported in the registry record. Investigator assessment remains the stated method for the primary endpoint.

What can censoring and follow-up change?

In time-to-event analysis, censoring means that the event time is only known to exceed the participant’s observed follow-up. Standard methods use such partial information rather than treating a censored participant as though an event occurred at the end of observation. Their validity depends on assumptions about censoring and the analysis. The registry gives scan schedules and assessment cutoffs but does not report detailed censoring rules, missing-data sensitivity analyses, or the extent of missing endpoint data.

Follow-up schedules also matter because progression is detected at assessments rather than continuously. The primary endpoint uses scheduled radiologic scans, and its timeframe states that scans become less frequent after 72 weeks. Thus the recorded progression time is tied to the study’s assessment process. The registry record does not provide additional detail on handling progression dates between scans.

For general context, time-to-event methods are useful when participants have different follow-up durations and when not everyone experiences an event before observation ends. They do not remove the need to examine the endpoint definition, assessment schedule, censoring, and model assumptions. The posted results should be read as analyses under the registry-described definitions, with unreported analysis details left uncertain rather than assumed.

11. Confidence Intervals and Precision

The global primary comparison has a reported hazard ratio of 0.30 and a 95% confidence interval from 0.22 to 0.41. The interval is relatively concentrated on values below one, indicating greater precision than the China cohort estimate. The global median PFS estimates also have reported confidence intervals: 16.3 to 25.7 months for olaparib and 5.2 to 5.8 months for placebo. These intervals describe uncertainty around the estimated medians; they are not ranges containing a fixed proportion of individual patients’ PFS times.

For the China comparison, the reported hazard ratio is 0.44, with a 95% confidence interval from 0.17 to 1.19. This interval is broad and extends across one, so the estimate allows a wider range of relative effects than the global estimate. The China olaparib median has a reported interval from 6.5 to 16.6 months, while the placebo median is 5.5 months with a lower confidence bound of 2.7 months and no upper bound reported. An unreported bound should not be treated as zero, infinity, or a known value.

As a general statistical concept, a confidence interval reflects sampling uncertainty under the model and method used. It does not account for every possible source of uncertainty, such as unreported analysis choices, endpoint measurement issues, or limits to generalizability. Wider intervals often occur when there is less information for estimating an effect; the China cohort intervals are less precise than those for the global cohort. The registry does not report the number of PFS events used in each treatment comparison, so event counts should not be inferred from the confidence intervals or planning illustrations.

The point estimates should not be read without their intervals. A precise estimate can still be affected by design or analysis limitations, while an imprecise estimate may remain compatible with a range of materially different effects. The registry’s p-value for the global comparison is reported as < 0.001; a p-value is not a measure of effect size or precision and does not replace the confidence interval.

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 illustrations are not the trial’s original design justification. For time-to-event outcomes, their figures are total event counts, not participants per arm. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect expressed as a stated fraction of the observed effect. The original trial sample-size assumptions are not reported in the registry record.

The 80% power column gives the total number of events required under the stated planning assumptions for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column describes the corresponding event requirement for a 90% chance. These are planning targets, not counts of events observed in the trial. For example, the global primary comparison’s display gives 22 total events for planning around 100% of the observed effect at 80% power and 29 at 90% power; for planning around 50% of the observed effect, the corresponding displayed totals are 87 and 116.

Smaller effects are harder to distinguish from random variation, so the planning illustrations require more events when the effect to detect is a smaller fraction of the observed effect. The displayed values are conditional on the listed assumptions and should not be mistaken for a recommendation about trial design. They are not observed power: observed power is not calculated by substituting the effect estimated from the completed study into a planning formula.

Where a planning display concerns a non-time-to-event outcome, the general convention described in the assumptions is participants per arm; the time-to-event displays instead use total events. These are planning illustrations based on observed effects, not a reconstruction of the sponsor’s original design process.

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 = 0.300, so ln(HR) = -1.2040.
2. d = 4 × (1.96 + 0.842)² / [ln(0.300)]² = 21.7, rounded up to 22 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 <- 0.3                              # 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(1874353)
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 = 22 (80% power), 29 (90% power)
 75% of observed effect: events = 39 (80% power), 52 (90% power)
 50% of observed effect: events = 87 (80% power), 116 (90% power)
Simulated power with 22 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 35 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 327 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 <- 5.5          # control-arm median, months (converted from the posted unit)
hr          <- 0.3          # 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: 24        p (1-sided)   0.0001
 Events: 10       ~HR at bound   0.0892
  Month: 16   P(Cross) if HR=1   0.0001
            P(Cross) if HR=0.3   0.0338
  IA 2: 67%                  Z   2.5114
      N: 36        p (1-sided)   0.0060
 Events: 19       ~HR at bound   0.3144
  Month: 26   P(Cross) if HR=1   0.0060
            P(Cross) if HR=0.3   0.5603
      Final                  Z   1.9930
      N: 36        p (1-sided)   0.0231
 Events: 29       ~HR at bound   0.4725
  Month: 60   P(Cross) if HR=1   0.0250
            P(Cross) if HR=0.3   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’s reported primary comparison for the global cohort is a Cox regression hazard ratio of 0.30, with a 95% confidence interval from 0.22 to 0.41 and p < 0.001. The China cohort’s reported hazard ratio is 0.44, with a 95% confidence interval from 0.17 to 1.19; the registry does not report a p-value for that comparison.

The simple unadjusted re-calculations from posted summary statistics do not indicate a discrepancy with the sponsor’s reported analyses. Where the sponsor has reported an analysis, that analysis takes precedence over a recalculation. In particular, the hazard ratios and their intervals are model-based results, and a re-calculation from summary values cannot reproduce all details of the sponsor’s Cox analysis.

The registry identifies the method as Cox regression but does not report all model specifications, covariate choices, diagnostic results, or handling details. A close numerical match between a recalculation and a posted estimate would not establish that every underlying analytic choice was identical. The sponsor’s reported result is therefore the relevant inferential result; recalculated values, where available, are supplementary checks rather than replacements for the trial analysis.

16. Multiplicity, Missing Data and Analysis Populations

The registry lists 10 outcome measures and 16 analyses, including the primary PFS endpoint and several secondary efficacy and quality-of-life outcomes. The number of analyses makes multiplicity relevant: when multiple outcomes or comparisons are tested, the chance of at least one apparently unusual result can rise even if there is no underlying effect for those tests. This is a general statistical issue, not a finding that any particular reported result is false.

Whether and how the investigators addressed multiplicity is not reported in the registry record. The record does not report a testing hierarchy, familywise error procedure, adjustment of secondary p-values, or a prespecified distinction between confirmatory and exploratory secondary analyses. Without that information, the secondary results should not be read as though each had the same confirmatory status as the primary endpoint.

The primary analysis population is described as the global Full Analysis Set, consisting of all patients randomized as part of global enrollment and excluding China. A separate China Full Analysis Set includes patients randomized at sites in China. This clarifies the registry’s population definitions, but additional details about analysis populations, exclusions after randomization, and the handling of deviations are not reported in the registry record.

The registry describes the primary outcome assessment schedule and cutoff dates, but detailed missing-data procedures are not reported. It does not state the amount or pattern of missing endpoint data, the censoring rules, sensitivity analyses for missingness, or the methods used to address informative censoring. These omissions matter because time-to-event estimates rely on assumptions about participants whose endpoint is not observed during follow-up.

The registry record identifies Cox regression for the reported hazard-ratio analyses but does not report model diagnostics, proportional-hazards checks, covariate adjustment details, or a full statistical analysis plan. Those details cannot be inferred from the reported point estimates and intervals. The limitations do not invalidate the posted results, but they constrain independent assessment of the full analysis strategy.

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: gastroenteritis (10.0%), anaemia (9.1%), neutropenia (4.5%), food poisoning (4.5%), white blood cell count decreased (4.5%).

The registry lists serious adverse events for each cohort and treatment group. In the global cohort, serious adverse events were reported for 50 of 195 participants in the olaparib group and 8 of 99 in the placebo group. In the China cohort, the corresponding figures were 5 of 22 and 1 of 10. The registry also reports deaths in the safety groups: 116, 65, 13, and 7, respectively. These are counts in the registry’s safety reporting and should not be interpreted as deaths caused by treatment.

The record lists gastroenteritis at 10.0%, anaemia at 9.1%, and neutropenia, food poisoning, white blood cell count decreased, and leukopenia at 4.5% each among the top serious-event terms. The registry extract does not specify the cohort or denominator for these term percentages, so they should not be assigned to a particular treatment group from the available information.

Serious adverse-event counts are not the same as all adverse events, treatment-related events, or events leading to discontinuation. The registry separately lists other adverse-event counts, but these aggregate figures do not establish causation or compare event severity in detail. Exposure duration, event timing, attribution, and detailed safety analysis methods are not reported in the registry record. Differences in raw counts should therefore be read in the context of the listed group sizes and the limits of the reporting, without calculating unreported rates or attributing individual events to treatment.

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

The posted global results show a lower estimated PFS event hazard for olaparib than placebo in the trial’s defined population, with a reported hazard ratio of 0.30 and a 95% confidence interval from 0.22 to 0.41. The global median PFS estimates were 19.1 months and 5.5 months, respectively. These results describe the randomized comparison for patients with BRCA-mutated relapsed ovarian cancer who had responded to platinum-based chemotherapy, under the registry’s investigator-assessed endpoint definition.

The China cohort estimate is less precise: its hazard-ratio interval extends from 0.17 to 1.19. This means the cohort-specific evidence is compatible with a wider range of relative effects than the global result, including values on either side of one. The separate populations and different precision mean that the cohort findings should not be collapsed into a single unreported estimate.

The findings do not establish what an individual patient will experience. Group medians do not predict a person’s time to progression, and a hazard ratio is not an individual probability or a direct estimate of additional months for each participant. The results also do not answer questions about patients without the specified BRCA mutation, patients who did not respond to platinum-based chemotherapy, or different disease and treatment settings.

The primary endpoint measures progression-free survival, not every dimension of benefit or harm. Overall survival, quality of life, subsequent therapies, and safety are separate outcomes, each with its own uncertainty and limitations. The registry’s secondary analyses should be interpreted with their status and multiplicity context in mind. The record does not report all details needed to evaluate missing data, model assumptions, or multiplicity procedures.

These statistics are a description of posted trial results, not medical advice. They do not by themselves determine whether a treatment is appropriate for any individual. Their meaning depends on the population studied, endpoint definitions, follow-up, analysis methods, and the uncertainty reflected in the reported intervals.

19. Why This Trial Matters Statistically

This trial illustrates how a randomized, blinded, placebo-controlled design can frame a comparative time-to-event question in a defined clinical population. Because treatment was assigned at random, the comparison is more informative about the assigned groups than an uncontrolled observation would be, while masking can reduce some influences of treatment knowledge. The registry identifies the primary endpoint and its assessment method, allowing the result to be interpreted in relation to a specific outcome rather than a general claim about efficacy.

It also demonstrates why both median times and hazard ratios are useful, but not interchangeable. The medians give recognizable time summaries for each group, whereas the Cox hazard ratio compares event hazards across follow-up. Confidence intervals are essential for judging how precisely those effects are estimated. The contrast between the global and China cohort intervals makes clear that a point estimate alone can conceal substantial differences in precision.

The secondary outcomes show why a trial may examine several related dimensions, and why multiplicity matters. A collection of endpoints can deepen understanding, but evidence from secondary analyses needs to be considered in light of prespecification, testing strategy, missingness, and analysis populations. Details not reported in the registry should remain unknown rather than being filled in by assumptions.

Finally, the planning illustrations emphasize that event-driven designs depend on the effect size a study aims to detect and the number of events available. They are not observed power and do not recover the sponsor’s original design assumptions. Keeping design planning, reported analysis, and retrospective illustration distinct is central to sound interpretation of clinical trial statistics.

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 leaves several analysis details unresolved. Although it reports Cox regression for the hazard-ratio comparisons, it does not report the full model specification, covariate adjustment, proportional-hazards diagnostics, or sensitivity analyses. These details are relevant to assessing the assumptions behind the reported relative hazard estimates.

The primary endpoint is based on investigator assessment, and the registry describes a scan schedule with intervals that change over follow-up. It does not report further detail on blinded independent review, adjudication, handling of progression between scans, or how assessment disagreements were managed. The record also does not report the amount and pattern of missing endpoint data or detailed censoring rules.

The global primary analysis excludes China, and the registry reports a separate China cohort analysis. The China estimates are less precise, with broad confidence intervals; they should not be treated as an equivalent replication of the global estimate or combined into a pooled result that the registry does not report. The record does not provide subgroup interaction tests establishing whether the cohort estimates differ from one another.

Several secondary outcomes and analyses are listed, but multiplicity procedures and a testing hierarchy are not reported in the registry record. The secondary findings therefore carry less confirmatory weight than the primary result. The safety information is also presented as aggregate counts and selected event terms; detailed attribution, exposure-adjusted comparisons, timing, and reasons for death are not reported in the registry record.

These are limitations of the available registry record, not claims that the study did not conduct additional analyses. The posted summary supports interpretation of the reported estimates, while the absent details restrict independent review of the full analysis and its assumptions.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Olaparib Treatment in BRCA Mutated Ovarian Cancer Patients After Complete or Partial Response to Platinum Chemotherapy — NCT01874353.
• Registry record last updated 2026-07-29; status last verified 2026-07.
• Results first posted 2018-02-07.
• 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

The registry describes a Phase III, randomized, double-blind, placebo-controlled, parallel-group study of olaparib maintenance monotherapy after response to platinum-based chemotherapy in patients with relapsed BRCA-mutated ovarian cancer. Olaparib 300 mg tablets and matching placebo were taken orally twice daily. The primary endpoint was investigator-assessed PFS using modified RECIST 1.1, with separate global and China cohort analyses.

For the global cohort, median PFS was 19.1 months with olaparib and 5.5 months with placebo; the reported hazard ratio was 0.30 (95% confidence interval 0.22 to 0.41; p < 0.001). For the China cohort, the reported hazard ratio was 0.44 (95% confidence interval 0.17 to 1.19), with less precision. Secondary outcomes and safety counts provide context, but their analysis details and multiplicity handling are not fully reported in the registry record.