Assessment of the Efficacy and Safety of Olaparib Monotherapy Versus Physicians Choice Chemotherapy in the Treatment of Metastatic Breast Cancer Patients With Germline BRCA1/2 Mutations.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Assessment of the Efficacy and Safety of Olaparib Monotherapy Versus Physicians Choice Chemotherapy in the Treatment of Metastatic Breast Cancer Patients With Germline BRCA1/2 Mutations. (NCT02000622), a randomized phase 3 study. The primary outcome is Progression-free Survival (PFS) Using Blinded Independent Central Review (BICR) According to Modified Response Evaluation Criteria In Solid Tumours (RECIST v1.1).

2. Clinical Question

The clinical question is a comparison between two treatment strategies in a selected trial population, not a comparison of olaparib with every possible chemotherapy regimen. The chemotherapy arm allowed a physician-selected option from the listed drugs, while the experimental arm received olaparib monotherapy.

The primary endpoint combines radiological disease progression and death. It therefore asks about the time until either event, rather than only whether a participant’s disease changed on a particular scan. Progression was assessed by blinded independent central review according to modified RECIST v1.1. Blinding the reviewers can reduce the chance that knowledge of treatment assignment influences assessment, even though the overall trial was open label.

The registry record identifies the study as completed and describes it as a phase III, randomized, controlled, multicentre study. Its primary comparison concerns the relative timing of progression or death in the trial’s defined population. It does not, by itself, answer questions about other populations, other treatments, or outcomes that were not measured.

3. Trial Design

This was a phase III, open-label, randomized, controlled, multicentre study with a parallel-group design. The registry record reports enrollment of 302 participants. Participants were assigned to olaparib monotherapy or physician’s choice chemotherapy. The chemotherapy choices were capecitabine, vinorelbine, and eribulin, with the listed regimen depending on the selected drug.

The registry record gives the study start as 2014-03-27 and primary completion as 2016-12-09, and lists the study status as completed. AstraZeneca is identified as the sponsor. The record describes no masking; however, the primary endpoint was assessed by blinded independent central review. These are distinct features: the treatment assignment was open label, while central reviewers assessing radiological progression were blinded.

The primary outcome was progression-free survival in the Full Analysis Set, defined as all randomised patients. Scans were scheduled at baseline and then approximately every six weeks up to 24 weeks, followed by approximately every 12 weeks thereafter until objective radiological progression, with assessment up to a maximum of 30 months. The endpoint was time from randomisation to objective radiological progression or death in the absence of objective progression.

The registry record lists 12 outcome measures and 11 analyses. It names several secondary outcomes, including time to second progression or death, overall survival, objective response rate, quality of life, and a progression-free survival analysis in patients confirmed as Myriad CDx gBRCAm. The trial’s original sample-size justification, detailed allocation procedures, interim analysis plan, and full prespecified statistical analysis plan are not reported in the registry record. The posted planning illustrations are not a substitute for those original design details.

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: Screening occurred in 2 parts. Part 1: patients with unknown BRCA status were tested by Myriad. Part 1 screening failures were mostly due to no BRCA1/2 mutation detected. Part 2: patients with a known germline BRCA mutation were screened. 302 patients were randomized.

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 randomised patients

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 consisting of all randomized patients.

6. Primary Endpoint

The registry lists the primary outcome as Progression-free Survival (PFS) Using Blinded Independent Central Review (BICR) According to Modified Response Evaluation Criteria In Solid Tumours (RECIST v1.1), measured over Radiological scans performed at baseline then every ~6 weeks up to 24 weeks, then every ~ 12 weeks thereafter until objective radiological disease progression. Assessed up to a maximum of 30 months..

The primary endpoint is progression-free survival measured from randomisation to the earliest of objective radiological progression or death from any cause in the absence of documented progression. Progression was determined using modified RECIST v1.1 criteria and blinded independent central review. The registry description defines progression through a specified increase in target lesions, measurable increase in a non-target lesion, or appearance of new lesions.

This endpoint is used to represent the length of time participants remain alive without recorded disease progression. Combining progression and death means that a participant can experience the endpoint through either event; it is not simply a measure of tumor shrinkage or of survival alone. The posted median summarizes the time-to-event distribution, while the hazard ratio summarizes the relative event rate over follow-up as estimated by the reported analysis.

Time-to-event methods are useful when participants can have different lengths of follow-up and some have not experienced the endpoint by the time their observation ends. Such participants contribute information up to their last known assessment rather than being treated as if the event had occurred. General statistical interpretation depends on how censoring and the analysis model are handled; the full details of those procedures are not reported in the registry record.

Central blinded review is relevant because radiological progression requires judgment about scan findings. It can help separate assessment of the endpoint from knowledge of assigned treatment. It does not remove every possible source of bias, and it does not make the study itself blinded.

7. Results Posted in the Registry

• Olaparib 300 mg bd vs Chemotherapy: hazard ratio 0.58 (95% CI 0.43–0.80), reported p < 0.001 (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.

Time to Second Progression or Death (PFS2)

• 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:
  • Olaparib 300 mg bd vs Chemotherapy: hazard ratio 0.57 (95% CI 0.40–0.83), reported p = 0.003 (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 300 mg bd vs Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Survival (OS)

• 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:
  • Olaparib 300 mg bd vs Chemotherapy: hazard ratio 0.90 (95% CI 0.63–1.29), reported p = 0.567 (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 300 mg bd vs Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate (ORR) Using Blinded Independent Central Review (BICR) Data Assessed by Modified Response Evaluation Criteria In Solid Tumours (RECIST v1.1)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Chemotherapy: 28.8% (19/66) versus 59.9% (100/167) on control; risk difference -31.1 percentage points (95% CI -44.3 to -17.9), risk ratio 0.48 (0.32–0.72); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Chemotherapy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary outcomes, the broad pattern is not uniform. The time-to-second-progression comparison points in the same general direction as the primary progression-free survival result, while the overall survival comparison is uncertain. Objective response counts also differ between groups, but that outcome is presented without a sponsor-reported analysis. Quality of life and other listed outcomes broaden the scope of assessment but do not replace the primary endpoint.

Secondary outcomes help describe whether the primary finding is accompanied by similar patterns in related measures or whether results differ for other questions. Time to second progression extends the assessment beyond the first progression event, whereas overall survival concerns death. Response rate records whether a response occurred, and quality of life captures a different dimension of outcome. Because these outcomes measure different things, agreement is informative but disagreement is not automatically a contradiction.

Secondary results generally carry less confirmatory weight when many outcomes or analyses are considered and the multiplicity strategy is not known. If many statistical tests are conducted, the chance of at least one apparently notable result can increase. Adjustments or a prespecified hierarchy can address that issue, but the registry record does not report a multiplicity plan. P-values for secondary comparisons should therefore be interpreted cautiously and alongside their confidence intervals, endpoint definitions, and analysis populations.

The record lists several secondary analyses, but the complete analysis plan and status of all planned assessments are not reported in the registry record. Consequently, the posted secondary results are best read as complementary evidence rather than as independent confirmation of the primary result. They cannot establish a broad pattern across outcomes beyond those recorded.

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

• Time to Second Progression or Death (PFS2)
• Overall Survival (OS)
• Objective Response Rate (ORR) Using Blinded Independent Central Review (BICR) Data Assessed by Modified Response Evaluation Criteria In Solid Tumours (RECIST v1.1)
• Adjusted Mean Change in Global Health Status/Quality of Life (QoL) Score From the European Organisation for Research and Treatment of Cancer - Quality of Life Questionnaire (EORTC QLQ-C30)
• Progression-free Survival (PFS) Using Blinded Independent Central Review (BICR) According to Modified Response Evaluation Criteria In Solid Tumours (RECIST v1.1) in Patients Confirmed as Myriad CDx gBRCAm
• Overall Survival (OS) at Final OS
• Overall Survival (OS) at Extended OS

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports time-to-event results for the primary outcome and several secondary outcomes. These methods account for the timing of an event, rather than reducing follow-up to a simple event/no-event count. A participant who has not had the event by the end of their observed follow-up may be censored, meaning that the event time is not known beyond that point. General time-to-event analysis uses the available follow-up while recognizing that uncertainty.

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

A median is the point in the estimated event-time distribution at which half of the population is expected to have experienced the event and half has not yet experienced it, subject to the estimation method and follow-up. It is not the mean, and it does not imply that all participants experienced the event at that time. A median alone also omits information about the shape of the event-time distributions over the rest of follow-up.

For the primary outcome, the posted medians are 7.0 months for olaparib and 4.2 months for chemotherapy. The comparison is not based only on subtracting these medians. The reported hazard ratio uses a time-to-event comparison across observed follow-up, and the registry identifies the log-rank method for the comparison. The details of the complete model and any additional adjustment are not reported in the registry record.

How should a hazard ratio be read?

A hazard ratio compares event rates between groups over time, as represented by the analysis. A value below 1 for olaparib versus chemotherapy indicates a lower estimated event rate in the olaparib group in the reported comparison. It is not a ratio of median times, a probability that a participant will have an event, or a direct statement about how long an individual will live without progression. The interpretation of a single hazard ratio as a constant relative contrast over follow-up relies on assumptions about how the relative event rates behave; the registry record does not report diagnostic results for those assumptions.

The primary hazard ratio is reported as 0.58 with a 95% confidence interval from 0.43 to 0.80. The interval stays below 1, and the reported p-value is 0.001. These are related but different summaries: the interval describes uncertainty in the estimated hazard ratio under the method, while the p-value assesses compatibility with a specified no-difference null under that method. Neither quantity indicates the size or importance of every participant’s experience.

What role does the log-rank method play?

The log-rank method compares the timing of events between groups over follow-up. In general, it uses information from event times and the numbers still at risk at each event time. It is not a comparison of just the final number of events or of the medians alone. The registry lists log-rank analyses for the reported time-to-event hazard ratios. The record does not provide enough detail to establish every implementation choice, such as all stratification or adjustment factors, so those should not be assumed.

How are response counts different?

Objective response rate is a binary outcome: participants are classified according to whether they met the response definition during assessment. Unlike progression-free survival, a response count does not directly include the timing of response or the duration of response. The posted response figures use different numbers of participants in the two groups than the primary Full Analysis Set. The registry record does not explain all reasons for those outcome-specific denominators. The unadjusted comparison is therefore a separate summary, and it should not be read as though it were the primary time-to-event analysis.

General statistical methods for binary outcomes can compare proportions, risk differences, risk ratios, or odds ratios. These measures answer related but non-identical questions. A risk difference describes a difference in event proportions, while ratios describe relative contrasts. The posted unadjusted recalculation is not a substitute for a sponsor-reported analysis; no sponsor-reported analysis is listed for the objective response outcome.

Why does over-dispersion matter in general?

For count outcomes, over-dispersion means the observed variability is greater than a chosen statistical model expects. If it is ignored, standard errors and uncertainty estimates can be too small, making results appear more precise than warranted. The primary outcome is time-to-event, not a count outcome, and the registry does not report an over-dispersion assessment. This general concept should not be taken as a description of the trial’s analysis.

Because the trial is open label, participants and treating clinicians knew treatment assignment, while the primary radiological endpoint was assessed by blinded independent central review. This distinction can matter: knowledge of assignment may affect care or reporting, whereas blinded endpoint review can reduce influence on scan interpretation. Neither feature alone resolves every potential source of bias. The full statistical analysis plan, including missing-data procedures and any sensitivity analyses, is not reported in the registry record.

11. Confidence Intervals and Precision

Confidence intervals describe the uncertainty around an estimated quantity under the analysis method. They are not a range that contains every participant’s outcome, nor do they guarantee that the true value lies within the interval. A 95% confidence interval is a property of the procedure that would generate intervals across repeated studies under its assumptions.

For the primary comparison, the hazard ratio is 0.58 and the 95% confidence interval is 0.43 to 0.80. The interval lies below 1, in keeping with the reported p-value of 0.001 and a group difference favoring olaparib in the reported time-to-event comparison. The interval still allows a range of possible relative event-rate contrasts; a single point estimate should not be treated as exact.

The median estimates also have uncertainty intervals: 5.7 to 8.3 months for olaparib and 2.8 to 4.3 months for chemotherapy. These intervals describe uncertainty in each median estimate, not a direct confidence interval for the difference between medians. The registry record does not post a separate interval for a median difference.

For overall survival, the hazard ratio is 0.90, with a 95% confidence interval from 0.63 to 1.29. Since this interval includes 1, the data are compatible with a range of relative event-rate contrasts that includes no difference under the reported method. This does not establish equivalence or prove that the groups have identical survival.

Precision depends on the amount and distribution of information, including the number and timing of events and the follow-up available. The registry record does not report all details needed to assess those components independently. A confidence interval should therefore be read alongside the endpoint definition, population, follow-up, and analysis method, rather than as a stand-alone verdict.

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 based on the observed effect and are not the trial’s original design justification. For time-to-event outcomes, the figures are total events required; for other outcomes, the figures are participants per arm. The binary outcome illustration therefore uses participants per arm, while the time-to-event illustrations use total events across the study.

The stated 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 a stated fraction of the observed effect. The registry record does not report the trial’s original sample-size assumptions or justification, so these illustrations should not be mistaken for the actual design calculation.

The 80% power column describes the number of events or participants the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were present. The 90% power column gives the corresponding planning quantity for a 90% chance. These are planning concepts, not guarantees about a future result. In general, smaller effects require more information to detect with the same target power, which is why the illustrations require larger event or participant counts as the assumed effect is reduced.

These figures are not observed power. They do not measure the probability that the completed study’s result is true, and they do not revise the uncertainty in the posted estimates. Their value is as conditional planning illustrations: the required information changes with the effect size assumed and with the stated statistical assumptions.

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 = 0.580, so ln(HR) = -0.5447.
2. d = 4 × (1.96 + 0.842)² / [ln(0.580)]² = 105.8, rounded up to 106 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 <- 0.58                              # 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(2000622)
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 = 106 (80% power), 142 (90% power)
 75% of observed effect: events = 189 (80% power), 252 (90% power)
 50% of observed effect: events = 424 (80% power), 567 (90% power)
Simulated power with 106 events: 0.767 (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 156 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 302 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 <- 4.2          # control-arm median, months (converted from the posted unit)
hr          <- 0.58          # 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: 94         p (1-sided)   0.0001
  Events: 48        ~HR at bound   0.3410
   Month: 14    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.58   0.0338
   IA 2: 67%                   Z   2.5114
      N: 150         p (1-sided)   0.0060
  Events: 96        ~HR at bound   0.5975
   Month: 23    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.58   0.5603
       Final                   Z   1.9930
      N: 156         p (1-sided)   0.0231
 Events: 143        ~HR at bound   0.7163
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.58   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The sponsor-reported primary analysis gives a hazard ratio of 0.58, a 95% confidence interval from 0.43 to 0.80, and p < 0.001, using the log-rank method. The registry record also lists the primary comparison as a hazard ratio of 0.58 with the same interval and p-value. No discrepancy is identified between these posted primary summaries.

The sponsor’s time-to-event analysis is the principal reported inferential result for the primary outcome. A simple unadjusted re-calculation from posted summary statistics, where available, is not a replacement for the sponsor’s analysis because it may not reproduce the underlying participant-level analysis or its exact procedures. In this record, the primary time-to-event result is presented as the sponsor-reported comparison.

For objective response rate, the registry lists response counts and an unadjusted comparison, but no sponsor-reported analysis. That comparison should be understood as a recalculation from the posted summary information, rather than a reported sponsor model. The registry record does not provide further sponsor analysis details for that outcome.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, treatment comparisons, or analyses. Even if each test uses a conventional significance threshold, conducting many tests can increase the chance that at least one result appears statistically notable by chance. Common general approaches include adjusting the significance threshold, controlling a family-wise error rate, or specifying a hierarchy in which outcomes are tested in a defined order.

The registry record lists a range of secondary outcomes, including time to second progression or death, overall survival, response rate, quality of life, and additional progression-free or overall-survival assessments. It also lists 12 outcome measures and 11 analyses. However, a multiplicity adjustment or testing hierarchy is not reported in the registry record. It is therefore not possible to determine from this record whether the secondary p-values were adjusted, which outcomes belonged to a formal testing family, or whether some were exploratory.

The primary analysis population is identified as the Full Analysis Set, consisting of all randomised patients. Outcome-specific denominators differ for some secondary measures. The registry record does not report all reasons for those denominators, the handling of missing outcome data, or the detailed analysis population for every endpoint. Missing data can affect estimates if participants with unavailable assessments differ systematically from those observed; the direction and size of any effect cannot be determined without further information.

The record does not describe the full prespecified statistical analysis plan, missing-data sensitivity analyses, interim analyses, or all censoring procedures. These omissions limit assessment of whether every analysis followed the original plan and how robust results are to alternative assumptions. They do not erase the posted results, but they define what can be concluded from the registry record alone. Interpretation of secondary findings should remain more cautious than interpretation of the designated primary outcome.

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 (2.4%), febrile neutropenia (2.2%), dyspnoea (2.0%), pyrexia (1.5%), febrile bone marrow aplasia (1.1%).

The registry safety figures report serious adverse events in 37 of 205 participants in the olaparib group and 15 of 91 participants in the chemotherapy group. These are counts of participants affected among the safety groups at risk. The record also lists the most frequent serious adverse event terms and their reported percentages, including anaemia at 2.4%, febrile neutropenia at 2.2%, and dyspnoea at 2.0%.

The registry separately reports other adverse events affecting 196 of 205 participants in the olaparib group and 85 of 91 in the chemotherapy group. It lists 159 deaths in the olaparib safety group and 73 in the chemotherapy safety group. These death counts should not be read as deaths caused by treatment: the record does not establish causation in these figures, and the counts alone do not describe timing, cause, or the role of disease progression.

Safety comparisons require care because the chemotherapy safety group at risk is reported as 91, whereas the primary efficacy population includes 97 participants assigned to chemotherapy. The registry record does not explain that difference in these figures. Counts and percentages also do not capture duration, severity beyond the stated serious classification, or each participant’s full experience. The posted information supports description of reported adverse events, not a causal conclusion about comparative safety.

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

The primary posted result provides statistical evidence of a difference in progression-free survival between olaparib and physician’s choice chemotherapy in the trial population. The reported hazard ratio is below 1, its confidence interval is below 1, and the reported p-value is 0.001. Together, these results support a group-level difference under the analysis reported in the registry record.

This does not mean that all participants assigned to olaparib experienced longer progression-free survival than all participants assigned to chemotherapy. The medians describe the center of estimated time-to-event distributions, and the hazard ratio describes a relative event-rate contrast. Neither gives an individual prediction. The endpoints also do not cover every outcome that matters to participants.

The primary endpoint includes radiological progression or death, rather than overall survival alone. The overall survival result is less conclusive: its confidence interval includes 1, and the record does not establish a difference in overall survival under the reported analysis. This should not be rephrased as proof of equal survival. The registry’s secondary outcomes offer additional context, but uncertainty about multiplicity and analysis details limits their confirmatory interpretation.

The results apply most directly to the enrolled patients with metastatic breast cancer and germline BRCA1/2 mutations, the treatments and regimens used, and the follow-up and assessment procedures described. The record does not justify extending the result automatically to other patient groups, treatment regimens, or settings. Nor does a statistical comparison by itself settle questions about trade-offs, preferences, or individual treatment decisions.

19. Why This Trial Matters Statistically

This trial is statistically informative because it compares randomized groups and uses a clearly defined primary time-to-event outcome. Random assignment supports a group comparison by reducing systematic differences in treatment allocation, while blinded independent central review provides an assessment of radiological progression separate from the open-label treatment assignment. These design features strengthen interpretation of the primary comparison, although they cannot remove every possible bias.

The result also illustrates why a time-to-event summary should be read using more than one statistic. Medians describe a point in each event-time distribution; the hazard ratio summarizes a relative contrast over follow-up; confidence intervals express uncertainty. These summaries complement each other, but they answer different questions and do not yield individual predictions.

The secondary outcomes demonstrate another important statistical issue: a trial can evaluate several distinct outcomes, and their results may not all have the same degree of certainty or relevance to the primary question. Without a reported multiplicity plan, secondary findings should be treated cautiously. The difference between a progression-based endpoint and overall survival also shows why outcomes that sound related should not be treated as interchangeable.

Finally, the registry record distinguishes a sponsor-reported primary analysis from unadjusted calculations based on summary information, and it includes planning illustrations derived from observed effects. Those illustrations are not the original design justification and are not observed power. Keeping those categories separate helps prevent descriptive, inferential, and planning statistics from being mistaken for one another.

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 original sample-size justification or the complete statistical analysis plan. It therefore does not permit a full check of the assumptions used to design the trial, the prespecified handling of multiple outcomes, or all analysis choices. The planning illustrations based on observed effects should not be interpreted as evidence about the original design.

The primary outcome is radiological progression or death, not overall survival alone. Although progression was assessed by blinded independent central review, the trial itself was open label. The registry record does not report the full details of censoring, missing-data handling, or sensitivity analyses, which limits assessment of how alternative assumptions might affect the estimates.

The safety-group denominators differ from the primary efficacy group sizes, and the registry record does not explain the difference. Outcome-specific denominators also vary for response rate. These differences make it important to keep each endpoint’s population in view rather than assume that every analysis uses the same participants.

Some secondary outcomes have posted comparisons, but the multiplicity strategy is not reported. Their results therefore have less clear confirmatory status than the primary outcome. The overall survival comparison is uncertain, and absence of clear evidence of a difference is not evidence that the groups are equivalent.

Finally, the study population is specific: metastatic breast cancer with germline BRCA1/2 mutations, treated with olaparib or one of the physician-selected chemotherapy options. The registry record alone cannot establish how the results apply to populations, treatments, or clinical settings outside that scope.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Assessment of the Efficacy and Safety of Olaparib Monotherapy Versus Physicians Choice Chemotherapy in the Treatment of Metastatic Breast Cancer Patients With Germline BRCA1/2 Mutations. — NCT02000622.
• Registry record last updated 2026-02-13; status last verified 2026-01.
• Results first posted 2017-12-22.
• 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

NCT02000622 is a completed phase III, open-label, randomized, controlled, multicentre, parallel-group study sponsored by AstraZeneca. It enrolled 302 participants with metastatic breast cancer and germline BRCA1/2 mutations and compared olaparib monotherapy with physician’s choice chemotherapy.

The primary outcome was progression-free survival assessed by blinded independent central review using modified RECIST v1.1 in the Full Analysis Set. The sponsor-reported analysis gives a hazard ratio of 0.58, a 95% confidence interval from 0.43 to 0.80, and p < 0.001. The registry record also lists secondary efficacy outcomes and adverse-event figures. Details about the original design justification, multiplicity approach, missing-data procedures, and complete statistical analysis plan are not reported in the registry record.