Testing Two Oral Drugs Combination (Cediranib and Olaparib) Compared to a Single Drug (Olaparib) for Men With Advanced Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Testing Two Oral Drugs Combination (Cediranib and Olaparib) Compared to a Single Drug (Olaparib) for Men With Advanced Prostate Cancer (NCT02893917), a randomized phase 2 study. The primary outcome is Radiographic Progression Free Survival.

2. Clinical Question

The central contrast is between adding cediranib to an olaparib regimen and continuing with olaparib alone. The trial record identifies radiographic progression-free survival as the primary outcome and also lists overall survival, objective response, prostate-specific antigen response, genomic measures, and adverse events as secondary outcomes. Those additional outcomes address different dimensions of the trial: time until an event, tumor response, biological characteristics, and harms. They should not be treated as interchangeable evidence about the primary question.

The registry describes a randomized phase 2 comparison in men with metastatic castration-resistant prostate cancer. The recorded enrollment is 90, with 45 participants assigned to each arm for the primary outcome. The results can therefore be read as a comparison between randomized groups, while keeping in mind that the estimates describe the participants and outcome data recorded for this trial. They do not establish that the findings apply to every patient or setting.

3. Trial Design

The registry record describes a randomized, phase 2, parallel-group study with no masking reported. The trial began on 2017-08-11, and the primary completion date is recorded as 2023-03-14. Its status is active, not recruiting. Enrollment is recorded as 90. For the primary outcome, each arm has 45 participants.

Arm A received olaparib by mouth twice daily and cediranib by mouth once daily on days 1-28. Arm B received olaparib by mouth twice daily on days 1-28. In both arms, cycles were to repeat every 28 days in the absence of disease progression or unacceptable toxicity. These descriptions identify the planned treatment schedules; the registry record does not provide individual-level treatment exposure or adherence information.

The primary outcome is radiographic progression-free survival, assessed from random assignment to the first recorded progression site or death, whichever occurs first. Its timeframe is assessed up to 5 years. The registry lists overall survival and response outcomes as secondary outcomes, along with genomic and adverse-event outcomes. It records 9 outcome measures and 4 analyses, while 6 secondary outcomes are posted.

Randomization supports comparison of the assigned groups, but the record does not report the sequence-generation method, allocation concealment details, or trial-specific assumptions used to determine the original enrollment target. Masking is recorded as none. The registry record also does not report detailed criteria for the analysis populations or participant flow through each outcome. Those omissions limit assessment of how the recorded outcome groups relate to all randomized participants.

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.

Overall Study

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.

6. Primary Endpoint

The registry lists the primary outcome as Radiographic Progression Free Survival, measured over Time interval from random assignment to the date when the first site of disease is found to progress, or death, whichever occurs first, assessed up to 5 years.

Radiographic progression-free survival measures the time from random assignment until the first finding that disease has progressed on imaging or until death, whichever occurs first. It is a time-to-event endpoint: the outcome is not simply whether a participant experienced progression, but how long the participant remained alive without a recorded radiographic progression. The registry specifies a timeframe assessed up to 5 years.

This endpoint is used to capture disease control over time while accounting for the timing of events. In general, time-to-event methods can incorporate participants whose event has not been observed by the end of their available follow-up; their information contributes up to the point at which they are last known to be event-free. The registry record does not describe the censoring rules in detail, so the handling of particular follow-up situations is not reported in the registry record.

The registry states that Kaplan-Meier estimates and log-rank tests will be used for the arm comparison, and that a Cox regression hazard ratio is reported. In general, the Kaplan-Meier method estimates the event-free proportion over time, while the log-rank test compares the observed event patterns between groups. A hazard ratio summarizes the relative event rate over follow-up under the model used. These measures answer related but not identical questions: a median gives a time point on the estimated event-free curve, whereas a hazard ratio compares event rates across the follow-up period.

7. Results Posted in the Registry

• Arm A (Olaparib, Cediranib) vs Arm B (Olaparib): hazard ratio 0.62 (95% CI 0.39–0.97), reported p = 0.036 (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.

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:
  • Arm A (Olaparib, Cediranib) vs Arm B (Olaparib): hazard ratio 1.30 (95% CI 0.70–2.40) (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Arm A (Olaparib, Cediranib) vs Arm B (Olaparib) and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate

• 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:
  • Arm B (Olaparib): 12.9% (4/31) versus 18.2% (6/33) on control; risk difference -5.3 percentage points (95% CI -23.0 to 12.4), risk ratio 0.71 (0.22–2.28); unadjusted two-proportion z-test p = 0.561.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Olaparib) and the control. The interval gives the range of effects that remain compatible with the data.

Prostate-specific Antigen Response Rate

• 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:
  • Arm B (Olaparib): 13.3% (6/45) versus 20.0% (9/45) on control; risk difference -6.7 percentage points (95% CI -22.0 to 8.7), risk ratio 0.67 (0.26–1.72); unadjusted two-proportion z-test p = 0.396.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm B (Olaparib) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover overall survival, objective response, prostate-specific antigen response, genomic characteristics, and adverse events. Together they provide different kinds of information rather than repeated measurements of one outcome. Overall survival is a time-to-event outcome; response endpoints count participants meeting defined criteria; genomic outcomes address biological features; and adverse-event outcomes describe harms. A pattern across these measures can add context, but the measures do not answer the same question as radiographic progression-free survival.

The secondary survival comparison does not point in the same direction as the primary survival estimate, while the recorded response counts are numerically more frequent in the combination arm. The response comparisons are unadjusted and have substantial uncertainty, so they should not be treated as confirming the primary finding. These broad patterns are descriptive; they do not establish that the primary result is or is not replicated by a secondary outcome.

Unadjusted secondary findings carry less weight because multiple outcomes create more opportunities for apparently notable results to arise by chance. The registry record does not report a multiplicity adjustment, a hierarchy for interpreting secondary outcomes, or a detailed plan for controlling the overall false-positive risk. In general, when many outcomes are examined, a nominal p-value for one outcome does not automatically retain the same interpretation it would have in a single prespecified test.

The registry lists 6 secondary outcomes as posted, and reports 9 outcome measures and 4 analyses. It does not report enough detail to establish how every secondary outcome was handled analytically or whether all possible analyses are included. The secondary results are therefore best read as supporting context and hypothesis-generating evidence, not as a substitute for the primary endpoint or as independent confirmation of a definitive conclusion.

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

• Overall Survival
• Objective Response Rate
• Prostate-specific Antigen Response Rate
• Correlation Between Homologous Recombination Deficiency Status and Radiographic Progression Free Survival
• Incidence of Genomic Alterations
• Incidence of Adverse Events

9. Statistical Interpretation

10. Statistical Methods Explained

How is time to an event analyzed?

The primary outcome is a time-to-event measure. Each participant contributes information from random assignment until progression, death, or the end of the participant’s recorded follow-up, according to the endpoint definition and analysis handling. In general, participants who have not had an observed event by the time follow-up ends are censored: their available event-free time is used, without treating them as if they had an event at that point. The detailed censoring rules are not reported in the registry record.

The registry names Kaplan-Meier estimates and log-rank tests for comparing radiographic progression-free survival. In general, a Kaplan-Meier estimate describes the probability of remaining event-free over time, updating as events occur and accounting for censored observations. A log-rank test assesses whether the event-time patterns differ between groups over the observed follow-up. The registry also states that possible confounding variables will be compared for survival with log-rank tests, but it does not identify those variables or give further details of that analysis.

What does the hazard ratio describe?

The reported comparison uses a Cox regression hazard ratio. In general, a hazard is the event rate at a particular point in follow-up among participants who have not yet experienced the event. A hazard ratio compares those rates between groups as represented by the fitted model. A value below 1 indicates a lower estimated event rate in the first group relative to the reference group; a value above 1 indicates a higher estimated rate. This is a relative, model-based summary, not a direct comparison of the number of participants who had an event and not a difference in median survival time.

The interpretation of a Cox hazard ratio relies on assumptions about how the relative hazards behave over time. The registry identifies Cox regression but does not report whether proportional-hazards assumptions were assessed, what diagnostics were used, or whether any alternative model was planned. Those details are not reported in the registry record.

Why are there several confidence-interval methods?

The primary-outcome description says that a Rothman confidence interval based on Greenwood’s variance, a Thomas and Grunkemeier confidence interval, and simultaneous confidence bands by Nair and Hall and Wellner will be reported. In general, Greenwood’s variance estimates uncertainty in a Kaplan-Meier curve. Confidence intervals and simultaneous bands express uncertainty around estimated survival patterns, using different constructions and intended coverage properties. The registry record does not identify which of these methods corresponds to each particular posted estimate, so a reader should not assume that every listed method was used for every displayed statistic.

The reported primary comparison also includes a 95% confidence interval for the Cox hazard ratio. In general, a confidence interval gives a range of estimates compatible with the observed data and the method’s assumptions at its stated confidence level. It is not a range containing a fixed proportion of individual participants’ outcomes, and it does not account for every possible source of bias or uncertainty.

How should the response outcomes be analyzed?

Objective response and prostate-specific antigen response are recorded as participant counts. For a binary outcome, the event is whether each participant met the outcome definition during the stated timeframe. In general, a risk difference compares the proportions meeting the outcome between groups, while a risk ratio compares those proportions as a ratio. An odds ratio compares the odds rather than the proportions directly. The registry does not post sponsor-reported analyses for these two response outcomes. The unadjusted comparisons are therefore not equivalent to a sponsor-reported adjusted analysis.

In general, uncertainty around a binary comparison depends on the number of participants with outcome data and the number meeting the response definition. The objective-response counts use different recorded denominators from the primary outcome groups, so those response estimates represent the outcome data recorded for those participants. Reasons for the difference in denominators are not reported in the registry record.

What do the analysis labels establish?

The primary analysis is labeled as a superiority analysis, and the comparison is reported with a Cox regression hazard ratio and p-value. A superiority label describes the purpose of the statistical comparison; it does not guarantee a particular result or establish clinical importance. The registry record does not report the complete statistical analysis plan, including all model specifications, covariate choices, or planned sensitivity analyses. The sponsor’s reported analysis is the principal analysis to interpret for the primary time-to-event endpoint.

11. Confidence Intervals and Precision

The primary hazard ratio is reported as 0.617 with a 95% confidence interval from 0.392 to 0.969. In general, a confidence interval represents statistical uncertainty in an estimate under the model and assumptions used. The interval indicates that the estimate is not exact: values across the reported range remain compatible with the data and method at the stated confidence level. It does not capture every uncertainty, such as possible selection, measurement, or modeling problems.

For a hazard ratio, 1 is the value corresponding to equal estimated hazards between groups. The primary interval lies below 1, while still spanning a range of possible relative effects. The interval is consequently informative both about direction, under the analysis, and about uncertainty in magnitude. It should be interpreted alongside the point estimate, the reported p-value of 0.036, the endpoint definition, and the trial’s scale.

The reported medians are 8.5 months for the combination arm and 4.0 months for olaparib alone. Their confidence intervals are 5.4 to 12.0 months and 3.2 to 8.5 months, respectively. These intervals describe uncertainty in the median estimates, not the spread of individual participants’ event times. The intervals overlap; that fact alone is not a formal test of the difference between groups. The registry’s reported comparison is the Cox analysis rather than a test derived from the two median intervals.

Precision is also affected by the amount of observed follow-up and the number and timing of events. The registry record does not report detailed event counts for the primary analysis or the number of participants censored at each time. Those details are not reported in the registry record, limiting a fuller assessment of how much information supports the survival estimates.

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 enrollment design. For time-to-event outcomes, the figures are total events required across both arms. For other outcomes, the figures are participants per arm. Thus the progression-free survival and overall survival illustrations should be read as event totals, while the response-outcome illustrations should be read separately as per-arm participant counts.

The stated assumptions for these illustrations 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 in turn to 100%, 75%, or 50% of the observed effect. The registry record does not report the assumptions used for the trial’s original design or its enrollment target; these illustrations are not evidence of those original assumptions.

The 80% power column describes the planned number of events or participants under which a test would have an 80% chance of detecting the specified effect if that effect and the planning assumptions were true. The 90% power column describes the corresponding target for a 90% chance. These are planning concepts, not guarantees about a future study, and they do not indicate the probability that the observed result is true.

Smaller effects require more information to detect reliably. In the illustrations, planning for a smaller fraction of the observed effect therefore entails larger event or participant targets than planning for the full observed effect. The values are not observed power for this trial; observed power is not a useful substitute for interpreting its estimate and confidence interval.

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 = 0.617, so ln(HR) = -0.4829.
2. d = 4 × (1.96 + 0.842)² / [ln(0.617)]² = 134.6, rounded up to 135 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 <- 0.617                              # 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(2893917)
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 = 135 (80% power), 181 (90% power)
 75% of observed effect: events = 240 (80% power), 321 (90% power)
 50% of observed effect: events = 539 (80% power), 721 (90% power)
Simulated power with 135 events: 0.816 (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 197 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 90 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          # control-arm median, months (converted from the posted unit)
hr          <- 0.617          # 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: 114         p (1-sided)   0.0001
  Events: 61        ~HR at bound   0.3855
   Month: 14    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.62   0.0338
   IA 2: 67%                   Z   2.5114
      N: 186         p (1-sided)   0.0060
 Events: 122        ~HR at bound   0.6337
   Month: 23    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.62   0.5603
       Final                   Z   1.9930
      N: 198         p (1-sided)   0.0231
 Events: 182        ~HR at bound   0.7441
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.62   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 comparison, the sponsor-reported Cox regression estimate is a hazard ratio of 0.617, with a 95% confidence interval from 0.392 to 0.969 and p = 0.036. The registry also describes Kaplan-Meier estimates and log-rank tests for the primary comparison. The reported Cox estimate is the sponsor’s analysis and is the appropriate result to treat as the principal analysis for this endpoint.

There is no recorded discrepancy between the sponsor’s primary analysis and the posted primary comparison. Where a result is labeled as recalculated, it is an unadjusted calculation from posted summary statistics, not a replacement for a sponsor’s model-based analysis. The primary endpoint is a time-to-event outcome, and the registry’s method meaning specifies use of the sponsor-reported hazard ratios rather than an independent recalculation of that comparison.

The secondary response outcomes do not have sponsor-reported analyses posted in the record. Their unadjusted comparisons can be useful as descriptive checks, but they do not have the same status as a prespecified sponsor analysis with documented modeling details. The registry record does not report a complete statistical analysis plan that would allow readers to reconstruct all modeling decisions or establish whether additional analyses were undertaken.

16. Multiplicity, Missing Data and Analysis Populations

The record identifies one primary endpoint and lists several secondary outcomes, but a multiplicity strategy is not reported in the registry record. In general, multiplicity arises when several hypotheses or outcomes are tested: the more comparisons made, the greater the chance that at least one result may appear statistically notable by chance. Prespecifying an outcome hierarchy or adjusting the testing procedure can address this issue, but neither approach is described in the registry record.

The primary result is reported with a p-value and confidence interval, while the secondary response analyses are unadjusted. Without a documented plan for how the primary and secondary hypotheses relate, secondary p-values should be interpreted cautiously. The registry record does not state whether secondary testing was exploratory, whether any adjustment was applied outside the posted analyses, or how the findings were intended to be interpreted collectively.

Details about missing outcome data are also limited. The objective response outcome has recorded denominators of 33 in Arm A and 31 in Arm B, compared with 45 assigned to each arm for the primary outcome. The record does not explain why the objective-response denominators differ or describe how missing response assessments were handled. The participant populations used for each analysis, including any intention-to-treat or per-protocol definitions, are not reported in the registry record.

The primary outcome description names possible confounding variables, but does not identify them or report how they were selected. The registry record does not report the planned covariates for the Cox model, detailed censoring rules, missing-data sensitivity analyses, or a complete statistical analysis plan. These omissions do not invalidate the posted estimates, but they restrict independent assessment of analysis choices, the completeness of outcome data, and the robustness of the results.

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: dyspnea (13.6%), confusion (9.1%), acute kidney injury (8.9%), anemia (8.9%), creatinine increased (8.9%).

The registry reports serious adverse events in 21 participants among the 44 at risk in Arm A and 21 among the 45 at risk in Arm B. It separately records other adverse events in 44 of 44 at risk in Arm A and 45 of 45 at risk in Arm B. Death counts are 35 in Arm A and 34 in Arm B. These are recorded counts and denominators; they should not be read as a direct comparison of severity or cause without further event-level information.

The most frequently listed serious-event terms include dyspnea at 13.6%, confusion at 9.1%, acute kidney injury at 8.9%, anemia at 8.9%, increased creatinine at 8.9%, and other general disorders and administration-site conditions at 8.9%. These percentages describe the registry’s listed terms. The record does not provide enough detail to determine event duration, recurrence, attribution to a study drug, or overlap among participants with different events.

In general, adverse-event counts need to be interpreted with their definitions, observation periods, denominators, and collection procedures in mind. The registry record does not report a full account of exposure time or detailed arm-specific event coding rules. The counts should therefore be treated as descriptive safety information, not as a complete causal comparison.

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

The primary result describes a statistically notable difference in radiographic progression-free survival between the randomized groups under the reported analysis. The estimated hazard ratio is below 1, its 95% confidence interval does not include 1, and the registry reports p = 0.036. The medians also differ in the direction of a longer estimated progression-free time in Arm A. These are findings about the trial’s recorded group-level outcomes.

The result does not mean every participant in the combination arm had a longer progression-free period, nor does it predict an individual participant’s course. A hazard ratio is a relative summary of event rates under a model, not a direct probability of benefit for a particular person. The median is a group summary, not a guaranteed duration. Neither statistic identifies the reason for the observed pattern.

The result also does not establish that the combination improves every outcome. Overall survival and response outcomes have distinct definitions and uncertainty, and the secondary analyses are not equivalent to the primary analysis. The registry record does not report a multiplicity approach or enough analysis detail to resolve every question about the secondary findings.

General interpretation of a randomized comparison still depends on trial conduct, completeness of follow-up, analysis choices, and the applicability of the enrolled population. Some of those details are not reported in the registry record. The trial is phase 2 and records enrollment of 90, so its estimates should be understood in that study context rather than as a universal conclusion. Statistical evidence, precision, design, and limitations all matter when interpreting the result; none alone settles the full meaning of the comparison.

19. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison should not be reduced to a single p-value. The primary endpoint is time to radiographic progression or death, and its analysis combines estimated event-free patterns with a model-based hazard ratio. The median and hazard ratio summarize different aspects of those patterns. Reading them together helps distinguish a time point on an estimated curve from a relative event-rate comparison across follow-up.

The record also makes the role of uncertainty visible. The primary hazard-ratio interval excludes 1 but still covers a range of effect sizes. That distinction matters: statistical compatibility with a difference does not mean the magnitude is known precisely. The secondary outcomes further demonstrate that endpoints can point in different directions or carry different levels of information, particularly when data are incomplete or analyses are unadjusted.

Finally, the registry separates observed trial results from planning illustrations. Sample-size calculations based on an observed effect can help readers understand how study size relates to the ability to detect effects, but they do not recover the original design rationale and are not observed power. This is a useful statistical distinction when interpreting modest-sized phase 2 trials. The record supports careful description of the estimates while leaving important design and analysis details unresolved.

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 recorded enrollment is 90, with 45 participants per arm for the primary outcome. This is a phase 2 trial, and the size of the study affects how much information is available for estimating outcomes, particularly when events are limited or follow-up is incomplete. The registry does not report the total number of primary events or detailed follow-up distribution, so the contribution of event information cannot be fully assessed.

The record reports no masking. Lack of masking can matter for outcomes involving clinical assessment or decisions about when to evaluate progression, although the registry does not provide enough detail to assess whether or how this affected this trial. The assessment procedures and radiographic review arrangements are not reported in the registry record.

The objective-response denominators are smaller than the 45 assigned to each arm for the primary outcome. Reasons for that difference, eligibility for the response analysis, and missing-data handling are not reported in the registry record. Analysis-population definitions and the details of censoring are also not reported. These gaps limit evaluation of whether outcome availability could have affected the secondary comparisons.

The registry record does not report the original sample-size justification, a complete statistical analysis plan, multiplicity handling, or detailed model diagnostics. It also does not identify the possible confounding variables mentioned in the primary outcome description. The primary result is therefore interpretable as reported, but independent evaluation of all modeling and robustness decisions is limited. The secondary analyses should be considered with particular caution because sponsor-reported analyses are not posted for the response outcomes and a multiplicity plan is not recorded.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Testing Two Oral Drugs Combination (Cediranib and Olaparib) Compared to a Single Drug (Olaparib) for Men With Advanced Prostate Cancer — NCT02893917.
• Registry record last updated 2026-07-31; status last verified 2026-06.
• Results first posted 2025-03-30.
• 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 randomized phase 2, parallel-group study with no masking reported, comparing olaparib plus cediranib with olaparib alone in men with metastatic castration-resistant prostate cancer. Enrollment is 90, with 45 participants in each arm for the primary outcome. The recorded status is active, not recruiting.

The primary endpoint is radiographic progression-free survival, defined from random assignment to progression or death, whichever occurs first, and assessed up to 5 years. The sponsor-reported Cox hazard ratio is 0.617, with a 95% confidence interval from 0.392 to 0.969 and p = 0.036. The record also includes overall survival, response, genomic, and adverse-event outcomes.

The primary estimate is statistically notable under the reported analysis, but uncertainty remains about its magnitude and the registry does not report several details needed to assess the full analysis plan, missing data, or multiplicity. Secondary findings are best treated as context rather than independent confirmation.