Cabazitaxel Versus Docetaxel Both With Prednisone in Patients With Metastatic Castration Resistant Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cabazitaxel Versus Docetaxel Both With Prednisone in Patients With Metastatic Castration Resistant Prostate Cancer (NCT01308567), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, open-label, multicenter, parallel-group study. The registry lists enrollment of 1168 and three treatment groups: docetaxel 75 mg/m^2, cabazitaxel 20 mg/m^2, and cabazitaxel 25 mg/m^2, each combined with prednisone. The primary objective was to demonstrate superiority of either cabazitaxel regimen over docetaxel for overall survival among participants with metastatic castration resistant prostate cancer who had not previously received chemotherapy.

Randomization assigns participants to study groups by chance, which is intended to support fair comparison of outcomes. Open-label means that masking was not used; the registry records masking as none. Awareness of assigned treatment can matter when outcomes involve participant or investigator judgment, although overall survival is based on death from any cause. The specific procedures used to preserve allocation concealment or reduce assessment bias are not reported in the registry record.

The primary analysis included all randomized participants, according to the registry’s description of the intention-to-treat population. The primary follow-up window began at baseline and continued until death or the study cut-off date, whichever was earlier, with a maximum duration of 51 months. The final overall-survival analysis cut-off was defined by the observation of the 774th death. The registry lists a study start of 2011-05-05, primary completion in 2015-09, and status as completed.

Each cabazitaxel dose was infused on Day 1 of each 21-day cycle, with daily oral prednisone. Docetaxel was likewise given on Day 1 of each 21-day cycle with daily prednisone. The registry says treatment continued until disease progression, unacceptable toxicity, or participant refusal. Details of stratification, allocation implementation, adherence, and protocol deviations are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 1168 participants randomized in this study. Of these, 21 participants randomized but not treated. These participants were included in intent-to-treat (ITT) population, not in safety population. "Study cut-off date" for outcome measures was up to "primary completion date" (PCD) only. After PCD, only adverse event (AE) data was updated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population included all randomized participants.

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 Overall Survival (OS), measured over Baseline up to death or study cut-off date, whichever was earlier (maximum duration: 51 months ).

Overall survival measures the time from randomization until death from any cause. The registry defines the endpoint as the interval from randomization to death. If a death was not confirmed, the participant’s survival time was censored at the last date they were known to be alive, or at the cut-off date if their last contact occurred after that date.

This endpoint is used in clinical trials because it captures survival regardless of the cause of death and does not depend on a judgment about whether a tumor has progressed. In general, a time-to-event analysis can include participants whose event has not yet been observed by the analysis cut-off, using their available follow-up rather than treating them as if an event had occurred. Censoring does not mean that the participant experienced the event; it indicates that the event time was not observed during the relevant follow-up.

The registry reports median overall survival for each group, with a 95% confidence interval, and describes the primary analysis as using the Kaplan-Meier method. The median is the estimated time by which half of the analyzed group’s survival distribution has experienced the event. It does not describe each participant’s survival time, and it does not by itself quantify the relative event rate between groups. For that comparison, the registry also reports hazard ratios from log-rank analyses.

The primary timeframe was baseline to death or study cut-off, whichever was earlier, with a maximum duration of 51 months. The cut-off for the final overall-survival analysis was the date when the 774th death had been observed.

7. Results Posted in the Registry

• Docetaxel 75 mg/m^2 vs Cabazitaxel 25 mg/m^2: hazard ratio 0.97 (95% CI 0.82–1.16), reported p = 0.757 (as reported in the registry).
• Docetaxel 75 mg/m^2 vs Cabazitaxel 20 mg/m^2: hazard ratio 1.01 (95% CI 0.85–1.20), reported p = 0.997 (as reported in the registry).

8. Secondary Efficacy Endpoints

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

Progression Free Survival (PFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Docetaxel 75 mg/m^2 vs Cabazitaxel 25 mg/m^2: hazard ratio 0.99 (95% CI 0.85–1.15) (as reported in the registry).
  • Docetaxel 75 mg/m^2 vs Cabazitaxel 20 mg/m^2: hazard ratio 1.06 (95% CI 0.91–1.24) (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 Docetaxel 75 mg/m^2 vs Cabazitaxel 25 mg/m^2 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 Docetaxel 75 mg/m^2 vs Cabazitaxel 20 mg/m^2 and the control. The interval gives the range of effects that remain compatible with the data.

Time to Tumor Progression Free Survival

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Docetaxel 75 mg/m^2 vs Cabazitaxel 25 mg/m^2: hazard ratio 0.96 (95% CI 0.79–1.17) (as reported in the registry).
  • Docetaxel 75 mg/m^2 vs Cabazitaxel 20 mg/m^2: hazard ratio 0.92 (95% CI 0.75–1.12) (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 Docetaxel 75 mg/m^2 vs Cabazitaxel 25 mg/m^2 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 Docetaxel 75 mg/m^2 vs Cabazitaxel 20 mg/m^2 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Overall Objective Tumor Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cabazitaxel 20 mg/m^2: 32.4% (61/188) versus 30.9% (54/175) on control; risk difference 1.6 percentage points (95% CI -8.0 to 11.2), risk ratio 1.05 (0.78–1.42); unadjusted two-proportion z-test p = 0.745.
  • Cabazitaxel 25 mg/m^2: 41.6% (72/173) versus 30.9% (54/175) on control; risk difference 10.8 percentage points (95% CI 0.7 to 20.8), risk ratio 1.35 (1.02–1.79); unadjusted two-proportion z-test p = 0.037.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cabazitaxel 20 mg/m^2 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cabazitaxel 25 mg/m^2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several domains: progression-free survival, tumor progression, objective tumor response, prostate-specific antigen response and progression, pain response and progression, skeletal-related events, quality of life, safety, and pharmacokinetic and pharmacogenomic assessments. The registry’s posted numerical secondary results include selected efficacy outcomes, while not every listed objective has a result described in the record. Details for outcomes without posted numerical results are not reported in the registry record.

Across the posted secondary efficacy comparisons, the estimates do not form a uniformly separated pattern from the docetaxel group. Time-to-event estimates have confidence intervals that include the no-difference reference value, and the response comparisons have varying estimates and uncertainty. These secondary results provide context about different aspects of disease progression and response, but they do not overturn the primary overall-survival interpretation. Each outcome has a distinct definition and analysis population, so a pattern across outcomes should be considered cautiously rather than treated as one combined result.

Secondary analyses usually carry less confirmatory weight when many outcomes or comparisons are examined. In general, testing numerous outcomes increases the chance that some apparently notable result will occur by chance. A prespecified multiplicity strategy can address this issue by controlling error across comparisons, but such a strategy is not reported in the registry record. The posted secondary results should therefore be viewed as supportive or exploratory evidence unless the complete analysis plan establishes otherwise.

The registry describes the primary analysis population as all randomized participants, while some secondary outcomes necessarily relate to specific outcome definitions or measurable disease. Endpoint-specific denominators and analysis details should be considered when comparing results. Secondary results can help identify questions for further study, but they should be interpreted in conjunction with the primary endpoint, uncertainty, and the degree of multiplicity control documented for the trial.

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

• Progression Free Survival (PFS)
• Time to Tumor Progression Free Survival
• Percentage of Participants With Overall Objective Tumor Response
• Time to Prostate Serum Antigen Progression Free Survival (PSA-PFS)
• Percentage of Participants With PSA Response
• Time to Pain Progression Free Survival (Pain PFS)
• Percentage of Participants With Pain Response
• Skeletal Related Events (SRE) Free Survival

9. Statistical Interpretation

10. Statistical Methods Explained

What does the Kaplan-Meier method do?

In general, the Kaplan-Meier method estimates the pattern of time to an event while accounting for participants whose event time is not observed before the end of follow-up. Participants with known event times contribute information up to their event. Participants who are censored contribute information up to the time they were last known to be event-free. The method produces an estimated survival curve and can be used to estimate a median time to event. The registry says this method was used for the overall-survival analysis. The specific implementation details are not reported in the registry record.

How should the hazard ratio be understood?

In general, a hazard ratio compares the event rates between groups over the observed follow-up, subject to assumptions of the analysis. A value near 1 indicates that the estimated event rates are similar in the comparison as parameterized; values on either side of 1 indicate different estimated directions. A hazard ratio is not a direct comparison of median survival times, nor does it say how many months an individual participant may live. The registry reports hazard ratios and confidence intervals for the primary comparisons, using the log-rank method.

The listed comparison labels are docetaxel versus cabazitaxel. Interpretation of the direction depends on how the ratio was parameterized, so the estimates are best read alongside their stated group comparison and the reported confidence interval. The confidence intervals include 1 for both primary comparisons. The registry’s stated p-values are 0.757 and 0.997.

What does a confidence interval convey?

In general, a confidence interval describes the uncertainty around an estimate under a statistical procedure. A narrower interval indicates greater precision than a wider interval, all else equal. A 95% confidence interval is not a guarantee that the true value lies inside that particular interval. It is a method-based interval whose long-run coverage is described by its confidence level. When an interval for a hazard ratio includes 1, the data are compatible with no relative difference under the comparison, as well as with some effects on either side of that value.

How do p-values fit with the estimates?

In general, a p-value measures how compatible the observed data are with a specified null hypothesis, under the model and assumptions used. It does not measure the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The registry reports p-values for the primary overall-survival comparisons. A p-value should be considered alongside the estimate, confidence interval, trial objective, and analysis plan, rather than treated as a complete summary of the evidence.

What does intention-to-treat mean?

In general, an intention-to-treat analysis retains participants in the groups to which they were randomized, regardless of later treatment changes or adherence, according to the defined analysis rules. This preserves the randomized comparison and estimates the effect of assignment under the trial’s conduct. The registry explicitly defines the primary population as all randomized participants. It does not describe the detailed handling of missing follow-up, treatment discontinuation, or other protocol events for every endpoint.

Why can endpoint-specific methods differ?

Time-to-event outcomes are analyzed differently from binary outcomes such as whether a response occurred. For a time-to-event outcome, the timing of an event and censoring are relevant. For a binary outcome, a comparison may instead describe the difference between observed response proportions. In general, these methods answer related but distinct questions, and their estimates should not be treated as interchangeable.

The registry reports secondary time-to-event outcomes with medians and confidence intervals, and reports tumor response as a percentage with a confidence interval. It also lists hazard ratios for secondary time-to-event comparisons, but does not list p-values or methods for those comparisons. For tumor response, the posted recalculations are unadjusted comparisons based on the summarized data. They do not replace the sponsor’s primary analysis, and they do not account for any adjustment that may have been used outside the registry record.

General statistical interpretation also depends on assumptions about outcome measurement, censoring, follow-up, and the analysis model. The registry describes the endpoint definitions and some methods, but additional model checks, missing-data procedures, and analysis-plan details are not reported in the registry record. Statistical results should therefore be interpreted at the level of detail the record supports.

11. Confidence Intervals and Precision

The primary overall-survival medians are reported with 95% confidence intervals. For docetaxel, the median is 24.3 months and the interval is 22.18 to 27.6 months. For cabazitaxel 20 mg/m^2, the median is 24.5 months and the interval is 21.75 to 27.2 months. For cabazitaxel 25 mg/m^2, the median is 25.2 months and the interval is 22.9 to 26.97 months. These intervals communicate uncertainty in each median estimate; they are not ranges containing most individual participants’ survival times.

The relative comparisons are also uncertain. The 95% confidence interval for the docetaxel versus cabazitaxel 25 mg/m^2 hazard ratio is 0.819 to 1.16. For docetaxel versus cabazitaxel 20 mg/m^2, it is 0.85 to 1.197. Since each interval includes 1, the posted estimates do not distinguish a relative effect from no difference at the conventional reference value. They also include values on both sides of that reference, so the direction and magnitude of any difference are not pinned down precisely.

Confidence intervals address sampling uncertainty under the analysis method. They do not capture every possible source of uncertainty, such as differences in trial conduct, measurement, or applicability to other settings. In general, interval width is best interpreted together with the endpoint, estimate, and study design. The registry does not report additional precision measures or sensitivity analyses for the primary result.

The medians and hazard ratios answer different questions. The medians summarize the estimated time at which half of the survival distribution has experienced the event, while the hazard ratios compare event rates across follow-up under the analysis. Neither measure should be substituted for the other. The reported confidence intervals are central to interpretation: a point estimate by itself can obscure how much uncertainty remains.

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 translate an observed effect into hypothetical sample-size or event-count requirements under stated assumptions. For binary outcomes, the entries are participants per arm. For time-to-event outcomes, the entries are total events, not participants per arm. The primary overall-survival planning figures are therefore total event counts. They are not a forecast of how many participants would be enrolled in a future study.

The stated 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 expressed as a stated fraction of the observed effect. For time-to-event outcomes, the calculation uses the Schoenfeld approach. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the hypothetical number of participants per arm, or total events for time-to-event outcomes, associated with an 80% chance of detecting the specified effect under the calculation assumptions if that effect were the true effect. The 90% column describes the corresponding requirement for a higher chance of detection. Higher power generally requires more information, which may mean more participants or more events.

Rows that plan for a smaller fraction of the observed effect require larger sample sizes or event counts. This reflects a general statistical principle: a smaller difference is harder to distinguish from random variation. Because the calculations use the observed effect as their starting point, they are illustrative and can be sensitive to uncertainty in that estimate. These figures are not observed power and do not describe the power achieved by this trial.

For the primary time-to-event endpoint, the figures are event totals; for the response outcome, they are per-arm participant counts. The units matter when reading the entries, and the two types of planning figures should not be compared as though they were the same quantity.

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 = 0.975, so ln(HR) = -0.0253.
2. d = 4 × (1.96 + 0.842)² / [ln(0.975)]² = 48,979.6, rounded up to 48,980 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 <- 0.975                              # 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(1308567)
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 = 48,980 (80% power), 65,570 (90% power)
 75% of observed effect: events = 87,075 (80% power), 116,569 (90% power)
 50% of observed effect: events = 195,919 (80% power), 262,280 (90% power)
Simulated power with 48,980 events: 0.794 (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 107,761 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 1,168 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 <- 24.3          # control-arm median, months (converted from the posted unit)
hr          <- 0.975          # 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: 95260         p (1-sided)   0.0001
 Events: 22115        ~HR at bound   0.9513
     Month: 21    P(Cross) if HR=1   0.0001
               P(Cross) if HR=0.98   0.0338
     IA 2: 67%                   Z   2.5114
     N: 107762         p (1-sided)   0.0060
 Events: 44229        ~HR at bound   0.9764
     Month: 34    P(Cross) if HR=1   0.0060
               P(Cross) if HR=0.98   0.5603
         Final                   Z   1.9930
     N: 107762         p (1-sided)   0.0231
 Events: 66344        ~HR at bound   0.9846
     Month: 60    P(Cross) if HR=1   0.0250
               P(Cross) if HR=0.98   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 registry reports the sponsor’s overall-survival analyses as hazard ratios from log-rank comparisons. For docetaxel versus cabazitaxel 25 mg/m^2, the reported hazard ratio is 0.975, with a 95% confidence interval of 0.819 to 1.16 and p = 0.757. For docetaxel versus cabazitaxel 20 mg/m^2, the reported hazard ratio is 1.009, with a 95% confidence interval of 0.85 to 1.197 and p = 0.997.

The record does not flag a discrepancy between the posted primary estimates and their reported analyses. The displayed interpretation therefore rests on the sponsor-reported hazard ratios and their intervals, rather than a newly reconstructed time-to-event analysis. Reconstructing a hazard ratio from group medians would not be a valid substitute, because the median values do not contain the full event-time and censoring information.

For the binary tumor-response outcome, the posted simple comparisons are unadjusted recalculations from the summary counts and are not identified as sponsor-reported analyses. Those calculations can help describe the raw contrast, but they do not establish what adjusted method, if any, the sponsor used outside the registry record. The registry does not list a p-value for the sponsor’s secondary time-to-event comparisons.

The sponsor’s reported primary analysis is the relevant result for the stated primary objective. Its confidence intervals and p-values should be read together with the medians and the study design, not replaced by an informal comparison of point estimates.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, treatment comparisons, or analyses. In general, the more statistical tests performed, the greater the chance that at least one result may appear notable by chance if each test is considered separately. A prespecified strategy may allocate error across comparisons, specify a testing sequence, or distinguish confirmatory from exploratory outcomes. The registry lists numerous secondary objectives and reports multiple comparisons, but a multiplicity adjustment or testing hierarchy is not reported in the registry record.

Because the adjustment strategy is not available in the record, the secondary p-values and estimates should not be treated as though they necessarily represent a single controlled confirmatory testing program. The primary overall-survival result remains the central test of the stated primary objective. This does not mean that secondary outcomes are uninformative; it means that their inferential strength depends on analysis-plan details that are not reported in the registry record.

The registry identifies the primary population as all randomized participants. It does not describe in detail how missing endpoint data were handled, how loss to follow-up was treated beyond the stated censoring rule for overall survival, or whether sensitivity analyses assessed the effect of missing information. The survival definition states that participants without confirmed death were censored at the last known alive date, or at the cut-off date under the specified condition. The broader assumptions and checks for censoring are not reported.

Allocation was randomized, and the study was open label. The registry does not report detailed allocation-concealment procedures, outcome-adjudication processes, or masking for specific assessments. It also does not report the full statistical analysis plan, protocol deviations, or the rules governing analysis populations for all secondary outcomes. These omissions limit how fully the posted results can be audited and how confidently secondary findings can be placed within the trial’s original confirmatory framework.

These are limits of the registry record, not evidence that a procedure was absent. The appropriate conclusion is that these details are not reported in the registry record.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: febrile neutropenia (10.2%), neutropenic infection (5.4%), haematuria (3.3%), pneumonia (3.1%), neutropenia (2.6%).

The safety summary gives, for each treatment group, the number at risk for the serious adverse event summary and the number affected. For docetaxel, the registry lists 387 at risk and 126 affected. For cabazitaxel 20 mg/m^2, it lists 369 at risk and 127 affected. For cabazitaxel 25 mg/m^2, it lists 391 at risk and 188 affected. The record also lists the number at risk and affected for other adverse events, but these counts should not be combined with the serious-event counts.

The registry lists febrile neutropenia at 10.2%, neutropenic infection at 5.4%, haematuria at 3.3%, pneumonia at 3.1%, neutropenia at 2.6%, and diarrhoea at 2.6% among the top serious terms. These are reported terms, not a complete account of every adverse event. The registry does not provide death counts in this safety summary.

Counts at risk and counts affected describe the safety summary as posted; they are not by themselves adjusted comparisons between regimens. The record does not supply additional information on event timing, severity grading, attribution, exposure duration, or statistical comparisons. Therefore, the figures should be read descriptively and in the context of the specific adverse-event definitions and analysis procedures, which are not fully reported in the registry record.

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

The posted results describe a randomized comparison of three regimens in participants with metastatic castration resistant prostate cancer who had not previously received chemotherapy. The primary endpoint was overall survival. The reported medians are close, and both sponsor-reported hazard-ratio confidence intervals include 1. The reported p-values are 0.757 and 0.997. Taken together, the posted primary analyses do not demonstrate superiority of either cabazitaxel regimen over docetaxel for overall survival.

That conclusion does not establish that the regimens are equivalent or that their effects are identical. Equivalence and noninferiority require their own prespecified margins and statistical frameworks, which are not reported in the registry record. A nonsignificant superiority result can reflect a small effect, uncertainty, or both. The confidence intervals indicate that the relative effects are estimated with uncertainty, so the point estimates should not be treated as exact.

The findings also do not answer every question about the treatments. The registry includes secondary efficacy and safety outcomes, but the number of outcomes and the absence of a reported multiplicity strategy limit how strongly isolated secondary findings can be interpreted. The safety summaries offer descriptive counts and serious-event terms, but the record does not report enough detail to infer comparative safety from those counts alone.

These results apply to the trial population and its treatment regimens as studied. The registry describes the population as participants with the specified disease who had not previously received chemotherapy; the record does not provide every detail needed to judge applicability to other populations or care settings. Results from this trial should not be generalized beyond the studied context without considering those differences.

Overall, the registry supports a restrained statistical conclusion: the primary comparisons do not show a clear overall-survival difference, while the precision and reporting limitations leave uncertainty. The findings are not medical advice and do not determine which treatment is appropriate for an individual.

19. Why This Trial Matters Statistically

This trial illustrates why the primary endpoint, effect estimate, and uncertainty need to be read together. The median survival values give a familiar time-scale summary, but they do not fully describe the event-time distributions or serve as a substitute for a comparative analysis. The hazard ratios and confidence intervals add a relative comparison over follow-up, while the p-values address compatibility with a specified null hypothesis under the analysis.

The results also demonstrate the distinction between failing to establish superiority and establishing equivalence. A superiority objective asks whether the evidence supports an advantage under the planned comparison. If the analysis does not show a clear difference, that does not by itself prove that the treatments have the same effect. Equivalence or noninferiority requires a prespecified margin and a corresponding design and analysis; those details are not reported in the registry record.

Multiple secondary outcomes can provide a broader view of disease progression, response, and safety, but they raise questions about multiplicity and the status of individual findings. Without a reported testing strategy, secondary results deserve more cautious interpretation than the primary analysis. This is especially important when endpoints use different definitions, populations, and statistical methods.

The study also highlights that registry reporting determines how much of the analysis can be independently assessed. The record identifies the primary population, endpoint definition, Kaplan-Meier method, and log-rank comparisons. Important details about missing data, multiplicity, and the full statistical plan are not reported. Clear reporting of these elements helps readers distinguish what the posted data establish from what remains uncertain.

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 full statistical analysis plan, the original sample-size justification, or the procedures used to address multiplicity across the many secondary objectives. It also does not report detailed missing-data methods or sensitivity analyses for the primary and secondary outcomes. These omissions limit assessment of whether all analyses followed a prespecified plan and how robust the findings are to analytic choices.

The primary outcome is reported with medians, confidence intervals, hazard ratios, and p-values, but details beyond the named Kaplan-Meier and log-rank methods are not reported. The registry does not provide the underlying survival curves or participant-level event-time data in this record. As a result, the posted summaries do not permit independent reconstruction of the time-to-event analysis or examination of how the relative event rate may have varied over follow-up.

The trial was open label. Overall survival is less dependent on subjective assessment than some outcomes, but awareness of treatment can still affect aspects of trial conduct and assessment for other endpoints. The registry does not report detailed protections against assessment bias or whether outcome adjudication was used.

The secondary outcomes vary in definition and may involve different analysis populations. Some outcomes are listed as objectives without numerical results in the record, and the registry does not report all endpoint-specific analysis details. The safety summary is descriptive and does not include death counts; event exposure, attribution, and comparative statistical analyses are not reported in the safety information.

Finally, the record describes a particular population and regimen, but does not include every clinical eligibility detail. Application beyond participants with the stated disease and treatment history requires consideration of differences that cannot be assessed from the registry record alone.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Cabazitaxel Versus Docetaxel Both With Prednisone in Patients With Metastatic Castration Resistant Prostate Cancer — NCT01308567.
• Registry record last updated 2019-06-05; status last verified 2019-05.
• Results first posted 2017-03-03.
• 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 completed, randomized, open-label, Phase 3, parallel-group comparison of docetaxel plus prednisone with cabazitaxel 20 mg/m^2 or 25 mg/m^2 plus prednisone in participants with metastatic castration resistant prostate cancer who had not previously received chemotherapy. The primary endpoint was overall survival, analyzed in the intention-to-treat population using the Kaplan-Meier method.

The sponsor-reported hazard-ratio confidence intervals include 1 for both primary comparisons, and the reported p-values are 0.757 and 0.997. The posted primary results do not demonstrate superiority for overall survival. Secondary results and safety summaries add context, but their interpretation is limited by unreported multiplicity and analysis details. The record does not establish equivalence, and uncertainty remains around the size and direction of possible differences.