A Study of Nivolumab or Placebo in Combination With Docetaxel in Men With Advanced Castration-resistant Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Nivolumab or Placebo in Combination With Docetaxel in Men With Advanced Castration-resistant Prostate Cancer (NCT04100018), a randomized phase 3 study. The primary outcome is Radiographic Progressive Free Survival (rPFS) Assessed by Blinded Independent Central Review (BICR) Per Prostate Cancer Working Group 3 (PCWG3).

2. Clinical Question

This is a comparative question about the relative timing of an event, not simply about the proportion of participants who experienced progression by a single fixed date. The event was the first qualifying radiographic progression or death, whichever occurred first. Participants without a qualifying event could be censored under the registry’s stated rules, so the analysis uses available follow-up rather than treating every participant as if observation continued for the same duration.

The comparison is between complete treatment regimens. It does not isolate the effect of nivolumab in the absence of docetaxel or prednisone, because both randomized groups received those other agents. The record describes a randomized, double-blind study, but does not report the randomization ratio or further details of allocation procedures. The result therefore addresses the randomized regimen contrast as defined in the record, and should not be generalized to a different treatment combination or population without additional evidence.

3. Trial Design

This was a phase 3, randomized, double-blind, parallel-group study sponsored by Bristol-Myers Squibb. The registry record lists the study as completed, an enrollment of 1030, a start date of 2020-02-06, and a primary completion date of 2023-06-01. The masking designation is quadruple. The record does not identify all roles included in that masking designation.

Participants were assigned to nivolumab plus docetaxel plus prednisone or placebo plus docetaxel plus prednisone. The comparison was designed to evaluate the addition of nivolumab to the docetaxel and prednisone regimen. The primary outcome analysis includes all randomized participants. The posted primary summaries list 514 participants in the nivolumab group and 516 in the placebo group. Those endpoint-specific counts should be read as the reported analysis counts, not as a replacement for the registry’s enrollment figure.

The primary outcome was radiographic progression-free survival assessed by blinded independent central review according to PCWG3. The outcome period was described as from randomization to progression or death, up to approximately 31 months. The registry lists 17 outcome measures and five analyses. Secondary outcomes include objective response, time to response, duration of response, PSA response, time to PSA progression, and adverse-event outcomes.

The record does not report the original sample-size justification, planned allocation ratio, detailed randomization procedure, interim analyses, or full statistical analysis plan. It also does not give enough information to reconstruct every analysis population for every secondary endpoint. These omissions limit the detail with which the design decisions and analysis conduct can be assessed from the registry record alone.

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.

Pre-Treatment Period

Reasons for not completing this period:

Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 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 Radiographic Progressive Free Survival (rPFS) Assessed by Blinded Independent Central Review (BICR) Per Prostate Cancer Working Group 3 (PCWG3), measured over from randomization to the first date of documented progression or death due to any cause, whichever occurs first (up to approximately 31 months).

Radiographic progression-free survival measures the time from randomization until the first documented radiographic progression or death from any cause, whichever occurs first. It combines tumor progression and death into one time-to-event outcome, so a participant can experience the endpoint through either event. The registry describes the primary population as all randomized participants.

Progression was assessed by blinded independent central review using PCWG3 criteria. For target lesions, progression required at least a 20% increase in the sum of lesion diameters relative to the smallest sum on study, including baseline if that was the smallest value, and an absolute increase of at least 5 millimeter. The appearance of one or more new lesions also counted as progression. Independent central review is intended to apply assessment criteria consistently and reduce the influence of knowledge of treatment assignment on the determination of progression.

The endpoint was summarized using medians and confidence intervals, with a reported hazard ratio for the treatment comparison. A median describes the time by which the estimated event-free proportion has reached the midpoint; it does not describe each participant’s individual course. A hazard ratio compares event rates over follow-up under the model used for the analysis, rather than subtracting the two median times.

Censoring was used for participants without a qualifying event and for specified missed-assessment situations. For participants without progression or death, censoring was at the last radiographic tumor assessment up to the start of subsequent cancer therapy. The record also describes censoring at the last radiographic assessment before certain sequences of missed assessments when progression or death followed. Censoring rules matter because they determine which observed follow-up contributes to the time-to-event analysis.

7. Results Posted in the Registry

• Nivolumab + Docetaxel + Prednisone vs Placebo + Docetaxel + Prednisone: hazard ratio 0.96 (95% CI 0.77–1.19), reported p = 0.590 (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.

Objective Response Rate (ORR) Assessed by Blinded Independent Central Review (BICR) Per Prostate Cancer Working Group (PCWG3)

• 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:
  • Nivolumab + Docetaxel + Prednisone: 27.3% (59/216) versus 23.5% (48/204) on control; risk difference 3.8 percentage points (95% CI -4.5 to 12.1), risk ratio 1.16 (0.84–1.61); unadjusted two-proportion z-test p = 0.374.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab + Docetaxel + Prednisone and the control. The interval gives the range of effects that remain compatible with the data.

Prostate-specific Antigen (PSA) Response Rate (PSA-RR)

• 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:
  • Nivolumab + Docetaxel + Prednisone: 42.4% (211/498) versus 41.6% (209/503) on control; risk difference 0.8 percentage points (95% CI -5.3 to 6.9), risk ratio 1.02 (0.88–1.18); unadjusted two-proportion z-test p = 0.793.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Nivolumab + Docetaxel + Prednisone and the control. The interval gives the range of effects that remain compatible with the data.

Time to PSA Progression (TTP-PSA)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor; it was not recalculated.
• Result:
  • Nivolumab + Docetaxel + Prednisone vs Placebo + Docetaxel + Prednisone: hazard ratio 1.00 (95% CI 0.86–1.16) (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 Nivolumab + Docetaxel + Prednisone vs Placebo + Docetaxel + Prednisone and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover response, PSA activity, time to PSA progression, and safety. They describe additional facets of the randomized comparison, but do not measure the same construct as radiographic progression-free survival. A response outcome addresses whether a specified response was recorded; a time-to-progression outcome addresses when an event occurred while accounting for censoring. Their results can be informative without serving as substitutes for the primary endpoint.

Across the posted efficacy summaries, response estimates are numerically higher for the nivolumab regimen, but their confidence intervals remain compatible with no difference and with effects in either direction. The PSA-response summary likewise does not establish a clear separation. The time-to-PSA-progression estimate is centered at a hazard ratio of 1.00, with an interval spanning 0.86 to 1.16. Considered together, these results do not provide a consistent basis for a strong claim of benefit on the secondary efficacy outcomes.

The primary outcome remains the central confirmatory result because it was designated as primary in the registry record. Secondary results are generally less conclusive when many endpoints are examined, particularly if the registry record does not state how multiplicity was controlled. Testing or estimating several outcomes can increase the chance that at least one appears notable by chance. The record does not report a multiplicity adjustment plan, so isolated secondary findings should not be treated as if they had the same evidential status as a prespecified primary analysis with a documented testing strategy.

The registry lists 17 outcome measures, while 15 secondary outcomes are posted in the secondary summaries. The record does not report the complete analysis plan needed to determine which comparisons were confirmatory, how outcome-specific missingness was handled, or whether any testing hierarchy was used. The secondary evidence is best read as descriptive and supportive, with attention to the estimates and their uncertainty rather than to any single result in isolation.

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

• Objective Response Rate (ORR) Assessed by Blinded Independent Central Review (BICR) Per Prostate Cancer Working Group (PCWG3)
• Time to Response (TTR) Assessed by Blinded Independent Central Review (BICR) Per Prostate Cancer Working Group (PCWG3)
• Duration of Response Assessed by Blinded Independent Central Review (BICR) Per Prostate Cancer Working Group (PCWG3)
• Prostate-specific Antigen (PSA) Response Rate (PSA-RR)
• Time to PSA Progression (TTP-PSA)
• Number of Participants With Adverse Events
• Number of Participants With Serious Adverse Events
• Number of Participants With Adverse Events Leading to Discontinuation

9. Statistical Interpretation

10. Statistical Methods Explained

What does a hazard ratio summarize?

A hazard ratio is a relative comparison of event rates over the observed follow-up, as estimated by the analysis. A value near the no-difference reference is consistent with similar event rates under the model; values on either side indicate the direction of the estimated contrast as defined by the comparison. It is not a ratio of median survival times and does not directly state how many additional months an individual participant might experience without progression.

The registry reports a Cox proportional hazards analysis for the primary outcome, alongside a log-rank method. In general, the Cox model estimates a hazard ratio while accounting for the timing of events and censoring. Its usual interpretation relies on the proportional-hazards assumption: the relative event rate is treated as sufficiently stable over follow-up for a single hazard ratio to summarize the contrast. Whether that assumption was assessed, and what diagnostics were used, are not reported in the registry record.

The log-rank test compares the event-time patterns between groups while accounting for censoring. It provides a test of whether the observed curves are consistent with the same underlying event experience, but does not by itself describe the size or precision of a treatment contrast. The hazard ratio and its interval provide an estimate and uncertainty range; the log-rank p-value addresses a related but distinct inferential question.

How should the median and confidence interval be read?

The median time-to-event is the point at which the estimated event-free experience reaches its midpoint. It is a compact summary, but it does not use the entire shape of the event-time distribution in the same way as a model-based hazard ratio. Median estimates can also be affected by how much follow-up is available and by censoring. The 95% confidence intervals accompanying the arm-specific medians express statistical uncertainty about those estimates; overlap between separate arm intervals is not a substitute for the direct treatment comparison.

A confidence interval describes a range of parameter values compatible with the data and analysis, subject to the method’s assumptions. It is not a range containing a specified proportion of individual participants’ outcomes, and it does not assign a probability that the true effect lies within that one calculated interval. A wide interval indicates less precision than a narrow interval, while the interval’s position relative to the no-difference reference helps interpret the evidence for a contrast.

What do the secondary-outcome comparisons add?

Objective response rate and PSA response rate are binary outcomes: each participant is classified according to whether the defined response occurred. Their reported arm percentages are accompanied by confidence intervals. A risk difference compares the response proportions by subtracting one group’s proportion from the other; the sponsor’s adjusted analysis may use a different method and adjustment set. The registry’s objective-response analysis reports an adjusted difference and confidence interval, while the PSA-response analysis reports a percentage difference and confidence interval.

Time to PSA progression is analyzed as a time-to-event outcome. Its reported hazard ratio is 1.00, with a confidence interval from 0.86 to 1.16. As with the primary outcome, interpretation must account for censoring and depends on the analysis assumptions. The record does not report all methodological details for these secondary comparisons, including a complete statistical plan for each endpoint.

These endpoint types answer different questions. A response proportion summarizes whether a defined event occurred within the outcome’s assessment framework, whereas time-to-event outcomes use the timing of events and censoring. A result on one endpoint does not automatically imply the same result on another. Differences in analysis populations, definitions, assessment timing, and follow-up can also make the estimates non-interchangeable.

Why do censoring and assessment rules matter?

In time-to-event analysis, censoring records that the event was not observed by a specified point while retaining the participant’s observed follow-up up to that point. It is not the same as observing that the event never happens. The registry specifies censoring at the last radiographic assessment before subsequent cancer therapy for participants without progression or death, and describes additional rules for missed assessments followed by progression or death. Such rules can affect which follow-up time contributes to the analysis.

General statistical interpretation assumes that censoring is handled appropriately for the analysis. If the reasons for follow-up ending are related to a participant’s unobserved event risk, censoring can complicate interpretation. The registry record does not report analyses of the sensitivity of the result to alternative censoring rules or missing-data assumptions. It therefore supports interpretation of the stated analysis, not a claim that all possible follow-up mechanisms have been resolved.

How should the reported test and estimate be considered together?

The effect estimate conveys direction and magnitude on the hazard-ratio scale, while the confidence interval conveys precision. A p-value summarizes how unusual the data would be under a specified null hypothesis and model; it does not measure the probability that the null hypothesis is true or the probability that a treatment is effective. A non-small p-value is not evidence of equivalence. An equivalence or non-inferiority conclusion would require a prespecified margin and a design and analysis suited to that question, which are not reported in the registry record.

For the primary comparison, the confidence interval spans the no-difference reference and the reported p-value is not conventionally small. These features are consistent with uncertainty about the direction and size of the relative effect. Statistical significance alone would not establish clinical importance, and the absence of a statistically persuasive difference does not prove that the regimens have identical effects. The record does not report a clinical threshold for a meaningful difference in radiographic progression-free survival.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimated effect. The primary hazard ratio is 0.96, and its reported confidence interval extends from 0.77 to 1.19. This interval includes the no-difference reference and allows for estimates favoring either regimen. The result is therefore not precise enough to establish a direction of effect from the interval alone. The reported p-value is also not conventionally small, which is consistent with the interval-based interpretation.

The arm-specific median estimates are 9.43 months for nivolumab plus docetaxel and prednisone and 8.74 months for placebo plus docetaxel and prednisone. Their respective 95% confidence intervals are 8.48 to 10.32 months and 8.38 to 9.99 months. The intervals communicate uncertainty in each median, but the primary comparative inference is based on the reported hazard ratio and its interval, not on visual comparison of the two median intervals.

For objective response, the sponsor-reported adjusted difference is 3.8, with a 95% confidence interval from -4.5 to 12.1. For PSA response, the sponsor-reported percentage difference is 0.9, with a 95% confidence interval from -5.2 to 7.0. Both intervals include values consistent with no difference and allow for effects in either direction. The time-to-PSA-progression hazard ratio is 1.00, with a confidence interval from 0.86 to 1.16. These estimates are also uncertain and should be interpreted in the context of their secondary status.

Confidence intervals are not guarantees that the true effect lies inside the displayed limits. They summarize uncertainty under the statistical method and assumptions used. The registry does not report all diagnostics or sensitivity analyses needed to assess those assumptions in detail. Precision is therefore best understood as the uncertainty represented by the posted intervals, not as certainty about the treatment contrast.

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 primary time-to-event planning illustration is expressed as total events, not participants per arm. Under the row for planning around 100% of the observed effect, the illustration lists 18,840 total events for 80% power and 25,222 total events for 90% power. Planning for 75% of the observed effect lists 33,494 total events for 80% power and 44,838 for 90% power. Planning for 50% of the observed effect lists 75,360 total events for 80% power and 100,886 for 90% power.

In plain terms, the 80% power column gives the illustrated event count for a design that would have an 80% chance of detecting the assumed effect under the stated assumptions, if that effect were real and the model assumptions held. The 90% power column describes the corresponding illustration for a higher probability of detection. These are planning calculations, not a claim about what the completed trial had power to detect after its results were known. They are not observed power.

The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation, with the effect set to the stated fraction of the observed effect. For time-to-event outcomes, the calculation uses the Schoenfeld method and counts total events. Other planning illustrations in the secondary-outcome summaries are stated as participants per arm, not total events.

Smaller assumed effects require more information to detect, which is why the event-count illustrations increase as the assumed effect is reduced from the full observed effect to 75% and then 50%. The registry record does not report the trial’s original design assumptions or original sample-size justification. These calculations are therefore planning illustrations based on the observed effect, rather than a reconstruction of the trial’s design or a description of its observed statistical power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.960, so ln(HR) = -0.0408.
2. d = 4 × (1.96 + 0.842)² / [ln(0.960)]² = 18,839.9, rounded up to 18,840 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 <- 0.96                              # 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(4100018)
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 = 18,840 (80% power), 25,222 (90% power)
 75% of observed effect: events = 33,494 (80% power), 44,838 (90% power)
 50% of observed effect: events = 75,360 (80% power), 100,886 (90% power)
Simulated power with 18,840 events: 0.797 (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 29,324 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 1,030 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 <- 8.74          # control-arm median, months (converted from the posted unit)
hr          <- 0.96          # 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: 20284         p (1-sided)   0.0001
  Events: 8506        ~HR at bound   0.9227
     Month: 17    P(Cross) if HR=1   0.0001
               P(Cross) if HR=0.96   0.0338
     IA 2: 67%                   Z   2.5114
      N: 29324         p (1-sided)   0.0060
 Events: 17012        ~HR at bound   0.9622
     Month: 26    P(Cross) if HR=1   0.0060
               P(Cross) if HR=0.96   0.5603
         Final                   Z   1.9930
      N: 29324         p (1-sided)   0.0231
 Events: 25518        ~HR at bound   0.9754
     Month: 60    P(Cross) if HR=1   0.0250
               P(Cross) if HR=0.96   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 primary comparison is reported as a Cox proportional-hazards estimate of 0.96, with a confidence interval from 0.77 to 1.19 and a reported log-rank p-value that is not conventionally small. The analysis information identifies a 99% confidence interval for the reported primary Cox analysis. The posted arm medians, by contrast, are accompanied by 95% confidence intervals. These are different summaries and should not be conflated.

For objective response, the sponsor’s posted analysis gives an adjusted difference of 3.8, with a 95% confidence interval from -4.5 to 12.1. For PSA response, the sponsor reports a percentage difference of 0.9, with a 95% confidence interval from -5.2 to 7.0. The recalculated comparisons are simple, unadjusted calculations from posted summary statistics, so they need not match adjusted sponsor estimates exactly. They also may not use the same modeling or adjustment procedures.

No discrepancy is flagged for the record. The sponsor’s reported analysis remains the relevant trial analysis; recalculated summaries are supplementary checks based on the information posted in the registry, not replacements for the sponsor’s method. In particular, differences in adjustment, analysis populations, or rounding can yield slightly different estimates. The registry does not provide enough detail to reproduce every aspect of the sponsor’s analyses independently.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, comparisons, time points, or subgroups. Even when each analysis uses a conventional statistical threshold, conducting many analyses can raise the chance of at least one apparently positive result arising by chance. Common approaches to address this include prespecified testing sequences or adjustments to the inferential thresholds. Whether such approaches were planned or used is not reported in the registry record.

The registry identifies radiographic progression-free survival as the primary outcome and lists multiple secondary outcomes, including objective response, time to response, duration of response, PSA response, time to PSA progression, and adverse-event measures. It also records 17 outcome measures and five analyses. The number of outcomes alone does not establish that a multiplicity problem occurred, but it makes the analysis plan important for interpreting secondary p-values and confidence intervals. A complete hierarchy, family of tests, or adjustment procedure is not reported in the registry record.

The primary endpoint description specifies censoring rules for participants without progression or death and for certain cases involving missed radiographic assessments. Those rules help define the time-to-event analysis, but they do not fully describe how missing observations were handled across all outcomes. The registry record does not report detailed missing-data assumptions, sensitivity analyses, or a full account of follow-up completeness by group. It is therefore not possible from the record alone to assess the robustness of every endpoint to alternative missing-data approaches.

The primary population is stated as all randomized participants. The record does not provide a fuller account of every analysis set used for each secondary outcome, nor does it specify all exclusions or endpoint-specific denominators beyond the posted summaries. The original sample-size justification, interim analysis plan, and complete statistical analysis plan are also not reported in the registry record. These omissions should be treated as limits on the available audit trail, rather than as evidence that a particular method was or was not used.

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: malignant neoplasm progression (5.3%), pneumonia (3.5%), febrile neutropenia (3.3%), covid-19 (2.5%), prostate cancer (2.5%).

The serious adverse-event summaries report 256 affected participants among 510 at risk in the nivolumab group and 242 among 510 at risk in the placebo group. These are participant counts for the reported serious adverse-event outcome. They should be interpreted with the registry’s definitions and observation periods in mind; the record does not provide enough detail in these summaries to determine the timing, duration, or severity distribution of every event.

The most frequently listed serious terms include malignant neoplasm progression at 5.3%, pneumonia at 3.5%, febrile neutropenia at 3.3%, COVID-19 at 2.5%, prostate cancer at 2.5%, and haematuria at 2.5%. Serious-event terms may overlap because a participant can experience more than one event, so the listed percentages should not be added to create a total. The registry also reports other adverse events and deaths by group, but those measures are distinct from the serious adverse-event count.

These summaries describe events recorded during the study; they do not by themselves determine whether a treatment caused an event. Attribution, exposure duration, event timing, and differences in follow-up can matter. The registry lists adverse events leading to discontinuation as an outcome, but the detailed results for that measure are not reported in the registry record.

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

The primary result is an estimate of the relative timing of radiographic progression or death under two randomized regimens. The reported hazard ratio of 0.96 is close to the no-difference reference, while its confidence interval from 0.77 to 1.19 includes that reference and spans possible effects in both directions. The posted evidence therefore does not establish a clear difference in radiographic progression-free survival between nivolumab plus docetaxel and prednisone and placebo plus docetaxel and prednisone.

This is not proof that the regimens are equivalent or that their effects are identical. A result without clear statistical evidence of a difference can reflect a small true difference, no difference, or uncertainty that leaves more than one possibility compatible with the data. The registry record does not report a prespecified equivalence or non-inferiority margin, so the comparison should not be interpreted as an equivalence assessment.

The result also does not answer every treatment question. It compares the two specified combinations in the study population and does not isolate nivolumab from the accompanying docetaxel and prednisone regimen. It does not establish effects in other populations, treatment settings, or combinations. The primary outcome concerns radiographic progression or death under the stated assessment and censoring rules; it is not a direct measure of every aspect of disease burden, quality of life, or individual experience. Those other outcomes should be interpreted only where the registry reports relevant results.

Secondary efficacy summaries do not provide a clear, independent confirmation of a difference. They are subject to uncertainty and multiplicity considerations, and the record does not report a full testing plan. Safety counts document events in both groups but do not alone establish treatment causation or compare risk without attention to definitions and follow-up. Overall, the registry results support a cautious account of the observed statistical evidence, not a treatment recommendation or a conclusion that no individual can benefit or experience harm.

19. Why This Trial Matters Statistically

This trial is statistically informative because it uses random allocation and a blinded assessment of the primary radiographic endpoint. Randomization is intended to make the groups comparable in expectation, while independent central review can reduce the influence of treatment knowledge on progression assessment. The parallel-group comparison also directly addresses the addition of nivolumab to a regimen used in both groups.

The result illustrates why the point estimate, interval, and test should be read together. The hazard ratio is close to the no-difference reference, but the interval extends to effects on either side of that reference. A single point estimate cannot express this uncertainty, and a non-small p-value does not demonstrate equivalence. The median summaries add a useful description of event timing but do not replace the comparative time-to-event analysis.

The record also highlights how endpoint definitions and censoring rules shape interpretation. Progression depends on specified radiographic criteria and central assessment; the time-to-event analysis uses censoring when a qualifying event is not observed under the stated follow-up rules. These features are central to the meaning of the estimate, not merely technical details.

Finally, the registry’s multiple outcome measures make transparent reporting of analysis plans important. Without a reported multiplicity strategy, the secondary results carry less confirmatory weight than the primary result. The record also leaves the original sample-size justification and detailed statistical plan unreported. These limitations demonstrate why registry summaries are useful for reviewing the stated findings while remaining distinct from a complete account of the trial’s design and analysis.

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 design assumptions used when the trial was planned. The posted planning illustrations are based on the observed effect and cannot establish what effect the original design was intended to detect. The detailed statistical analysis plan, interim analyses, and any stopping rules are also not reported in the registry record.

The record gives the primary endpoint definition and censoring rules, but does not report whether proportional-hazards assumptions were assessed or provide diagnostic results. It does not give sensitivity analyses for alternative censoring or missing-data assumptions. This limits independent evaluation of how robust the primary hazard-ratio estimate is to those choices.

The registry lists multiple outcome measures, but does not report a multiplicity-control strategy or a complete hierarchy for the secondary analyses. It also does not provide the full analysis populations and all outcome-specific handling details for every secondary endpoint. Consequently, the secondary results are harder to classify as confirmatory versus exploratory from the registry record alone.

Some endpoint summaries use fewer participants than the primary analysis population, such as the objective-response assessment. The record provides the posted counts but does not fully explain the reason for each endpoint-specific denominator. The safety summaries are counts and selected event terms, without enough detail to assess exposure-adjusted rates, timing, participant-level overlap, or attribution. These are limitations of interpretation from the registry summaries and do not imply that the trial did not collect or analyze additional information.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Nivolumab or Placebo in Combination With Docetaxel in Men With Advanced Castration-resistant Prostate Cancer — NCT04100018.
• Registry record last updated 2025-06-12; status last verified 2025-05.
• Results first posted 2024-07-22.
• 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

NCT04100018 is a completed phase 3, randomized, double-blind, parallel-group study of nivolumab or placebo with docetaxel and prednisone in men with metastatic castration-resistant prostate cancer. The registry lists enrollment of 1030 and identifies radiographic progression-free survival assessed by blinded independent central review under PCWG3 as the primary outcome.

The primary comparison reports a hazard ratio of 0.96, with a confidence interval from 0.77 to 1.19. The interval includes the no-difference reference, and the reported test is not conventionally small. The result does not establish a clear difference between the regimens, but it also does not prove equivalence.

Secondary efficacy summaries are uncertain, and the record does not report a multiplicity strategy or the complete statistical analysis plan. Serious adverse events were reported in both groups. The registry provides useful endpoint definitions and selected results, while leaving several design and analysis details not reported in the registry record.