A Study to Assess the Benefit of Treatment Beyond Progression With Enzalutamide in Men Who Are Starting Treatment With Docetaxel After Worsening of Their Prostate Cancer When Taking Enzalutamide Alone: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Benefit of Treatment Beyond Progression With Enzalutamide in Men Who Are Starting Treatment With Docetaxel After Worsening of Their Prostate Cancer When Taking Enzalutamide Alone (NCT02288247), a randomized phase 3 study. The primary outcome is Progression Free Survival (PFS).

2. Clinical Question

The study addresses a treatment-sequence question rather than the initial use of enzalutamide. Participants first received open-label enzalutamide in Period 1. Those with confirmed progression who met eligibility criteria could be randomized to Period 2. The primary comparison therefore concerns the randomized period and the selected participants who entered it, not everyone enrolled at the outset.

Progression-free survival was defined from randomization until the earliest progression event or death on study. Progression could be radiographic, unequivocal clinical progression, or death. The registry definition includes bone and soft-tissue radiographic criteria, new cancer pain requiring chronic opiate analgesia, deterioration in ECOG performance status to the stated threshold, or subsequent treatment or intervention because of tumor progression complications.

This question is about the relative timing of such events under the randomized assignments. The registry result does not by itself establish what an individual participant would experience, nor does it settle questions outside the specified population, treatment sequence, endpoint, and follow-up recorded for this trial.

3. Trial Design

This was a Phase IIIb, randomized, double-blind, placebo-controlled, parallel-group study with triple masking recorded in the registry. Enrollment was 688. The study began on 2014-12-01, had primary completion on 2020-04-30, and is listed as completed. Astellas Pharma Europe Ltd. is the sponsor.

The trial had two treatment periods. During Period 1, participants received open-label enzalutamide. The registry describes 160 mg once daily, beginning on Day 1, until randomization to Period 2 or an earlier stopping circumstance such as ineligibility, intolerable toxicity, withdrawal, or death. Participants with confirmed progression who met eligibility criteria could be randomized. The primary analysis used the Full Analysis Set, defined as randomized participants who received at least one dose of investigational medicinal product.

For Period 2, the randomized groups were enzalutamide and placebo. The registry’s official title describes both groups as receiving docetaxel plus prednisolone. The posted primary endpoint counts were 136 participants in the enzalutamide group and 135 in the placebo group. Those counts belong to the primary endpoint analysis and should not be mistaken for the original enrollment total or for the number initially exposed to enzalutamide in Period 1.

Randomization supports a comparison between the assigned Period 2 groups, while blinding is intended to limit the influence of treatment knowledge on care and assessment. The precise randomization procedure, allocation concealment details, masking roles, and rules governing treatment after randomization are not reported in the registry record. The registry also does not report the original sample-size justification or the trial’s full statistical analysis plan.

The study assessed progression-free survival as its primary outcome. Secondary outcomes included PSA progression and response, objective response rate, pain-related outcomes, skeletal-related events, and patient-reported measures. The available registry record gives results for some secondary outcomes; the complete results for all listed outcomes 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: Following Screening, participants received open-label (OL) treatment with enzalutamide in period 1 followed by period 2 randomized double-blind (DB) treatment with continued enzalutamide or placebo, adding with docetaxel and prednisolone. Participants were stratified by disease progression in Period 1 (evidence of radiographic progression or not).

Period 1: OL Treatment (Max: 462 Weeks)

Reasons for not completing this period:

Period 2: DB Treatment (Max: 180 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consisted of all participants who were randomized and received at least one dose of IMP.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Safety Analysis Set 1 (SAF1) included all participants who received at least one dose of investigational medicinal product (IMP) in period 1.

6. Primary Endpoint

The registry lists the primary outcome as Progression Free Survival (PFS), measured over From date of randomization to the earliest of either documented disease progression (median duration: 35 weeks).

Progression-free survival measures the time from randomization in Period 2 to the earliest qualifying progression event or death on study. It combines disease progression and death into a time-to-event outcome. A participant’s event time is therefore determined by whichever qualifying event occurs first.

The registry defines progression through several routes. Radiographic progression includes specified new bone lesions requiring confirmation at the next assessment, or soft-tissue progression under RECIST 1.1. Unequivocal clinical progression includes new cancer pain requiring chronic opiate analgesia or deterioration in ECOG performance status to the stated threshold. Initiation of later cytotoxic chemotherapy, radiation therapy, or surgery because of tumor progression complications is also included. The registry timeframe notes a median duration of 35 weeks.

As a general statistical concept, a time-to-event endpoint uses both whether an event occurred and the time until it occurred. It can retain information from participants whose event has not been observed by the end of their available follow-up, provided the analysis handles that incomplete observation appropriately. The exact censoring rules and handling of incomplete follow-up for this trial are not reported in the registry record.

Progression-free survival is used to summarize the timing of a defined clinical event without relying only on a single end-of-study status. Its interpretation remains specific to the progression criteria, assessment schedule, analysis population, and follow-up used in the trial. It is not the same as overall survival, and the primary endpoint description does not establish an effect on outcomes that were not measured by this endpoint.

7. Results Posted in the Registry

• Enzalutamide vs Placebo: hazard ratio 0.72 (95% CI 0.53–0.96), reported p = 0.027 (as reported in the registry).

8. Secondary Efficacy Endpoints

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

Time to Prostate-specific Antigen (PSA) Progression

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Cox proportional hazards model); it was not recalculated.
• Result:
  • Enzalutamide vs Placebo: hazard ratio 0.58 (95% CI 0.41–0.82), reported p = 0.002 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Enzalutamide vs Placebo than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Objective Response Rate (ORR)

• 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:
  • Enzalutamide: 31.6% (43/136) versus 25.9% (35/135) on control; risk difference 5.7 percentage points (95% CI -5.1 to 16.4), risk ratio 1.22 (0.84–1.78); unadjusted two-proportion z-test p = 0.301.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enzalutamide and the control. The interval gives the range of effects that remain compatible with the data.

Time to First Skeletal-related Event (SRE)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Cox proportional hazards model); it was not recalculated.
• Result:
  • Enzalutamide vs Placebo: hazard ratio 1.00 (95% CI 0.47–2.13), reported p = 0.994 (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 Enzalutamide vs Placebo and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results span different kinds of outcomes: timing of progression or other events, binary response, pain-related outcomes, skeletal events, and patient-reported measures. The reported results do not form a single uniform pattern across those outcome types. Some of the available estimates are directionally compatible with the primary comparison, while other posted results are less conclusive or close to a neutral comparison. That variation is expected to matter when interpreting a set of outcomes that measure different aspects of disease and experience.

Secondary endpoints can help assess whether the primary finding is accompanied by related signals, but they do not independently confirm the primary endpoint simply because they are listed in the same trial. Their interpretation depends on endpoint definitions, analysis populations, follow-up, precision, and the methods used. In this record, the available secondary results include different statistical approaches, and detailed methods for all listed outcomes are not reported in the registry record.

Multiplicity is also relevant. When several outcomes are tested, the chance of observing at least one apparently notable result can increase unless the analyses are structured or adjusted to address that issue. The registry does not report a multiplicity adjustment or a confirmatory hierarchy for the secondary outcomes. Consequently, individual secondary p-values should be read as supportive or exploratory evidence rather than as a collection of independent definitive tests.

The registry lists nine outcome measures and posts results for only some of them. Complete numerical results and analysis details for every listed secondary outcome are not reported in the registry record. Absence of a result in the record should not be treated as evidence of no effect, and selective availability cannot be evaluated from the posted information alone. The secondary evidence can contextualize the primary analysis, but its overall weight is limited by incomplete reporting and the lack of documented multiplicity procedures.

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

• Time to Prostate-specific Antigen (PSA) Progression
• Prostate-specific Antigen (PSA) Response
• Objective Response Rate (ORR)
• Time to Pain Progression
• Time to Opiate Use for Cancer-related Pain
• Time to First Skeletal-related Event (SRE)
• Change From Baseline in Functional Assessment of Cancer Therapy - Prostate (FACT-P)
• Change From Baseline in EuroQOL 5-dimension 5-level Questionnaire [EQ-5D-5L] Visual Analog Scale (VAS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a time-to-event measure. Its event is the earliest qualifying progression or death on study, measured from randomization in Period 2. This definition matters: an endpoint’s meaning depends on which events count, when the clock starts, and how event times are recorded. The registry supplies a detailed progression definition, but the full assessment schedule and the rules for censoring participants without an observed event are not reported in the registry record.

What does the hazard ratio describe?

As a general statistical explanation, a hazard is the event rate at a particular point in follow-up among participants who have not yet had the event. A hazard ratio compares those rates between groups over time. A value below 1 indicates a lower estimated hazard in the numerator group relative to the comparator, within the fitted model. It is not a ratio of median survival times, a risk ratio at a fixed time, or a percentage of participants who benefit.

The reported primary hazard ratio is 0.72 for enzalutamide versus placebo. The registry identifies the method as a Cox proportional hazards model. In general, the Cox model estimates a group comparison while using event timing and allowing the underlying event rate to vary over follow-up without specifying a particular baseline hazard shape. Its usual interpretation as one common relative hazard across follow-up relies on a proportional-hazards assumption. Whether that assumption was evaluated, and what diagnostic results were found, are not reported in the registry record.

Why are medians also reported?

A median time-to-event value marks the estimated time at which half of the relevant event distribution has occurred, according to the analysis. It is a useful summary in the units of the endpoint, here months, but it compresses the time-to-event distribution into one value. It does not show the shape of the event pattern across follow-up or convey the uncertainty in the comparison by itself. The posted median values have 95% confidence intervals, while the model-based hazard ratio offers a separate relative comparison.

How should the confidence interval and p-value be read?

As a general explanation, a confidence interval gives a range of estimates compatible with the data and model under the method used; it is not a range that contains a known true value with certainty. The primary 95% interval runs from 0.53 to 0.96 for the hazard ratio. The p-value of 0.027 is the registry’s reported test result for the group comparison under the Cox model. A p-value is not the probability that the null hypothesis is true, and it does not measure effect size or clinical importance.

The hazard ratio, confidence interval, and p-value are related but answer different descriptive questions. The hazard ratio gives the point estimate of the relative event rate; the interval conveys its statistical precision; and the p-value summarizes how incompatible the observed result is with a specified null comparison under the model. None alone describes all uncertainty about study conduct, endpoint measurement, generalizability, or the treatment sequence.

What methods appear for other outcomes?

For the reported time-to-event secondary outcomes, the registry also gives hazard ratios from Cox proportional hazards models. PSA progression and first skeletal-related event are examples. Those outcomes have their own event definitions and follow-up context, so their results should not be treated as equivalent to the primary progression-free survival result. The registry does not report a full account of model diagnostics or all analysis details for those outcomes.

Objective response rate is a binary outcome: participants are classified according to whether they met the response definition during the specified period. The registry reports a Cochran-Mantel-Haenszel analysis for the comparison. As a general explanation, this method can compare categorical outcomes while accounting for strata, when such strata are defined. The registry record does not identify the stratification factors or provide the full response-assessment details. A binary response measure does not convey when a response occurred or how long it lasted unless those features are analyzed separately.

The registry lists additional secondary outcomes involving pain, opiate use, FACT-P, and EQ-5D-5L VAS, but complete results and detailed methods for all listed outcomes are not reported in the registry record. The record lists nine outcome measures and four analyses; that does not establish that every listed outcome has a posted result or that all analysis choices are documented.

What is not established by the posted methods?

The exact randomization procedure, stratification factors, censoring rules, missing-data methods, prespecified analysis hierarchy, multiplicity adjustment, interim-analysis plan, and protocol deviations are not reported in the registry record. The trial’s own design assumptions and sample-size justification are also not reported in the registry record. These omissions limit how fully a reader can reconstruct the planned analyses or assess whether each posted result followed a prespecified approach. They do not change the numbers the registry reports, but they are relevant to how much methodological detail can be independently assessed.

11. Confidence Intervals and Precision

The primary hazard ratio is 0.72, and its 95% confidence interval extends from 0.53 to 0.96. This interval is relatively close to the null value of 1 at its upper end, while remaining entirely below 1. It indicates statistical uncertainty around the estimated relative hazard: the point estimate is not an exact description of the underlying group comparison. The interval is compatible with a range of relative hazard values under the fitted model, rather than only the point estimate.

The reported medians are 9.53 months for enzalutamide, with a 95% confidence interval from 8.25 to 10.87, and 8.28 months for placebo, with a 95% confidence interval from 6.28 to 8.71. These are group-level summaries, not intervals for individual participants. Overlap or non-overlap of median confidence intervals is not a substitute for the model-based comparison, which uses the event-time information through the Cox analysis.

As a general statistical explanation, precision reflects how narrowly an estimate is determined by the data and analysis method. A confidence interval does not address every source of uncertainty. It does not, by itself, show whether the endpoint was assessed without bias, whether model assumptions were adequate, whether missing observations were handled appropriately, or how closely the analyzed population represents other settings. Those matters require information beyond the interval.

The primary analysis includes 136 participants in the enzalutamide group and 135 in the placebo group. The number of participants is relevant to the information available, but precision in a time-to-event analysis also depends on the observed event information and follow-up. The total number of primary endpoint events and detailed follow-up distribution are not reported in the registry record. The confidence interval therefore offers the clearest posted summary of statistical precision for the hazard ratio, but cannot resolve the absent detail about event counts and analysis assumptions.

The primary p-value of 0.027 is consistent with a confidence interval that excludes 1. It does not mean the estimate is precise in every practical sense, nor does it establish that a specific effect size is certain. The interval’s endpoints should be considered alongside the point estimate and the study’s population and endpoint definition.

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 figures are illustrations based on the observed effect, not the trial’s original design calculations. For time-to-event outcomes, the entries are total events required across the comparison, not participants per arm. For the binary outcome, entries are participants per arm. These units are different, so event totals must not be read as enrollment targets, and per-arm participant counts must not be read as totals across both groups.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. Time-to-event event totals use the Schoenfeld approach. These assumptions describe the planning illustration; the trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of events or participants that the calculation indicates would be needed for an 80% chance of detecting the specified effect at the stated significance level, if the assumptions hold. The 90% power column uses a higher target probability of detection and therefore generally requires more information. These are design-planning probabilities under assumed conditions, not guarantees about what a future study would find.

Rows that use a smaller fraction of the observed effect represent a more modest effect to detect. Smaller effects need more participants or, for time-to-event outcomes, more events to distinguish them from no difference with the same planned power and significance level. The figures are not observed power; they are planning illustrations based on the observed effect and the stated assumptions. They should not be interpreted as the number enrolled or analyzed in this trial.

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 = 0.720, so ln(HR) = -0.3285.
2. d = 4 × (1.96 + 0.842)² / [ln(0.720)]² = 290.9, rounded up to 291 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 <- 0.72                              # 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(2288247)
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 = 291 (80% power), 390 (90% power)
 75% of observed effect: events = 518 (80% power), 693 (90% power)
 50% of observed effect: events = 1,164 (80% power), 1,558 (90% power)
Simulated power with 291 events: 0.787 (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 461 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 688 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 <- 8.28          # control-arm median, months (converted from the posted unit)
hr          <- 0.72          # 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: 326         p (1-sided)   0.0001
 Events: 131        ~HR at bound   0.5228
   Month: 17    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.72   0.0338
   IA 2: 67%                   Z   2.5114
      N: 462         p (1-sided)   0.0060
 Events: 262        ~HR at bound   0.7332
   Month: 27    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.72   0.5603
       Final                   Z   1.9930
      N: 462         p (1-sided)   0.0231
 Events: 393        ~HR at bound   0.8178
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.72   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 primary comparison as a Cox proportional hazards model with a hazard ratio of 0.72, a 95% confidence interval from 0.53 to 0.96, and p = 0.027. These are the sponsor’s reported inferential results for the primary endpoint. They should be distinguished from any simple unadjusted recalculation based on summary data, because a recalculation cannot reproduce all details of a fitted model unless the underlying analysis data and procedures are available.

No discrepancy is flagged between the posted primary comparison and the reported analysis. The sponsor’s reported model is therefore the relevant analysis to interpret for this result. A model-based analysis can use event timing and other analysis choices that are not recoverable from group medians alone. The detailed implementation, including censoring rules and diagnostics, is not reported in the registry record.

For the secondary objective response rate outcome, the registry reports a Cochran-Mantel-Haenszel p-value of 0.142. A simple unadjusted comparison would not necessarily match that result because the methods may differ, including whether strata are incorporated. The registry does not report enough detail to reconstruct the sponsor’s full method or establish the factors used. The posted sponsor analysis remains the primary reference for interpreting the registry result.

Planning calculations based on an observed effect answer a different question from the sponsor’s trial analysis. They illustrate hypothetical information requirements under stated assumptions; they do not replace the reported treatment comparison or establish the original design rationale.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, subgroups, or comparisons. As a general statistical concept, testing many hypotheses can increase the chance that at least one result appears unusual even when there is no corresponding effect. A prespecified hierarchy or adjustment can control how confirmatory claims are made across multiple tests. The registry lists multiple secondary outcomes, but a multiplicity strategy, testing hierarchy, or adjustment is not reported in the registry record.

The primary endpoint is identified as progression-free survival, and the registry reports a sponsor analysis for it. The available record does not state whether secondary analyses were formally designated as confirmatory, how their order was determined, or whether any were adjusted for the number of tests. Therefore, the primary result and the secondary p-values should not be assigned equal evidential weight. The latter require caution when considered one by one.

The primary population is described as the Full Analysis Set, including participants who were randomized and received at least one dose of investigational medicinal product. The registry does not provide a complete accounting of the analysis population for every outcome, reasons for exclusion, or deviations from the randomized assignment. The posted primary endpoint arm counts are 136 and 135; the registry record does not provide enough detail to reconstruct all participant flow through each analysis.

Missing-data and censoring methods are not reported in the registry record. This is important for time-to-event analyses because participants may have incomplete event information at the end of observation, and for patient-reported outcomes because some assessments may be unavailable. The record does not describe assumptions used for missing outcomes, sensitivity analyses, or the impact of missingness.

Interim analyses, stopping rules, and the full statistical analysis plan are also not reported in the registry record. The available information is therefore insufficient to determine the complete planned testing framework or evaluate every analysis decision against a prespecified protocol. This is a limit on methodological transparency, not evidence that a particular procedure was or was not followed.

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 2% 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 (11.1%), neutropenia (8.1%), malignant neoplasm progression (4.4%), pyrexia (4.4%), neutropenic sepsis (3.7%).

The registry reports safety counts for Period 1 and for each randomized Period 2 group. In Period 1, 687 participants were at risk for serious adverse events and 238 were recorded as affected; 687 were at risk for other adverse events and 523 were affected. In Period 2, the enzalutamide group had 136 at risk for serious adverse events and 67 affected, while the placebo group had 135 at risk and 52 affected. For other adverse events, 125 of 136 in the enzalutamide group and 123 of 135 in the placebo group were recorded as affected.

Deaths are listed as 51 in Period 1, 18 in Period 2 with enzalutamide, and 15 in Period 2 with placebo. These are registry counts; the record does not give enough detail to infer from these figures alone whether deaths were caused by treatment, disease, or another circumstance. Nor do the counts alone provide a time-adjusted comparison or a causal estimate.

The most frequently listed serious adverse event terms include febrile neutropenia, neutropenia, malignant neoplasm progression, pyrexia, neutropenic sepsis, and spinal cord compression. The registry gives percentages for those terms. Adverse-event counts and percentages describe events recorded in the specified periods; they are not by themselves a complete assessment of comparative safety. The registry record does not provide detailed event definitions, exposure-adjusted rates, or a full narrative of severity and relatedness for each event.

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

The primary registry result supports a statistical difference in progression-free survival between the randomized Period 2 groups under the reported Cox proportional hazards analysis. The estimated hazard ratio is below 1, its 95% confidence interval excludes 1, and the reported p-value is 0.027. The group medians also describe the time-to-event distributions in months. Together, these statistics characterize the posted primary comparison; they do not describe the outcome of every participant.

The result does not establish that every participant assigned enzalutamide had a longer progression-free interval than a participant assigned placebo. It is a comparison between groups, with uncertainty, in a defined analysis population and treatment sequence. A hazard ratio summarizes relative event rates under a model and should not be interpreted as an absolute risk reduction or an individual prediction.

The study addresses continuation of enzalutamide after progression on enzalutamide alone, in the context of starting docetaxel and prednisolone. It does not directly answer whether enzalutamide should be started in another population, whether a different treatment sequence has the same results, or what would happen under treatments not studied in this comparison.

The primary outcome concerns progression or death, not every possible dimension of health or treatment experience. Secondary outcomes cover additional measures, but their methods and multiplicity strategy are not fully documented in the registry record. Safety counts provide a descriptive account of recorded events, not a complete causal comparison. The findings should therefore be understood as specific to the primary endpoint, randomized groups, and available follow-up information.

Statistical evidence and clinical importance are related but distinct. The confidence interval describes uncertainty in the model-based relative hazard, while judging the practical importance of the result requires context beyond a p-value. The registry record does not report all details needed to assess the trial’s full design rationale, missing-data handling, or every aspect of implementation.

19. Why This Trial Matters Statistically

Statistically, this trial is notable because it evaluates a treatment-sequence question through a randomized comparison after progression during an initial open-label period. The primary comparison is not between people starting enzalutamide and people who have never received it. It concerns participants who progressed on enzalutamide, remained eligible, and entered the randomized period while beginning chemotherapy. Defining that population is essential to interpreting the estimand—the specific treatment comparison the analysis addresses.

The primary endpoint combines radiographic and clinical progression with death, then analyzes the timing of the earliest event. This makes the result sensitive to the operational details of progression assessment. The registry supplies extensive event criteria, while other essential details, including censoring rules and diagnostics for the Cox model, are not reported in the registry record.

The hazard ratio, its confidence interval, and the p-value provide complementary information. The point estimate conveys the modeled relative comparison, the interval shows statistical precision, and the p-value summarizes evidence against the null comparison under the reported method. Reading them together is more informative than focusing on a single summary, but none removes uncertainty about conduct, measurement, or generalizability.

The secondary outcomes illustrate another statistical issue: a trial may report several measures that use different definitions and methods. Their findings can add context, but multiple testing and incomplete methodological reporting make it important not to treat every secondary result as an equally strong confirmation. The registry’s planning illustrations also distinguish event requirements for time-to-event outcomes from per-arm participant requirements for a binary outcome.

Finally, the randomized Period 2 analysis and the open-label Period 1 safety experience have different populations and purposes. Keeping those periods distinct avoids conflating initial exposure with the randomized comparison. That distinction is central to a careful reading of both efficacy and safety statistics in this study.

20. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves several trial-specific details unavailable. It does not report the original sample-size justification, the full protocol, or the complete statistical analysis plan. The planning illustrations based on the observed effect are not substitutes for those original design materials, so they cannot establish what assumptions guided the trial’s enrollment target or whether the study was planned around a particular effect size.

The primary analysis uses a Cox proportional hazards model, but the record does not describe proportional-hazards diagnostics, censoring rules, or sensitivity analyses. Without those details, readers cannot fully assess how model assumptions and incomplete follow-up were handled. The total number of primary events and a detailed follow-up distribution are also not reported in the registry record.

Although the primary analysis population is defined, the record does not provide a complete participant-flow account for every outcome, reasons for missing assessments, or methods for handling missing data. Detailed randomization and stratification procedures are not reported, and the method information for the Cochran-Mantel-Haenszel analysis does not identify the strata. The record also does not specify whether outcome definitions or analysis choices were changed during the study.

Several secondary outcomes are listed, but complete results are not posted for all of them. A multiplicity strategy and confirmatory hierarchy are not reported. This limits the strength of conclusions drawn from individual secondary findings and makes it difficult to assess how the set of results was planned to be interpreted.

The randomized comparison applies to eligible participants who progressed during Period 1 and entered Period 2. That selection is part of the study question, but it limits direct generalization to people who would not meet those criteria or who have not received enzalutamide. The registry also reports adverse-event counts without sufficient detail to make a complete treatment-attributable safety comparison.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study to Assess the Benefit of Treatment Beyond Progression With Enzalutamide in Men Who Are Starting Treatment With Docetaxel After Worsening of Their Prostate Cancer When Taking Enzalutamide Alone — NCT02288247.
• Registry record last updated 2025-04-08; status last verified 2025-04.
• Results first posted 2021-12-15.
• 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

NCT02288247 is a completed Phase IIIb randomized, double-blind, placebo-controlled, parallel-group study sponsored by Astellas Pharma Europe Ltd. Enrollment was 688. It examined continued enzalutamide versus placebo when docetaxel and prednisolone were started after progression on enzalutamide alone.

The primary endpoint was progression-free survival in the Full Analysis Set. The registry reports a median of 9.53 months for enzalutamide and 8.28 months for placebo, with a hazard ratio of 0.72, a 95% confidence interval from 0.53 to 0.96, and p = 0.027 from a Cox proportional hazards model.

Secondary outcomes included PSA progression, PSA response, objective response rate, pain-related outcomes, skeletal events, and patient-reported measures. The record posts results for some secondary outcomes but does not report complete results or full methods for every listed outcome. Details on multiplicity, missing-data handling, interim analyses, and the original design assumptions are not reported in the registry record.