An Asian Study to Evaluate Efficacy and Safety of Oral Enzalutamide in Progressive Metastatic Prostate Cancer Participants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Asian Study to Evaluate Efficacy and Safety of Oral Enzalutamide in Progressive Metastatic Prostate Cancer Participants (NCT02294461), a randomized phase 3 study. The primary outcome is Time to Prostate-specific Antigen (PSA) Progression.

2. Clinical Question

The clinical question is framed around a biomarker-defined event. PSA progression was determined using the Prostate Cancer Clinical Trials Working Group 2 consensus guidelines, with the progression rule depending on whether PSA had declined at Week 13. The study also collected outcomes concerning overall survival, radiographic progression-free survival, skeletal-related events, chemotherapy initiation, PSA response, soft tissue response, and pharmacokinetics. Those outcomes broaden the questions addressed by the trial, but they do not change the identity of its primary endpoint.

3. Trial Design

This was a phase 3, randomized, parallel-group study with quadruple masking recorded in the registry. Its official title describes an Asian multinational study and identifies it as double-blind and placebo-controlled. The registry lists an enrollment of 395. The reported primary analysis includes 198 participants in the enzalutamide group and 190 in the placebo group; these are the endpoint-specific analysis counts, and they should not be treated as a reconciliation of the overall enrollment figure.

The study began on 2014-04-23, had a primary completion date of 2015-09-20, and is listed as completed. The primary objective was to assess enzalutamide versus placebo for time to PSA progression in chemotherapy-naïve participants with progressive metastatic prostate cancer after failure of androgen deprivation therapy.

During the double-blind period, participants assigned to enzalutamide received 160 mg orally once a day. Participants assigned to placebo received matching placebo orally once a day. The registry describes treatment as continuing until specified disease-progression and treatment events, but the arm descriptions are not fully detailed in the record excerpt. Eligible participants assigned to placebo could consent to an open-label period in which they received enzalutamide. The safety results list this crossover group separately from the randomized treatment groups.

Randomization and masking can reduce systematic differences in treatment assignment and assessment, as a general design principle. The registry record does not report the randomization ratio, the method used to generate or conceal the allocation sequence, or which roles were included in the quadruple-masking designation. It also does not report the original sample-size justification or detailed trial conduct procedures. These details should not be inferred from the phase, masking label, or observed enrollment.

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: Participants who met inclusion criteria and none of the exclusion criteria were enrolled in the study.

Double-blind Period (up to 29.4 Months)

Reasons for not completing this period:

Open-label Period (up to 54.3 Months)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population with available data.

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: Intent-to-treat (ITT) population consisted of all randomized participants in the study.

6. Primary Endpoint

The registry lists the primary outcome as Time to Prostate-specific Antigen (PSA) Progression, measured over From the date of randomization to PSA progression median follow-up time is 6.47 months for enzalutamide and 2.99 months for placebo.

The primary endpoint was time to prostate-specific antigen (PSA) progression, measured in months from randomization to the defined PSA-progression date. PSA is a biomarker used in monitoring prostate cancer. A time-to-event endpoint captures how long participants remain without the specified event, while allowing participants without a confirmed event to contribute follow-up until censoring.

The registry defines PSA progression according to the Prostate Cancer Clinical Trials Working Group 2 consensus guidelines. For participants with a PSA decline at Week 13, progression required an increase of at least 25% and an absolute increase of at least 2 ng/mL above the nadir, confirmed by a second consecutive value obtained 3 or more weeks later. For participants without a PSA decline at Week 13, the same percentage and absolute-increase thresholds were applied relative to baseline, with confirmation by a second consecutive value 3 or more weeks later.

The endpoint was estimated with the Kaplan-Meier method, and participants without confirmed PSA progression were censored. This approach is used generally for time-to-event data because it can incorporate differing follow-up times and censoring rather than requiring every participant to experience the event. The registry reports median time to PSA progression of 8.31 months for enzalutamide and 2.86 months for placebo. Median follow-up time is reported as 6.47 months for enzalutamide and 2.99 months for placebo. PSA progression is not the same endpoint as death or radiographic progression, so the primary result answers a specific disease-marker question rather than every question about disease course.

7. Results Posted in the Registry

• Enzalutamide vs Placebo: hazard ratio 0.38 (95% CI 0.27–0.52), reported p < 0.001 (as reported in the registry).

8. Secondary Efficacy Endpoints

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

Duration of Overall Survival

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Unstratified log-rank test); it was not recalculated.
• Result:
  • Enzalutamide vs Placebo: hazard ratio 0.70 (95% CI 0.51–0.95), reported p = 0.021 (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.

Duration of Radiographic Progression-free Survival (rPFS) Based on Independent Central Review Facility Assessment

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Unstratified log-rank test); it was not recalculated.
• Result:
  • Enzalutamide vs Placebo: hazard ratio 0.31 (95% CI 0.20–0.46), reported p < 0.001 (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.

Time to First Skeletal-Related Event

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Unstratified log-rank test); it was not recalculated.
• Result:
  • Enzalutamide vs Placebo: hazard ratio 0.56 (95% CI 0.21–1.52), reported p = 0.250 (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 extend the assessment beyond PSA progression to overall survival, radiographic progression-free survival, skeletal-related events, and other outcomes. Among the posted time-to-event comparisons, the hazard-ratio estimates for overall survival and rPFS are below 1, in the same direction as the primary hazard-ratio estimate. The skeletal-related-event estimate is also below 1, but its confidence interval includes 1 and its reported p-value is 0.250. This pattern is compatible with more support for some secondary comparisons than others; it does not make every secondary outcome conclusive.

These outcomes are related to the primary question but are not interchangeable. PSA progression is a biomarker-defined event, rPFS combines radiographic progression and death, overall survival concerns death from any cause, and a skeletal-related event is a different clinical event. A consistent direction across estimates can add context, but it does not prove that the outcomes share the same effect or that the primary endpoint captures all clinically relevant consequences.

The registry lists additional secondary outcomes, including PSA response, soft tissue response, and pharmacokinetic measures. Their presence indicates a wider set of questions, but the posted information summarized for the time-to-event results should not be taken as a complete interpretation of every secondary measure. The registry reports 15 secondary outcomes, while the record's number of analyses is 7; the relationship between outcome listings and analyses should not be assumed to be one-to-one.

When multiple outcomes are tested, the chance of at least one apparently notable result can increase. This is a general statistical concern. The registry record does not report whether a multiplicity-control procedure was specified or used for the secondary outcomes. Consequently, unadjusted secondary p-values carry less confirmatory weight than a prespecified primary analysis with a stated testing framework. They are useful for describing the posted evidence and motivating further study, but should be interpreted cautiously rather than as independent proof across all outcomes.

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

• Duration of Overall Survival
• Duration of Radiographic Progression-free Survival (rPFS) Based on Independent Central Review Facility Assessment
• Time to First Skeletal-Related Event
• Time to Initiation of Cytotoxic Chemotherapy
• Number of Participants With Confirmed Best PSA Response (≥50% Decrease From Baseline)
• Best Overall Soft Tissue Response
• Time to Maximum Concentration (Tmax) of Enzalutamide, M1,M2 and Enzalutamide Plus M2
• Maximum Observed Plasma Concentration During the First 24 Hours After Dosing (Cmax) Enzalutamide, M1,M2 and Enzalutamide Plus M2

9. Statistical Interpretation

10. Statistical Methods Explained

Time-to-event methods are used when the outcome is the time until an event, such as PSA progression or death. Participants may have different lengths of observation, and some may not experience the event before their follow-up ends. Such participants are generally censored at their last relevant observation. Censoring preserves information about the time they were followed, but interpretation depends on assumptions about the relationship between censoring and the event process. The registry states that participants without confirmed PSA progression were censored; further details about censoring patterns and sensitivity analyses are not reported in the registry record.

What does the Kaplan-Meier median represent?

The Kaplan-Meier method estimates the probability of remaining free of the event over time while incorporating censored observations. The median event time is the time at which the estimated event-free probability reaches 50%, if that point can be estimated. It is not the arithmetic average of observed times. A median can be unavailable when the estimated curve does not reach that threshold during available follow-up. In the posted radiographic progression-free survival results, the enzalutamide median is not reported as a numeric value; the registry gives a lower confidence limit of 10.97 months and no upper limit. The other numerical median and interval details should be read as reported, without trying to fill missing values.

How should a hazard ratio be read?

A hazard is the instantaneous event rate among participants who have not yet experienced the event. A hazard ratio compares that rate between groups over time. A value below 1 means the estimated hazard is lower in the first-named group than in the comparator, under the model's assumptions. The hazard ratio is not a risk ratio, an absolute risk difference, or a comparison of medians. In general, the proportional-hazards model treats the hazard ratio as constant over time. If the relative event rates change over time, a single hazard ratio may not fully describe the pattern. The registry record does not report an assessment of the proportional-hazards assumption.

For the primary endpoint, the sponsor's reported analysis is an unstratified Cox proportional-hazards analysis. The Cox model estimates the relative hazard while allowing the baseline hazard to vary over time. “Unstratified” indicates that the reported analysis is not divided into strata in the model as described in the record. The registry does not report covariate adjustment details beyond that method label. The primary comparison reports a hazard ratio of 0.38, a 95% confidence interval from 0.27 to 0.52, and p < 0.001.

The Kaplan-Meier method and a Cox model serve different purposes. Kaplan-Meier estimates the event-free curve and supports a median estimate; the Cox analysis supplies a relative hazard estimate. The numerical median comparison and hazard ratio therefore should not be substituted for one another. They complement one another by describing different features of the time-to-event data.

What do confidence intervals and p-values contribute?

A confidence interval conveys uncertainty around an estimate. In repeated use of the same statistical procedure under its assumptions, intervals at a stated confidence level are designed to cover the underlying parameter at that level. It is not a range containing a known proportion of individual outcomes, and it does not guarantee that the true value lies inside a particular reported interval. The 95% interval for the primary hazard ratio extends from 0.27 to 0.52.

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary p-value is reported as p < 0.001. That threshold should be quoted as reported; it should not be converted into a more precise value.

The sponsor also reports unstratified log-rank analyses for the listed secondary time-to-event outcomes. The log-rank test compares event-time distributions between groups and is commonly used for time-to-event comparisons. Its associated hazard ratio is a separate effect estimate reported alongside the test result. The registry record does not describe a multiplicity strategy for these secondary comparisons, so the nominal p-values should not be interpreted as if they were adjusted for testing multiple outcomes.

For rPFS, the event is defined as death from any cause or radiographic disease progression, with assessment based on an independent central review facility. This differs from the primary PSA-progression event. The registry reports an enzalutamide hazard ratio of 0.31 with a 95% confidence interval from 0.20 to 0.46 and p < 0.001. For overall survival, the reported hazard ratio is 0.70 with a 95% confidence interval from 0.51 to 0.95 and p = 0.021. For time to first skeletal-related event, the reported hazard ratio is 0.56 with a 95% confidence interval from 0.21 to 1.52 and p = 0.250. These are sponsor-reported analyses, and their endpoint-specific definitions and follow-up apply.

General statistical interpretation also depends on the amount and pattern of follow-up, event counts, outcome ascertainment, and analysis assumptions. The registry reports median follow-up times for the named time-to-event outcomes, but does not report detailed censoring distributions, diagnostic checks, or sensitivity analyses in the summarized record. These omissions limit what can be independently assessed about model fit and robustness. A statistically significant result is not a substitute for those checks, and the absence of reported detail should not be read as evidence that a particular procedure was or was not performed.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.38, and its 95% confidence interval ranges from 0.27 to 0.52. The interval lies below 1, the value representing equal hazards in the two groups under this measure. Its width conveys that the estimate is not exact: values across a range below 1 remain compatible with the data and the model. The p-value is reported as p < 0.001, but that does not remove uncertainty about the magnitude of the relative hazard.

The median time estimates have their own 95% confidence intervals. Enzalutamide has a median of 8.31 months with an interval from 5.72 to 10.25 months; placebo has a median of 2.86 months with an interval from 2.83 to 4.63 months. These intervals describe uncertainty in each group's median, while the hazard-ratio interval describes uncertainty in a relative event-rate measure. The intervals should not be used as a substitute for a formal comparison between groups.

Precision is influenced generally by the number and timing of observed events, the amount of follow-up, and censoring. The primary endpoint's reported analysis counts are 198 for enzalutamide and 190 for placebo, but the registry record does not provide enough detail to infer precision from those counts alone. Median follow-up is reported as 6.47 months and 2.99 months, respectively. A shorter follow-up distribution or fewer events can leave less information about later portions of an event-time curve.

Confidence intervals are not guarantees and do not represent the range of outcomes expected for individual participants. They also do not account for every possible source of uncertainty, such as unreported analysis choices or model violations. The registry record does not report a proportional-hazards diagnostic, and the interpretation of a single hazard ratio relies on the model's suitability for the data. The interval is best read alongside the endpoint definition, analysis method, censoring information, and limitations in what the record reports.

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 a reconstruction of the trial's original design. For these time-to-event endpoints, the entries are total events required, not participants per arm. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario asks what event target would correspond to detecting a stated fraction of the observed effect. The planning rows describe 100%, 75%, and 50% of the observed effect.

The 80% power column describes a planning target under which a study would have an 80% chance of detecting the specified effect, if the assumptions hold and the effect is present. The 90% power column uses a higher chance of detection and therefore generally requires more information. For time-to-event planning, that information is expressed as total events. These are conditional design calculations, not predictions that a future study will achieve its target or reproduce the observed effect.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more events and, typically, more participants or longer observation. The figures should be read as sensitivity to the assumed effect size, not as evidence that the current study had a particular probability of detecting its observed result. This is not observed power.

The registry record does not report the trial's original sample-size justification or original planning assumptions. The posted illustrations use the observed effect and the assumptions stated above; they should not be attributed to the sponsor's original protocol. Because the figures are event targets, they are not directly interchangeable with a target number of participants per arm. The number of participants needed to accumulate a given number of events would depend on follow-up and event occurrence, among other design features.

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 = 0.380, so ln(HR) = -0.9676.
2. d = 4 × (1.96 + 0.842)² / [ln(0.380)]² = 33.5, rounded up to 34 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 <- 0.38                              # 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(2294461)
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 = 34 (80% power), 45 (90% power)
 75% of observed effect: events = 60 (80% power), 80 (90% power)
 50% of observed effect: events = 135 (80% power), 180 (90% power)
Simulated power with 34 events: 0.800 (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 49 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 395 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 <- 2.86          # control-arm median, months (converted from the posted unit)
hr          <- 0.38          # 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: 28         p (1-sided)   0.0001
 Events: 15        ~HR at bound   0.1471
  Month: 13    P(Cross) if HR=1   0.0001
            P(Cross) if HR=0.38   0.0338
  IA 2: 67%                   Z   2.5114
      N: 46         p (1-sided)   0.0060
 Events: 30        ~HR at bound   0.3996
  Month: 22    P(Cross) if HR=1   0.0060
            P(Cross) if HR=0.38   0.5603
      Final                   Z   1.9930
      N: 50         p (1-sided)   0.0231
 Events: 45        ~HR at bound   0.5519
  Month: 60    P(Cross) if HR=1   0.0250
            P(Cross) if HR=0.38   0.9000



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

15. Analyses Reported by the Sponsor

The sponsor's primary analysis is reported as an unstratified Cox proportional-hazards analysis. It gives a hazard ratio of 0.38, a 95% confidence interval from 0.27 to 0.52, and p < 0.001. These are the registry's reported primary comparison results. The registry record does not flag a discrepancy between the reported analysis and the comparison displayed for the primary endpoint.

The recalculated planning illustrations are not a replacement for the sponsor's trial analysis. They use the observed effect with stated planning assumptions to show event requirements across hypothetical effect sizes and power targets. They do not estimate a new treatment effect, change the trial's reported p-value, or supply missing details about the original design. The sponsor's analysis is the appropriate reference for the reported trial result.

For the secondary time-to-event outcomes, the registry identifies unstratified log-rank analyses and reports hazard ratios, confidence intervals, and p-values. These sponsor-reported analyses should also be distinguished from planning calculations. The latter are design illustrations, while the former are inferential results from the trial. The record does not report further analysis-plan details that would clarify prespecified covariates, testing order, or adjustment for multiple comparisons.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies time to PSA progression as the primary endpoint and lists multiple secondary outcomes, including survival, radiographic progression-free survival, skeletal-related events, chemotherapy initiation, PSA response, soft tissue response, and pharmacokinetic measures. Testing multiple outcomes raises a general multiplicity issue: as the number of statistical tests grows, the chance of obtaining at least one small p-value by chance can increase if each test is assessed separately.

The registry record does not report a multiplicity adjustment strategy, a hierarchical testing sequence, or which secondary outcomes were intended to support confirmatory claims. It also does not report whether interim analyses were planned or conducted. These details should not be inferred from the phase or from the existence of posted results. Without a stated strategy, secondary p-values are best treated as nominal evidence rather than as results with a documented family-wise error guarantee.

The primary endpoint is described as using the ITT population with available data. The record also states that participants without confirmed PSA progression were censored. It does not provide detailed information about missing-data frequency, reasons for missingness, handling of missing assessments, or sensitivity analyses for the primary endpoint. The phrase “with available data” should not be expanded into an assumption about how unavailable observations were handled.

The registry does not report further analysis-population definitions for each secondary endpoint in the information summarized for this study. It is therefore not possible to establish from the record whether every secondary outcome used the same population or the same rules for censoring and missing observations. Such differences can affect interpretation, particularly where outcomes depend on follow-up, central imaging review, or continued observation.

In general, missingness and censoring matter because conclusions can be sensitive to who remains under observation and why observation ends. Randomization supports treatment-group comparisons, but it does not automatically resolve every issue arising after randomization. The available record supports describing the named analysis population, endpoint definitions, and reported estimates; it does not support claims about unreported missing-data procedures or multiplicity control.

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: pneumonia (7.9%), haematuria (4.0%), cataract (3.9%), nausea (3.9%), vomiting (3.9%).

The serious-adverse-event counts are reported separately for the enzalutamide group, the placebo group, and participants who crossed from placebo to enzalutamide. The registry lists 87 serious adverse events among 202 participants at risk in the enzalutamide group, 57 among 193 at risk in the placebo group, and 24 among 51 at risk in the crossover group. These counts should be read with the group labels and denominators as reported, not combined across groups.

The registry also lists deaths of 85, 57, and 21 in those respective safety groups. These are reported death counts; the record excerpt does not establish that the deaths were caused by treatment. It also reports other, non-serious adverse events for each group, but counts alone do not describe severity, duration, relatedness, or exposure time.

The most frequently listed serious adverse-event terms include pneumonia at 7.9%, haematuria at 4.0%, cataract at 3.9%, nausea at 3.9%, vomiting at 3.9%, and septic shock at 3.9%. These percentages should be interpreted as registry-reported terms, not as a complete account of all possible harms. The crossover group has a different treatment history from the randomized groups, so its results are not a like-for-like randomized comparison. Follow-up and exposure details needed for adjusted safety comparisons are not reported in the registry record.

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

The primary result describes a statistically clear difference in time to PSA progression between the randomized groups in the analyzed population. The reported hazard ratio is below 1, its 95% confidence interval remains below 1, and the p-value is p < 0.001. The median estimates also differ between groups. These findings characterize the posted primary endpoint; they do not establish what will happen to a particular participant.

The endpoint is based on a PSA-progression definition and should not be equated with survival, radiographic progression, symptom relief, or quality of life. The registry reports separate secondary outcomes for some of these domains, with differing levels of statistical precision. A result on one endpoint does not automatically establish the same effect on another. In particular, the primary result alone cannot answer whether the observed difference translates into a broader clinical benefit or how it should be weighed against adverse events.

Random assignment and masking are important design features because, in general, they help protect comparisons from systematic differences in treatment allocation and outcome assessment. They do not remove uncertainty, guarantee that every analysis assumption is satisfied, or make the results applicable to populations not studied. This trial concerned chemotherapy-naïve participants with progressive metastatic prostate cancer after failure of androgen deprivation therapy, and its findings should be understood within that population and treatment setting.

The posted safety counts provide descriptive information, but do not establish treatment causality for each event or death. The crossover group also complicates simple comparisons after the double-blind period because those participants received enzalutamide following placebo assignment. The registry record does not report enough exposure and attribution detail to resolve those questions from the listed counts alone.

Overall, the record supports a clear statistical conclusion about the primary PSA-progression comparison and provides additional, less definitive information about secondary outcomes and safety. It does not, by itself, settle questions about long-term outcomes, quality of life, comparative harms over equal exposure, or applicability outside the studied population. Those questions require evidence beyond the primary endpoint estimate.

19. Why This Trial Matters Statistically

This trial is statistically instructive because it reports both a biomarker-based primary time-to-event outcome and several broader secondary outcomes. The primary analysis combines a Kaplan-Meier estimate of time to PSA progression with a Cox-model hazard ratio. Reading these measures together illustrates why time-to-event studies often report both an event-time summary and a relative event-rate estimate: they describe different aspects of the data.

The design also makes the distinction between statistical evidence and clinical interpretation important. The primary hazard-ratio interval lies below 1, while the secondary outcomes vary in precision. The skeletal-related-event interval is notably broad and includes 1, unlike the reported intervals for the other posted time-to-event comparisons. This contrast helps show why a shared direction among point estimates does not mean that every endpoint provides equally strong evidence.

The placebo-to-enzalutamide crossover is relevant when reading the safety record and the overall study course. The randomized comparison is the basis for the principal treatment contrast during the blinded period; a later crossover group has a different treatment history. Keeping those groups distinct avoids treating descriptive safety counts as if they were all generated by the same randomized exposure comparison.

Finally, the registry illustrates the importance of separating sponsor-reported analyses from planning calculations. The reported hazard ratios and p-values address trial outcomes, whereas sample-size illustrations based on observed effects describe hypothetical planning requirements. Neither the observed result nor the planning illustration supplies unreported protocol details. Clear distinctions among endpoint, analysis population, follow-up, and inferential purpose are essential to a sound statistical reading.

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 unreported. It does not provide the original sample-size justification, the original design assumptions, or information about interim analyses. The planning illustrations based on the observed effect therefore cannot be used to reconstruct the sponsor's initial design rationale.

The primary analysis population is described as the ITT population with available data, but the record does not provide detailed counts or reasons for missing observations, missing-assessment procedures, or sensitivity analyses. It states that participants without confirmed PSA progression were censored, but does not report detailed censoring patterns. The proportional-hazards diagnostic and other model checks are also not reported in the registry record.

The registry lists multiple secondary outcomes but does not report a multiplicity-control plan in the summarized information. Secondary p-values may therefore have a different evidential status from the primary test. Detailed analysis populations and missing-data approaches for all secondary endpoints are not reported. These gaps limit independent assessment of the full analysis strategy.

Generalizability is also bounded by the recorded study population: chemotherapy-naïve participants with progressive metastatic prostate cancer after failure of androgen deprivation therapy in an Asian multinational study. The registry record does not provide country-level enrollment or further demographic detail in the information. Results should not be assumed to apply unchanged to populations or treatment settings not represented by the recorded eligibility description.

Finally, the safety summaries include a crossover group, and the record does not provide exposure-adjusted safety rates or detailed event attribution in the information summarized. The reported counts and terms are descriptive and cannot by themselves establish causation or support a complete comparison of harms over equivalent exposure.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: An Asian Study to Evaluate Efficacy and Safety of Oral Enzalutamide in Progressive Metastatic Prostate Cancer Participants — NCT02294461.
• Registry record last updated 2025-10-24; status last verified 2025-10.
• Results first posted 2017-04-12.
• 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

NCT02294461 is a completed phase 3 randomized, parallel-group, placebo-controlled study of oral enzalutamide in chemotherapy-naïve participants with progressive metastatic prostate cancer who had failed androgen deprivation therapy. The registry reports quadruple masking, an enrollment of 395, a start date of 2014-04-23, and a primary completion date of 2015-09-20.

The primary endpoint was time to PSA progression. The sponsor-reported unstratified Cox analysis gives a hazard ratio of 0.38, a 95% confidence interval from 0.27 to 0.52, and p < 0.001. Secondary outcomes include overall survival, rPFS, and time to first skeletal-related event, alongside other listed measures. The registry also reports adverse-event counts and a separate placebo-to-enzalutamide crossover group.

The primary result supports a difference in the specified PSA-progression outcome. Secondary findings, safety counts, and planning illustrations require separate interpretation and do not replace the primary analysis or fill gaps in unreported protocol and analysis details.