Aflibercept in Combination With Docetaxel in Metastatic Androgen Independent Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Aflibercept in Combination With Docetaxel in Metastatic Androgen Independent Prostate Cancer (NCT00519285), a randomized phase 3 study. The primary outcome is Overall Survival Time.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group study with an enrollment of 1224. Participants were assigned to aflibercept or placebo, each added to docetaxel and prednisone or prednisolone. The registry records triple masking. The official title describes the study as double blind; which specific people were masked is not reported in the registry record.

The study began in 2007-08, reached primary completion in 2012-04, and is listed as completed. Its stated primary objective was to demonstrate an overall survival improvement with aflibercept compared with placebo in patients receiving docetaxel and prednisone for metastatic androgen-independent prostate cancer. Secondary objectives covered other efficacy measures, safety, pharmacokinetics, and immunogenicity.

The primary endpoint analysis used the intent-to-treat population, retaining randomized participants in their assigned groups regardless of the drug actually received. Each group had 612 participants in the primary endpoint summary. At the cutoff, the registry describes a median follow-up of 35.4 months and 873 deaths, with 445 in the placebo group and 428 in the aflibercept group. The analysis censored participants without a confirmed death at the last date they were known to be alive or the cutoff date, whichever was earlier.

The registry identifies a range of secondary outcomes, including prostate-specific antigen response, progression-free survival, tumor response among participants with measurable disease, pain outcomes, skeletal events, and health-related quality of life. The listed secondary objectives also included safety, pharmacokinetics, and immunogenicity. Further details about treatment exposure, adherence, and the roles of people masked to assignment 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: Amongst these patients, a total of 324 were screening failures (primarily due to non-compliance with exclusion criteria) and did not get randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis was performed on the Intent-to-treat (ITT) population (i.e all randomized participants according to the treatment assigned regardless of the drug actually received). At the cut-off date, 873 deaths had occurred, 445 in the Placebo group and 428 in the Aflibercept group.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival Time, measured over From randomization up to the cut-off date (median follow-up of 35.4 months).

Overall survival time was measured from randomization to death from any cause. Participants without a confirmed death were censored at the last date they were known to be alive or the study cutoff, whichever came first. The registry reports a median overall survival estimate for each assigned group using the Kaplan-Meier method.

Overall survival is used in clinical trials because it captures the time until a direct, clearly defined event: death from any cause. It does not depend on a judgment that a tumor has changed by a particular amount, or on a decision about whether a symptom has progressed. Those other outcomes can provide additional information, but they measure different aspects of the disease course. Overall survival can also be affected by events and care occurring after randomization; the registry record does not report details about later treatment.

The median describes the point in the estimated survival distribution at which half of the participants are estimated to have experienced the event and half to remain event-free. It is not a measure of the experience of every participant, nor does it by itself compare the entire survival patterns. The hazard ratio and its confidence interval provide a separate summary of the relative event rates over follow-up under the analysis used. These measures should be read together, with attention to uncertainty and the censoring process.

7. Results Posted in the Registry

• Placebo vs Aflibercept: hazard ratio 0.94 (95% CI 0.82–1.08), reported p = 0.380 (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.

Prostate Specific Antigen Response Rate

• 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:
  • Aflibercept: 68.6% (384/560) versus 63.5% (355/559) on control; risk difference 5.1 percentage points (95% CI -0.5 to 10.6), risk ratio 1.08 (0.99–1.17); unadjusted two-proportion z-test p = 0.074.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept and the control. The interval gives the range of effects that remain compatible with the data.

Tumor Response Rate in Participants With Measurable Disease

• 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:
  • Aflibercept: 38.7% (125/323) versus 28.1% (90/320) on control; risk difference 10.6 percentage points (95% CI 3.3 to 17.8), risk ratio 1.38 (1.10–1.72); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Aflibercept than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Pain Response Rate

• 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:
  • Aflibercept: 35.8% (24/67) versus 46.3% (31/67) on control; risk difference -10.4 percentage points (95% CI -27.0 to 6.1), risk ratio 0.77 (0.51–1.17); unadjusted two-proportion z-test p = 0.219.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains rather than a single alternative measure of survival. The posted response outcomes do not all point in the same direction: the response comparisons vary, and their precision also differs. The tumor-response comparison is the clearest unadjusted signal in the listed results, while the PSA-response comparison is less conclusive and the pain-response comparison does not show a clear difference. These findings do not alter the interpretation of the primary overall-survival analysis.

Other listed secondary outcomes include progression-free survival, time to skeletal-related events, PSA progression-free survival, pain progression-free survival, and health-related quality of life. Their estimates and comparisons are not reported in the registry record. The registry’s secondary objectives also included safety, pharmacokinetics, and immunogenicity; detailed results for pharmacokinetics and immunogenicity are not reported in the registry record.

Secondary outcomes can help describe effects beyond the primary endpoint, but each addresses a distinct question and may use a different analysis population or measurement process. A pattern across several measures can be informative, yet results from multiple comparisons are more vulnerable to chance findings when no multiplicity adjustment is reported. The registry does not report whether such an adjustment was planned or applied. The secondary results should therefore be treated as supportive and exploratory in interpretation, rather than as independent confirmation of an overall survival effect.

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

• Prostate Specific Antigen Response Rate
• Time to Skeletal Related Events
• Progression Free Survival Time
• Tumor Response Rate in Participants With Measurable Disease
• Prostate Specific Antigen Progression-free Survival Time
• Pain Progression-free Survival Time
• Pain Response Rate
• Change From Baseline in Functional Assessment of Cancer Therapy-Prostate Total Score as a Measure of Health Related Quality of Life

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis uses methods suited to time-to-event data. Such data record not only whether an event occurred, but also the time from a defined starting point to the event. Here, time began at randomization and the event was death from any cause. Participants who were not known to have died by the cutoff could still contribute information up to their last known-alive date.

What does Kaplan-Meier estimation do?

The Kaplan-Meier method estimates the probability of remaining event-free over time while accounting for censoring. When a participant is censored, their later event status is unknown, but their observed follow-up still contributes information up to the censoring time. The method uses the event and censoring times rather than treating every participant as if they had the same length of observation. The registry used this method to estimate median overall survival and its confidence intervals. The assumptions and checks used to assess censoring are not reported in the registry record.

What does the median summarize?

The median survival estimate is the time at which the estimated survival probability reaches the midpoint of the distribution. It provides an interpretable summary for each group, but it does not capture every feature of the survival pattern. Two groups can have similar medians and still differ at other points in follow-up, or have different medians without that difference being precisely estimated. For this reason, the registry also reports a hazard ratio and a log-rank test for the group comparison.

How should the hazard ratio be read?

A hazard ratio compares the event rates between groups over follow-up, according to the model or test convention used. A value of 1 represents no relative difference under that comparison; values on either side represent different directions of relative event rate. It is not a ratio of median survival times, and it does not directly state how many months an individual participant might live. The registry labels its result as placebo versus aflibercept and reports the hazard ratio as 0.942. The record does not provide further detail about the coding convention beyond that comparison label.

The log-rank test compares the observed event experience between the groups over follow-up. The reported p-value is 0.380. A p-value measures how unusual the data, or more extreme data, would be under a specified null hypothesis and the test assumptions; it is not the probability that the null hypothesis is true. It also does not quantify the clinical importance of a difference. The registry identifies the log-rank method for this comparison.

What do the confidence intervals add?

A confidence interval conveys uncertainty around an estimate under the method used to construct it. For the hazard ratio, the reported 95.6% interval extends from 0.822 to 1.08. Since it includes 1, the data are compatible with no relative difference as well as values on either side of that reference. The interval is not a range that guarantees the true effect lies within it. The median survival intervals likewise describe uncertainty around the group-specific estimates, not a direct interval for the difference between the medians.

The secondary binary outcomes are presented as percentages with confidence intervals. A percentage describes the observed response proportion among the participants contributing to that outcome; denominators can differ from the primary analysis population. Simple unadjusted comparisons can be recalculated from posted summary statistics, but such calculations do not replace an analysis that accounts for trial design features or multiple testing. For secondary outcomes, the registry does not list sponsor-reported analyses in the record.

The risk difference is one way to compare binary outcomes: it expresses the difference between group proportions on the percentage-point scale. A confidence interval around that difference reflects uncertainty in the comparison. If the interval includes zero, the data are compatible with no difference as well as differences in either direction. The p-values for the secondary comparisons are unadjusted; their interpretation should account for the fact that several outcomes were examined.

Why can event counts matter in planning?

For time-to-event comparisons, planning is often expressed in terms of the number of events rather than the number of people enrolled, because events provide the information used to estimate differences in event experience. The registry’s planning illustrations use total events for the primary time-to-event endpoint. For binary outcomes, the illustrations are expressed as participants per arm. These planning values depend on assumptions about the effect to detect, significance level, allocation, and statistical approximation; they are not observations from the trial.

The registry provides the sponsor’s reported primary analysis and posted outcome summaries. Details such as the original sample-size justification, interim analyses, covariate adjustment, subgroup methods, and procedures for handling multiplicity are not reported in the registry record. Those omissions limit how far the statistical methods can be reconstructed from the registry alone.

11. Confidence Intervals and Precision

The precision of an estimate is reflected partly in the width of its confidence interval: narrower intervals indicate less uncertainty under the method used, while wider intervals indicate more. The median overall survival estimates have overlapping confidence intervals, and the reported hazard-ratio interval spans values below and above 1. The latter means the primary comparison does not precisely rule out either direction of relative difference.

The hazard-ratio confidence interval is 0.822 to 1.08 at the reported 95.6% confidence level. Its inclusion of 1 aligns with the log-rank p-value of 0.380: neither result supports a statistically clear difference in the primary analysis. This does not prove that the groups are identical. It means the estimated effect remains uncertain at the precision represented by the interval.

The median estimates are 21.22 months for placebo and 22.14 months for aflibercept. Their respective intervals are 19.61 to 23.75 months and 20.3 to 24.08 months. These intervals concern each group’s median separately. They should not be treated as a confidence interval for the between-group difference. The registry does not report a confidence interval for that median difference.

Confidence intervals for secondary outcomes also vary in width, reflecting the amount of information available for each measure. Their denominators differ, and some outcomes are based on fewer participants than the primary analysis. Wider intervals make estimates less precise, while intervals that include a no-difference value do not establish a clear direction. Precision is distinct from clinical importance: an estimate can be precise without being important, or potentially important but imprecise.

All confidence intervals depend on statistical assumptions and the analysis method. They do not account automatically for the fact that multiple outcomes were examined, and they do not capture every possible source of bias or missing information. The registry does not report additional sensitivity analyses for the primary endpoint.

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 original trial design. For the primary time-to-event comparison, the figures represent total events, not participants per arm. For the other outcomes, the figures represent participants per arm. The registry’s 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 to the stated fraction of the observed effect; the time-to-event calculations use the Schoenfeld approach.

The 80% power column describes a planning scenario in which a study using the stated assumptions would have an 80% chance of detecting the specified effect under the alternative, if that effect were truly present. The 90% power column describes the corresponding 90% chance. Power is a design property under assumptions, not a probability that the trial conclusion is correct. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, the illustrations express the needed information as total events. They show 8,795 events for 80% power and 11,773 events for 90% power when planning for 100% of the observed effect. For smaller assumed effects, the event requirements are larger: the figures for 75% and 50% of the observed effect are given in the planning values. This illustrates the general principle that smaller effects are harder to distinguish from random variation and require more information.

For binary outcomes, the corresponding figures are participants per arm, rather than total events. These are not enrollment targets for the completed trial and do not describe its observed power. They are conditional planning illustrations derived from the observed effect and stated assumptions. The curve and figures should therefore be read as showing how hypothetical requirements change as the target effect and desired power change, not as a reconstruction of the trial’s original design.

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 = 0.942, so ln(HR) = -0.0598.
2. d = 4 × (1.96 + 0.842)² / [ln(0.942)]² = 8,794.1, rounded up to 8,795 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 <- 0.942                              # 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(519285)
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 = 8,795 (80% power), 11,773 (90% power)
 75% of observed effect: events = 15,634 (80% power), 20,930 (90% power)
 50% of observed effect: events = 35,177 (80% power), 47,092 (90% power)
Simulated power with 8,795 events: 0.804 (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 18,237 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 1,224 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 <- 21.22          # control-arm median, months (converted from the posted unit)
hr          <- 0.942          # 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: 15778         p (1-sided)   0.0001
  Events: 3971        ~HR at bound   0.8889
     Month: 21    P(Cross) if HR=1   0.0001
               P(Cross) if HR=0.94   0.0338
     IA 2: 67%                   Z   2.5114
      N: 18238         p (1-sided)   0.0060
  Events: 7941        ~HR at bound   0.9452
     Month: 33    P(Cross) if HR=1   0.0060
               P(Cross) if HR=0.94   0.5603
         Final                   Z   1.9930
      N: 18238         p (1-sided)   0.0231
 Events: 11911        ~HR at bound   0.9641
     Month: 60    P(Cross) if HR=1   0.0250
               P(Cross) if HR=0.94   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 result reported by the registry is the sponsor’s log-rank analysis: a hazard ratio of 0.942 for placebo versus aflibercept, with a 95.6% confidence interval from 0.822 to 1.08 and p=0.380. The registry also reports group-specific Kaplan-Meier median estimates and confidence intervals. These are the posted primary results and should anchor interpretation of the survival comparison.

The record does not flag a discrepancy between the sponsor’s result and a recalculation. The primary survival comparison is not replaced by an unadjusted recalculation from summary statistics; the sponsor’s reported analysis is the relevant analysis for that endpoint. The secondary outcome comparisons are simple unadjusted calculations from posted summaries, and no sponsor-reported analyses for those outcomes are listed in the registry record.

Unadjusted secondary calculations can help describe the direction and uncertainty in the posted summaries, but they may not reproduce analyses that account for design details, covariates, or multiplicity. Such methods are not reported for those secondary outcomes in the registry record. Consequently, the secondary calculations should be read as descriptive comparisons, not as substitutes for a prespecified sponsor analysis.

16. Multiplicity, Missing Data and Analysis Populations

The trial has one stated primary objective focused on overall survival and a range of secondary objectives. When researchers examine multiple outcomes, the chance of at least one apparently notable result arising by chance can increase. Statistical procedures can address this issue, but the registry record does not report a multiplicity strategy, such as a hierarchy of testing or adjustment of significance thresholds. The secondary comparisons available in the registry are unadjusted, so their p-values should not be interpreted as if each were the only comparison conducted.

The primary population is explicitly identified as intent-to-treat: randomized participants were analyzed according to assigned treatment regardless of the drug actually received. That supports interpretation of the primary comparison as an analysis by randomized assignment. The registry does not provide the corresponding analysis population details for each secondary outcome beyond the denominators associated with the posted summaries.

For overall survival, the stated missing-event approach is censoring participants without a confirmed death at their last known-alive date or the study cutoff, whichever was earlier. This makes use of observed follow-up, but the registry record does not report sensitivity analyses for alternative censoring assumptions, the amount of missing follow-up, or other methods for addressing missing outcome information. Details of missing-data handling for secondary measures are not reported in the registry record.

Interim analyses, stopping rules, the original sample-size justification, and a fuller statistical analysis plan are also not reported in the registry record. This does not establish that such procedures were absent; it means their use cannot be assessed from the registry information summarized. The available results can be interpreted as posted, while conclusions about prespecification, multiplicity control, and robustness to missing data remain limited.

17. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (7.9%), neutropenia (4.9%), neutropenic infection (3.6%), pneumonia (3.4%), epistaxis (3.3%).

The registry lists serious adverse events among participants at risk: 184 of 598 in the placebo group and 331 of 611 in the aflibercept group. It separately lists other adverse events for 551 of 598 and 573 of 611, respectively. These are counts, not percentages, and should be read with their stated denominators. The registry does not explain in this record why the safety denominators differ from the primary analysis group sizes.

The listed serious adverse-event terms include febrile neutropenia at 7.9%, neutropenia at 4.9%, neutropenic infection at 3.6%, pneumonia at 3.4%, epistaxis at 3.3%, and dehydration at 3.1%. The registry summary does not specify a treatment group alongside these term percentages, so they should not be attributed to one group from this information alone. Death counts in the adverse-event summary are not reported in the registry record.

These safety entries describe events recorded during the trial; they do not by themselves establish that a treatment caused an event. The registry summary does not provide event timing, duration, recurrence, or a fuller account of how adverse events were adjudicated. The counts should be considered alongside the design and the specific safety definitions used, which are not fully detailed in the record.

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

The primary survival analysis estimates outcomes in randomized groups receiving aflibercept or placebo in addition to docetaxel and prednisone or prednisolone. The group-specific median estimates are close, and the reported hazard-ratio confidence interval includes 1. The log-rank p-value does not indicate a statistically clear difference in overall survival under the reported analysis.

This result does not prove that the groups had identical outcomes. A non-significant comparison can arise when the true difference is small, when estimates are uncertain, or for other reasons; the interval describes the uncertainty that remains. Nor does the result show that aflibercept has no effect on every secondary outcome. The registry reports selected secondary results that address different measures, with mixed directions and varying precision.

The result also does not establish effects in populations or treatment settings not represented by this trial. The study concerned metastatic androgen-independent prostate cancer in participants receiving the stated chemotherapy backbone. The registry record does not provide enough detail to assess how the findings vary by participant characteristics, later treatment, or other clinical contexts.

Overall survival is a direct endpoint, but it is only one part of the study’s stated objectives. Response rates, progression measures, pain, skeletal events, and quality of life describe other outcomes. Some of those results are not reported in the registry record, and the available secondary comparisons are unadjusted. They should not be combined into a single conclusion that goes beyond what each measure and its uncertainty support.

These statistics describe the posted trial results and their precision. They are not personal predictions, and they do not provide medical advice. Interpretation of an individual treatment decision requires clinical context beyond the registry analysis.

19. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be interpreted through both its estimated effect and its uncertainty. The primary endpoint is overall survival, analyzed from randomization with Kaplan-Meier methods and a log-rank comparison. The reported hazard ratio, confidence interval, and p-value do not establish a statistically clear difference, while the interval also does not prove equivalence.

It also shows why different summaries answer different questions. Median survival estimates describe a point in each group’s estimated survival distribution; the hazard ratio summarizes relative event experience over follow-up. Looking at both avoids treating one number as a complete description of the survival data. Censoring is part of time-to-event analysis, so the stated rule for participants without a confirmed death matters to understanding how follow-up contributes.

The secondary outcomes make another statistical point: a favorable-looking result on one measure is not the same as a consistent result across outcomes, particularly when multiple comparisons are made. The available secondary responses vary in direction and certainty, and the registry does not report a multiplicity strategy. This makes a careful distinction between the primary analysis and unadjusted secondary findings essential.

Finally, planning illustrations are not evidence that a completed trial was adequately or inadequately powered. They are conditional calculations from an observed effect under stated assumptions. The original design assumptions are not reported in the registry record. Separating those planning scenarios from observed results prevents a planning exercise from being mistaken for a retrospective test of the trial’s conclusions.

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 provide the original sample-size justification or the assumptions used to plan the completed trial. The planning illustrations based on the observed effect cannot fill that gap. Interim analyses and stopping rules are also not reported, so their role in the conduct or interpretation of the study cannot be assessed from this record.

Although the primary analysis is identified as intent-to-treat and the survival censoring rule is described, the record does not report sensitivity analyses for censoring or missing data. The analysis population details for the secondary outcomes are not fully described, and their denominators differ across measures. These differences limit direct comparisons of precision across outcomes.

The primary comparison is reported with a hazard ratio, confidence interval, and log-rank p-value, but the record does not give further detail about covariate adjustment or the assumptions checked for the time-to-event analysis. It also does not report a multiplicity plan for the numerous secondary measures. The posted secondary comparisons are unadjusted, and results for several listed outcomes are not reported in the registry record.

The registry describes triple masking, while the official title describes a double-blind study; which study roles were masked is not reported in the registry record. The safety summary provides counts and selected event terms, but does not provide fuller detail on timing, event attribution, or the group associated with the listed term percentages. These reporting gaps do not show that the procedures or analyses were absent, but they constrain independent assessment from the registry information alone.

Finally, the study population and treatment regimen are specific: metastatic androgen-independent prostate cancer treated with docetaxel and prednisone or prednisolone. The record does not establish how the results apply to other populations or treatment settings.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Aflibercept in Combination With Docetaxel in Metastatic Androgen Independent Prostate Cancer — NCT00519285.
• Registry record last updated 2016-07-22; status last verified 2016-06.
• Results first posted 2013-10-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

24. Record Summary

The registry describes a completed phase 3 randomized parallel-group trial of aflibercept versus placebo added to docetaxel and prednisone or prednisolone for metastatic androgen-independent prostate cancer. Enrollment was 1224, and the primary endpoint was overall survival in the intent-to-treat population.

The Kaplan-Meier median estimates were 21.22 months for placebo and 22.14 months for aflibercept. The reported placebo-versus-aflibercept hazard ratio was 0.942, with a 95.6% confidence interval from 0.822 to 1.08 and a log-rank p-value of 0.380. The primary comparison does not establish a statistically clear difference.

Selected secondary response outcomes show mixed patterns, and the available secondary comparisons are unadjusted. Safety counts and selected serious adverse-event terms are also listed. The registry does not report several statistical-plan details, including the original sample-size justification and multiplicity strategy.