Prostate Cancer Study In Men Who Have Failed First-Line Androgen Deprivation Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prostate Cancer Study In Men Who Have Failed First-Line Androgen Deprivation Therapy (NCT00470834), a randomized phase 4 study. The primary outcome is Time to Disease Progression.

2. Clinical Question

The central question was whether adding dutasteride to bicalutamide was associated with a different time to disease progression than adding placebo to bicalutamide in men whose prostate cancer had failed first-line androgen deprivation therapy, as assessed by rising PSA. The comparison was randomized, double-blind, and parallel-group.

The question is about a comparison between two treatment strategies in this trial population, not about dutasteride in isolation: both groups received bicalutamide. The registry describes the biological rationale as inhibition of conversion of testosterone to dihydrotestosterone by dutasteride, with the possibility that this could allow bicalutamide to be a more effective anti-androgen. That rationale is not itself evidence of a difference in clinical outcomes.

3. Trial Design

The registry describes a randomized, double-blind, parallel-group Phase 4 study with an enrollment of 127 participants. The study compared bicalutamide 50 mg with dutasteride 3.5 mg against bicalutamide 50 mg with placebo. The planned treatment period was 18 months, followed by a two-year extension phase. The registry record marks the study as completed.

The study began in 2007-05, and primary completion was recorded in 2013-02. GlaxoSmithKline is listed as the sponsor. The registry describes the condition as prostate neoplasms and the intended population as men with prostate cancer who had failed first-line androgen deprivation therapy, with failure assessed by rising PSA.

Random allocation is intended to make the groups comparable, on average, with respect to both measured and unmeasured characteristics. Double masking is intended to limit differences in care or outcome assessment related to knowledge of assigned treatment. These are general design principles; the registry record does not report the sequence-generation method, allocation concealment procedures, or how masking was maintained.

The primary outcome was time to disease progression, with events assessed through Study Month 42. The registry also lists time to treatment failure, PSA response, change from baseline in total PSA at specified study months, and metastatic disease as secondary outcomes. The number of participants enrolled is not the same as the number represented in every outcome summary: the registry notes that participants without progression were censored and that their data were not summarized for the primary outcome.

The original sample-size justification and the assumptions used to design the trial are not reported in the registry record. The planning illustrations associated with the posted summaries are separate from the trial's original design calculations.

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.

Treatment Period (18 Months)

Reasons for not completing this period:

Extension Period (24 Months)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all participants randomized to study treatment. Data were not summarized for censored participants (no disease progression).

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 Time to Disease Progression, measured over Interval of time between the date of the start of treatment and the date of disease progression (up to Study Month 42).

The primary endpoint was time to disease progression, measured in days. It was defined as the interval between the start of treatment and the date of progression, assessed up to Study Month 42. The endpoint combines several ways in which disease status could worsen: specified PSA progression from baseline or nadir, radiographic evidence of metastatic disease, death due to prostate cancer, or receipt of post-baseline rescue medication.

The PSA criteria distinguish progression according to baseline and nadir values, including whether PSA had previously decreased from baseline. The specified PSA changes required confirmation by a second PSA value, except when no subsequent PSA values were available. Participants without an event were censored at the date of their latest follow-up information.

Time-to-progression endpoints are used to capture both whether an event occurs and when it occurs. In general, this can retain timing information that a simple event count would omit. The registry's posted primary summaries, however, are means and standard deviations, and it states that data for censored participants were not summarized. That qualification matters: the displayed mean summaries do not by themselves describe the full follow-up experience of everyone randomized. The registry record does not report further details about how censored observations were handled in the sponsor's primary analysis beyond the stated censoring definition.

7. Results Posted in the Registry

• Bicalutamide 50 mg/Dutasteride 3.5 mg: mean 433.10 versus 376.90 on control; difference 56.20 (95% CI -87.14 to 199.54), standardized effect d = 0.17; z-test p = 0.442.

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 Treatment Failure

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Bicalutamide 50 mg/Dutasteride 3.5 mg: mean 457.50 versus 368.40 on control; difference 89.10 (95% CI -75.91 to 254.11), standardized effect d = 0.28; z-test p = 0.290.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bicalutamide 50 mg/Dutasteride 3.5 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering time to treatment failure, PSA response, change from baseline in total PSA at specified study months, and metastatic disease. The numerical secondary summary available in the record includes time to treatment failure. Results for the other listed secondary outcomes are not reported in the registry record described by these statistics, so their direction and precision cannot be assessed.

The time-to-treatment-failure summary has a recalculated mean difference of 89.1 days, with a 95% confidence interval from -75.91 to 254.1 days and an unadjusted p-value of 0.29. As with the primary endpoint, this is a comparison of posted means and does not replace a time-to-event analysis. It also describes a different endpoint from disease progression, so agreement or disagreement between the two endpoints would not by itself establish a single overall treatment effect.

At a broad level, the secondary evidence does not provide a precise, independently persuasive pattern that changes the interpretation of the primary result. The available numerical secondary comparison remains uncertain, while the other registered outcome domains lack results in the registry record. It is therefore not possible to assess whether PSA response, PSA changes, or metastatic disease outcomes consistently support or qualify the primary finding.

General explanation: multiple secondary outcomes create multiple opportunities to observe apparently notable results by chance, especially when many tests are examined. Unless a multiplicity strategy is specified, individual secondary p-values are usually less conclusive than a prespecified primary analysis. The registry record does not report a multiplicity adjustment or a hierarchy for testing secondary outcomes. Secondary results can provide context and generate further questions, but unadjusted results should be interpreted cautiously and should not be treated as equivalent to a confirmatory primary result.

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

• Time to Treatment Failure
• Number of Participants With PSA Response
• Change From Baseline in Total PSA at Months 6, 12, 18, 21, and 42
• Number of Participants With Metastatic Disease

9. Statistical Interpretation

10. Statistical Methods Explained

The statistical summaries involve two different kinds of analysis: a recalculation from posted group summaries and analyses reported by the sponsor in the registry. These answer related but not identical questions. Keeping the methods distinct is important when reading the numerical results.

What does a mean comparison describe?

The primary outcome is a continuous measure recorded in days, and the registry identifies its summary parameter as a mean with standard deviation. A mean describes the average of the observations included in that summary. A standard deviation describes how spread out individual observations are around the mean. These are general statistical definitions. In this trial, the registry states that participants who were censored without disease progression were not summarized for the primary outcome, so the posted means should not be interpreted as means for every randomized participant.

The unadjusted recalculation compares the two posted group means. Its estimated mean difference is 56.2 days for bicalutamide plus dutasteride relative to bicalutamide plus placebo. The associated 95% confidence interval runs from -87.14 to 199.5 days, and the unadjusted p-value is 0.442. The term “unadjusted” means that this recalculation uses the group summaries without adjustment for covariates or other trial features. It is not a replacement for a prespecified sponsor analysis.

Why is the log-rank analysis different?

General explanation: a log-rank test compares event-time experience between groups while accounting for the ordering of events and censoring. It is commonly used for time-to-event outcomes. The registry reports a log-rank p-value of 0.79 for the comparison. A log-rank result is not a test of the same quantity as a difference between arithmetic means, so the two p-values need not match. The registry record does not describe additional details of the sponsor's log-rank implementation, such as any stratification or adjustment.

General explanation: censoring occurs when a participant's event time is not observed during the available follow-up, while some follow-up information is available up to a last contact or assessment. Censoring does not mean that progression occurred at the censoring date. The registry says participants without progression were censored at the date of their latest follow-up information and that their data were not summarized in the primary mean outcome. The full statistical handling of censoring in the sponsor analysis is not reported in the registry record.

What does a confidence interval convey?

General explanation: a confidence interval represents the uncertainty around an estimate under the assumptions of the method used. A wider interval indicates less precision than a narrower interval. The primary recalculated interval includes both negative and positive differences, so the posted summary does not narrowly determine the direction or size of the mean difference. A confidence interval is not a range that guarantees where the true value lies, and it does not directly measure clinical importance.

What do the relative-risk summaries add?

The registry reports a relative risk of 0.94 and a relative risk reduction of 5.62, each with a 95% confidence interval. These are different effect measures from a difference in mean days. The record does not specify enough detail next to these summaries to establish the precise time point, event definition, or calculation used for them. They should not be combined with the mean difference as if all three were estimates of the same parameter.

General explanation: relative measures compare event occurrence between groups on a ratio-based scale, whereas an absolute difference expresses a contrast in the original units. Relative measures can be difficult to interpret without knowing the event definition and the underlying risks. The registry record does not supply the contextual details needed to translate the reported relative measures into a specific absolute risk contrast.

Why do distributions and endpoint definitions matter?

General explanation: time-to-event data can be skewed, and participants may have different follow-up durations. A mean may not capture the timing pattern as fully as an analysis that uses event times and censoring. The posted summaries give standard deviations, but the registry record does not report the shape of the outcome distribution. The composite progression definition also combines several event types, so the primary result is a result for that defined composite rather than for each component separately.

The registry reports the PSA confirmation rule and its exception when no later PSA value was available. It does not report whether additional sensitivity analyses tested alternative endpoint definitions or assumptions. Likewise, the record does not report the original analysis plan, interim analyses, or a detailed missing-data strategy. These omissions limit how much can be inferred about robustness beyond the results that are explicitly reported.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 56.2 days, with a 95% confidence interval from -87.14 to 199.5 days. The interval spans values below and above zero, so the estimate is compatible with a range of possible differences, including no mean difference. Its width indicates that the mean-based estimate is not precise enough to pin down a narrow effect range.

General explanation: precision concerns the uncertainty around an estimate, not whether an effect is beneficial, harmful, or clinically important. A confidence interval is interpreted in relation to the measure being estimated and the assumptions behind the analysis. For a mean difference, zero represents no difference between the group means. Because the reported interval includes zero, the recalculation does not exclude no mean difference at the interval's stated confidence level.

The sponsor's log-rank analysis reports p = 0.79 but no effect estimate or confidence interval for that analysis in the registry record. The separately reported relative risk has a 95% confidence interval from 0.61 to 1.46, and the relative risk reduction has a 95% confidence interval from -46.14 to 39.05. These intervals also reflect uncertainty, but the record does not establish sufficient detail about their exact estimands to equate them with the mean-difference interval.

The primary summaries are further limited by the registry's note that censored participants without progression were not included in the mean summary. The displayed precision therefore pertains to that posted summary and should not be mistaken for a complete characterization of time-to-event uncertainty for all randomized participants. The registry record does not report additional confidence intervals for the group means or the sponsor's log-rank effect estimate.

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 participants per arm for the mean-based endpoint, not total event counts. They are planning illustrations computed from the observed effect, not the trial's original sample-size justification. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and a target effect set to the stated fraction of the observed effect. The trial's own original design assumptions are not reported in the registry record.

The 80% power column describes an illustrative sample size per arm intended to give an 80% chance of detecting the chosen effect under those planning assumptions, if that effect were the true effect. The 90% power column describes the corresponding illustration for a 90% chance. These are planning probabilities under a model, not guarantees about a future result. The sample-size curve expresses the same general relationship: the required planned sample grows as the target effect becomes smaller.

For example, the row planning for 100% of the observed effect gives 539 participants per arm for 80% power and 722 participants per arm for 90% power. Planning for 75% of the observed effect gives 958 participants per arm for 80% power and 1,282 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,155 participants per arm for 80% power and 2,885 participants per arm for 90% power. The increasing requirements illustrate why smaller effects need more participants to detect under otherwise unchanged assumptions.

This is not observed power. The figures do not measure the probability that the completed trial detected its true effect, nor do they establish what the trial was originally designed to detect. They are hypothetical planning illustrations based on the observed mean difference and the stated assumptions.

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

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 56.200; pooled standard deviation σ = 329.192.
2. n = 2 × (1.96 + 0.842)² × 329.192² / 56.200² = 538.6, rounded up to 539 participants per arm 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
delta <- 56.2                      # observed difference in means
sigma <- 329.191979336517                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(470834)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 539 (80% power), 722 (90% power)
 75% of observed effect: n per arm = 958 (80% power), 1,282 (90% power)
 50% of observed effect: n per arm = 2,155 (80% power), 2,885 (90% power)
power.t.test: 539.6 
Simulated power at n = 539 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis of the primary time-to-progression outcome using the log-rank method, with p = 0.79. It also reports a relative risk of 0.94 with a 95% confidence interval from 0.61 to 1.46, and a relative risk reduction of 5.62 with a 95% confidence interval from -46.14 to 39.05. The record does not fully describe the estimand and time point associated with those relative measures.

The recalculation from the posted means is a separate, unadjusted comparison: it estimates a mean difference of 56.2 days, with a 95% confidence interval from -87.14 to 199.5 days and an unadjusted p-value of 0.442. A log-rank test and a mean comparison use different summaries of time-to-event data, so their results should not be expected to match numerically. The sponsor analysis and recalculation address the same broad primary outcome but are not identical statistical tests.

The registry record identifies no discrepancy between the posted summaries and the recalculation. That does not make the recalculation a substitute for the sponsor's analysis. The sponsor's result should be read as the reported time-to-event analysis, while the recalculated result is a transparent, unadjusted comparison based on the posted group means and standard deviations. The registry does not report further details about adjustments, stratification, or the analysis plan that would allow a fuller reconciliation.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary endpoint and several secondary outcome domains, but it does not report a multiplicity strategy. In particular, it does not state whether secondary tests were adjusted, ordered in a prespecified hierarchy, or treated as exploratory. When several outcomes are tested, the chance of at least one apparently unusual result can increase. General statistical practice therefore distinguishes a prespecified primary analysis from multiple secondary comparisons, especially when the latter are unadjusted.

The record also does not report the trial's full statistical analysis plan, the original sample-size justification, or whether interim analyses were planned or conducted. Those details cannot be inferred from the posted outcome summaries. The absence of these details makes it harder to determine which analyses were prespecified and how the study's statistical error rates were intended to be controlled.

The primary endpoint definition does describe censoring: participants without progression were censored at their latest follow-up information, and the registry states that censored participants were not summarized in the primary mean outcome. PSA confirmation was not required when no subsequent PSA values were available. The registry does not report additional information on missing-data imputation, sensitivity analyses for missing data, or other approaches to evaluate the effect of incomplete follow-up.

The primary population is defined as the Intent-to-Treat population, comprising all participants randomized to study treatment. However, the posted primary mean summaries list 41 participants in the placebo group and 40 in the dutasteride group, while the study enrollment was 127. The registry's note about excluding censored participants from the summary is relevant to this difference in the populations represented. The record does not report a complete accounting that reconciles every randomized participant with each endpoint analysis.

These reporting gaps do not establish that a particular method was or was not used; they mean that the method is not reported in the registry record. Interpretation should stay within the defined endpoint, the stated analysis populations, and the results that are actually available.

16. 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: pneumonia (4.6%), cerebrovascular accident (3.2%), transient ischaemic attack (3.2%), myocardial infarction (3.2%), cardiac failure congestive (3.2%).

The registry reports serious adverse events in 31 of 65 participants at risk in the bicalutamide-plus-placebo group and 30 of 62 participants at risk in the bicalutamide-plus-dutasteride group. It reports other adverse events in 48 of 65 and 51 of 62 participants at risk, respectively. These are counts of participants affected, not measures of treatment effect adjusted for follow-up or differences in exposure.

The serious adverse-event terms listed most often include pneumonia at 4.6%, cerebrovascular accident at 3.2%, transient ischaemic attack at 3.2%, myocardial infarction at 3.2%, cardiac failure congestive at 3.2%, and cellulitis at 3.2%. The registry's serious-event group figures and the listed terms describe the reported safety data; they do not by themselves establish that an event was caused by a study treatment.

Death counts are not reported in the registry record. The record also does not provide enough detail to compare event timing, duration, severity beyond the serious classification, or exposure-adjusted rates. Safety interpretation should therefore remain descriptive and should not be used to infer a causal difference between groups from these counts alone.

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

The results describe a randomized comparison of bicalutamide plus dutasteride with bicalutamide plus placebo among men with prostate cancer who had failed first-line androgen deprivation therapy. For the primary endpoint, the posted mean summaries produce a positive mean difference for the dutasteride group, but the confidence interval is broad and includes zero. The sponsor's log-rank analysis also does not provide a precise effect estimate in the registry record. Taken together, the posted statistics leave substantial uncertainty about the size and direction of any difference in disease progression time.

This does not establish equivalence between the treatments. A result that does not precisely distinguish groups is not the same as evidence that the groups are identical. It also does not show that the observed numerical difference is clinically important. The registry record does not report a threshold for clinical importance, and the confidence interval includes a range of possible effects.

The endpoint combines PSA progression, metastatic disease, prostate-cancer death, and rescue medication. The result applies to that registry-defined composite and to the study's stated population and follow-up. It does not independently establish results for each component of the composite. Participants who had no progression were censored, and the registry says their data were not summarized in the primary mean summaries.

The secondary information is incomplete for interpretation across all listed outcomes. Time to treatment failure has a posted mean comparison, but results for PSA response, PSA change, and metastatic disease are not reported in the registry record described by these statistics. The available secondary information therefore cannot establish a consistent pattern across all outcome domains.

These findings are statistical descriptions of this trial's posted data. They do not provide medical advice, prove a treatment effect, or establish that there is no treatment effect. Their meaning depends on the endpoint definitions, analysis methods, uncertainty, and reporting limitations described in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why a single point estimate should not be read in isolation. The recalculated mean difference is positive, but its confidence interval ranges from -87.14 to 199.5 days. That interval communicates substantial uncertainty about the size and direction of the contrast. Reporting the estimate together with its interval is more informative than treating the point estimate or p-value as a complete account of the evidence.

It also shows how the choice of statistical method matters for time-to-event outcomes. The registry's sponsor analysis uses a log-rank method, while the recalculation compares posted means. These methods summarize different features of the outcome and should not be collapsed into one result. The registry's note that censored participants were not summarized in the mean outcome further emphasizes that a mean-based summary may not represent all randomized participants' event-time experience.

The trial is also a useful example of the distinction between a study's original design and retrospective planning illustrations. Sample-size figures derived from the observed effect can help readers understand how planned requirements change for different target effects, but they are not evidence about the trial's original assumptions or achieved power. The original sample-size rationale is not reported in the registry record.

Finally, the outcome list and reporting gaps matter. A primary result can be understood only in light of its endpoint definition, while unadjusted secondary analyses need caution when multiple outcomes are considered. The registry record's incomplete secondary results and unreported multiplicity strategy limit the strength of any broad claim based on secondary outcomes. These are general lessons in evaluating clinical trial statistics, grounded in the details and omissions of this particular record.

19. 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 primary mean summaries exclude participants censored without disease progression, according to the registry. That means the summaries do not represent all randomized participants, even though the stated analysis population is the Intent-to-Treat population. The registry record does not provide a complete participant flow accounting for the primary endpoint or explain in detail how the sponsor's time-to-event analysis handled censoring.

The primary endpoint is a composite that includes several distinct events: PSA progression under specified rules, metastatic disease, death due to prostate cancer, and rescue medication. The record does not report component-specific results, so it is not possible to determine whether one event type dominated the composite result. The PSA confirmation exception when no further PSA measurement was available is stated, but the record does not report sensitivity analyses for this rule.

The registry reports a sponsor log-rank p-value and relative measures, but provides limited detail about the estimands and methods for the latter. The unadjusted recalculation uses posted means and standard deviations and is not the same as the sponsor's time-to-event analysis. The registry record does not report the full statistical analysis plan, adjustment or stratification details, or the original sample-size assumptions.

Secondary outcome reporting is also incomplete in the available record: numerical results are not reported for PSA response, PSA changes, or metastatic disease. A multiplicity strategy is not reported. The serious adverse-event summary is descriptive, and death counts are not reported. These limitations constrain interpretation of efficacy, secondary outcomes, and safety without establishing that unreported analyses were not conducted.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Prostate Cancer Study In Men Who Have Failed First-Line Androgen Deprivation Therapy — NCT00470834.
• Registry record last updated 2017-02-27; status last verified 2016-11.
• Results first posted 2013-11-01.
• 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.

23. Record Summary

NCT00470834 is a completed, randomized, double-blind, parallel-group Phase 4 study sponsored by GlaxoSmithKline, with an enrollment of 127. It compared bicalutamide 50 mg plus dutasteride 3.5 mg with bicalutamide 50 mg plus placebo in men with prostate cancer who had failed first-line androgen deprivation therapy.

The primary endpoint was time to disease progression, assessed through Study Month 42. The recalculated mean difference was 56.2 days, with a 95% confidence interval from -87.14 to 199.5 days and an unadjusted p-value of 0.442. The sponsor's reported log-rank analysis had p = 0.79. These analyses use different methods, and the posted results leave the size and direction of any difference uncertain.

The registry also lists secondary outcomes and reports serious and other adverse-event counts. Important details, including the original sample-size assumptions, multiplicity approach, and several secondary outcome results, are not reported in the registry record.