Radiation Therapy With or Without Androgen-Deprivation Therapy in Treating Patients With Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Radiation Therapy With or Without Androgen-Deprivation Therapy in Treating Patients With Prostate Cancer (NCT00936390), a randomized phase 3 study. The primary outcome is Percentage of Participants Alive (Overall Survival).

2. Clinical Question

The trial record describes a prospective, randomized phase III comparison with two parallel arms and no masking. Its stated purpose was to compare radiation therapy alone with radiation therapy given together with androgen-deprivation therapy. The question is clinically and statistically focused on the incremental contribution of the added therapy within the radiation approach under study, rather than on radiation versus no radiation.

The primary outcome was overall survival, defined as time from randomization to death from any cause or last known follow-up, with participants without a recorded death censored at their last known follow-up. Five-year rates were reported, while the registry also describes a log-rank comparison of survival time between the arms. The results therefore include both a time-specific estimate and a comparison using the event-time experience over follow-up.

The trial also reported outcomes relating to biochemical failure, local recurrence, distant metastasis, and other measures. These outcomes provide context about disease-related events but do not replace the primary overall-survival question. The registry record does not report the original statistical justification for the trial's enrollment target, its planned handling of multiple secondary tests, or details of missing-data procedures.

3. Trial Design

This was a randomized, parallel-arm phase III trial sponsored by the Radiation Therapy Oncology Group. The registry lists 1,538 enrolled participants and describes the study as completed. The two treatment groups were dose-escalated radiation therapy alone and dose-escalated radiation therapy combined with short-term androgen-deprivation therapy. Masking was listed as none, so the trial was open-label as recorded.

Both groups received a dose-escalated radiation approach. The radiation description allowed either 79.2 Gy external-beam radiation therapy alone or 45 Gy external-beam radiation therapy followed by low- or high-dose rate brachytherapy; external-beam radiation was delivered in 1.8 Gy daily fractions. In the combined-treatment arm, the registry describes six months of androgen-deprivation therapy starting 8 weeks before radiation. Listed drugs include bicalutamide, flutamide, and luteinizing-hormone releasing hormone agonist or antagonist therapy. Further regimen details are not reported in the registry record.

The primary outcome analysis included 750 participants in the radiation-alone arm and 742 in the combined-treatment arm. The record defines the primary population as eligible participants. The registry's enrollment count and these outcome denominators are different reported quantities; the record does not explain the difference. Allocation concealment, eligibility exclusions after enrollment, and a full account of analyzed participants by outcome are not reported in the registry record.

Follow-up for the primary outcome was defined from randomization to last follow-up. The listed schedule was at the end of radiation therapy for the second arm, then every 3 months for a year, every 4 months for 4 years, and yearly. Maximum follow-up at the time of analysis was 10.3 years, while the primary percentages reported were five-year rates. Analysis was planned to occur after 218 deaths were reported. Whether any interim analyses occurred is 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Eligible participants

5. Baseline Characteristics

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

Population: Eligible participants

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Alive (Overall Survival), measured over From randomization to last follow-up. Follow-up schedule: end of RT (2nd arm only), then every 3 months for a year, every 4 months for 4 years, then yearly. Maximum follow-up at time of analysis was 10.3 years. Five-year rates reported here..

The primary endpoint is the percentage of participants alive at five years, an overall-survival measure. Overall survival counts death from any cause as the event, rather than limiting events to prostate cancer deaths. The record defines survival time as the interval from randomization to death or last known follow-up; participants whose last known follow-up occurs without a recorded death are censored at that time.

The registry says the five-year rates were estimated with the Kaplan-Meier method. In general, this method uses the observed event and follow-up times to estimate the probability of remaining alive over time, while accounting for censoring. It is used because participants may have different lengths of observation and not everyone will have died by the analysis time. The five-year estimate gives a clinically interpretable time-specific summary, while the sponsor's log-rank analysis compares survival experience across the follow-up period.

Overall survival is used because it captures death from any cause and does not require deciding whether a death was caused by the cancer or a treatment. It is distinct from disease-specific outcomes such as biochemical failure, local recurrence, or distant metastasis. Those secondary outcomes can describe other aspects of disease course, but they do not answer the same question as overall survival.

The record reports five-year estimates of 90.0% with radiation alone and 91.0% with the addition of short-term androgen-deprivation therapy. The uncertainty intervals should be considered alongside those point estimates: they show a range of values compatible with the observed data under the estimation method, not a guarantee about an individual's outcome.

7. Results Posted in the Registry

• Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation: 91.0% (675/742) versus 90.0% (675/750) on control; risk difference 1.0 percentage points (95% CI -2.0 to 3.9), risk ratio 1.01 (0.98–1.04); unadjusted two-proportion z-test p = 0.523.

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.

Percentage of Participants With Biochemical Failure

• 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:
  • Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation: 7.7% (57/742) versus 13.9% (104/750) on control; risk difference -6.2 percentage points (95% CI -9.3 to -3.1), risk ratio 0.55 (0.41–0.75); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Local Recurrence

• 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:
  • Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation: 0.5% (4/742) versus 2.7% (20/750) on control; risk difference -2.1 percentage points (95% CI -3.4 to -0.9), risk ratio 0.20 (0.07–0.59); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Distant Metastasis

• 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:
  • Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation: 0.5% (4/742) versus 3.1% (23/750) on control; risk difference -2.5 percentage points (95% CI -3.9 to -1.2), risk ratio 0.18 (0.06–0.51); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Dose-Escalated Radiation Therapy and Short-Term Androgen-Deprivation than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover biochemical failure, local and regional recurrence, distant metastasis, prostate cancer-specific mortality, non-prostate cancer-specific mortality, receipt of salvage androgen-deprivation therapy, and overall survival by radiation modality. Eighteen secondary outcomes are posted, while the record lists 21 outcome measures. The details of the unposted outcomes are not reported in the registry record.

Among the secondary results with numerical data in the record, five-year biochemical failure, local recurrence, and distant metastasis percentages are lower in the arm that received short-term androgen-deprivation therapy. Their sponsor-reported log-rank analyses have hazard ratios of 0.52, 0.44, and 0.25 respectively, with confidence intervals that exclude 1 and p-values below 0.05. Gray's test p-values are also reported 0.05 for these outcomes. These results indicate a pattern in disease-related event measures distinct from the primary overall-survival comparison.

The secondary pattern does not establish an overall-survival difference. Disease-related events and death from any cause are different endpoints, with different event rates, follow-up information, and statistical uncertainty. A secondary outcome may show a detectable difference even when the primary endpoint does not; it does not change the primary endpoint's estimate or its uncertainty.

Unadjusted secondary p-values carry less weight when many outcomes or analyses are examined, because repeated testing increases the chance of finding at least one apparently significant result by chance. The registry lists 21 outcome measures and 37 analyses. Whether a multiplicity procedure was planned or applied is not reported in the registry record. The secondary findings are therefore best treated as supportive and interpreted cautiously, rather than as a set of independent confirmations or as a replacement for the primary analysis.

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

• Percentage of Participants With Biochemical Failure
• Percentage of Participants With Local Recurrence
• Percentage of Participants With Regional Recurrence
• Percentage of Participants With Distant Metastasis
• Percentage of Participants Dead Due to Prostate Cancer (Prostate Cancer-specific Mortality)
• Percentage of Participants Dead Due to Cause Other Than Prostate Cancer (Non-Prostate Cancer-specific Mortality)
• Percentage of Participants Receiving Salvage Androgen Deprivation Therapy (ADT)
• Percentage of Participants Alive (Overall Survival) by Radiation Therapy Modality

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary estimate represent?

The primary outcome is a time-to-event outcome: time from randomization until death from any cause, with last known follow-up used for participants without a recorded death. The five-year percentage alive is an estimate of survival at a specified time, not a simple count divided by the number enrolled. The registry states that the Kaplan-Meier method was used. In general, Kaplan-Meier estimation updates the estimated probability of remaining event-free at each observed event time and accounts for participants whose follow-up ends before an event is observed by censoring them at their last known follow-up.

Censoring does not mean that a participant is known to remain alive indefinitely. It means that an event was not recorded before the participant's observation ended. Standard interpretation of Kaplan-Meier estimates relies on assumptions about censoring, including that the reason follow-up ends does not systematically distort the remaining event experience after accounting for relevant information. The registry record does not describe censoring patterns or provide an assessment of this assumption.

How does the log-rank test differ from a five-year percentage comparison?

The sponsor's primary analysis used a log-rank method and reported a hazard ratio. In general, a log-rank test compares event-time distributions between groups, making use of the ordering of deaths and the time participants were observed. A fixed-time comparison instead contrasts survival estimates at a particular time, here five years. These approaches address related but not identical summaries of the data. The recalculated risk difference is an unadjusted comparison of the posted five-year percentages; it does not reproduce the log-rank analysis.

A hazard ratio is a relative comparison of event rates over time under the model or interpretation used for the analysis. The registry reports a hazard ratio of 0.85 with a 95% confidence interval from 0.65 to 1.11 for the primary comparison. The confidence interval includes 1, the value representing no relative difference in hazards. A hazard ratio is not itself a percentage alive, nor does it directly describe an absolute difference at five years. Interpreting it as a constant relative effect over time would require assumptions not assessed in the posted summary; proportional-hazards diagnostics are not reported in the registry record.

What do the confidence intervals and p-values convey?

A confidence interval describes statistical uncertainty around an estimate under the method used. In general, a 95% confidence interval is constructed so that, over repeated studies using the same procedure and assumptions, the intervals would cover the target quantity at the stated rate. It does not mean there is a 95% probability that the fixed underlying value lies inside this particular interval. The primary survival intervals quantify uncertainty in each arm's estimate. The interval for the recalculated risk difference quantifies uncertainty in the unadjusted contrast.

A p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions hold. 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 sponsor-reported primary p-value is 0.22. The recalculated unadjusted p-value is 0.523. They differ because they come from different statistical comparisons, not because one is a correction of the other.

Why can disease outcomes use competing-risk methods?

The record reports Gray's test for some secondary disease outcomes, alongside log-rank hazard ratios. In general, competing-risk methods are relevant when an event of interest can be precluded by another event, such as death before a recurrence is recorded. A method such as Gray's test compares cumulative incidence in the presence of competing events; it answers a different question from a standard analysis that treats competing events as ordinary censoring. The registry lists Gray's test p-values for biochemical failure, local recurrence, and distant metastasis, but does not fully describe the estimand, event coding, or analytic implementation.

What does over-dispersion mean in general?

Over-dispersion is a general issue in statistical models for counts or proportions when the observed variability is greater than the model assumes. If it is ignored, standard errors and confidence intervals can be too small, making results appear more precise than warranted. The posted primary endpoint is a Kaplan-Meier survival estimate and the sponsor's principal comparison is log-rank, so over-dispersion is not identified as a specific issue in the registry's primary analysis. The record does not report model diagnostics for the secondary endpoints.

The record says analysis was planned after 218 deaths were reported. It does not report whether interim analyses occurred, whether stopping boundaries were specified, or the detailed original statistical analysis plan. The listed secondary results include multiple outcomes and analyses; whether the testing strategy controlled the overall chance of false-positive findings is not reported in the registry record.

11. Confidence Intervals and Precision

The primary five-year survival estimate is 90.0% for radiation therapy alone, with a 95% confidence interval from 87.7% to 92.2%. For radiation therapy plus short-term androgen-deprivation therapy, it is 91.0%, with a 95% confidence interval from 88.8% to 93.1%. These intervals show that each arm's survival estimate has sampling uncertainty; they are not exact boundaries on the true value. The substantial overlap is consistent with the absence of a clear separation in the sponsor-reported primary comparison.

The sponsor's hazard ratio is 0.85, with a 95% confidence interval from 0.65 to 1.11. This interval includes 1, the null value for a hazard ratio, and the sponsor-reported p-value is 0.22. The unadjusted recalculated risk difference is 0.010, with a 95% confidence interval from -0.020 to 0.040. That interval includes zero, the null value for an absolute difference. The two intervals describe different effect measures and should not be compared as if they had the same scale.

Precision depends on the number of observed events, the amount and timing of follow-up, and the estimation method, not only on the number enrolled. The primary description gives maximum follow-up of 10.3 years, but reports five-year rates. The registry does not give the number of deaths observed in the final analysis or the arm-specific censoring pattern. It therefore does not permit a fuller assessment of how the event count and follow-up contributed to precision.

Confidence intervals describe uncertainty under the methods used; they do not establish that all values within an interval are equally plausible or clinically equivalent. The record does not specify a clinically meaningful survival difference against which to judge the interval. As a result, the statistical uncertainty can be described, but the practical importance of every value compatible with the interval cannot be determined from the registry record alone.

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 illustrations express sample sizes as participants per arm for binary outcomes such as the posted percentage endpoints. For time-to-event outcomes, the stated convention is total number of events, but the primary planning illustration is based on a binary percentage outcome. The figures use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They illustrate the sample size associated with detecting the stated fraction of the observed effect. The trial's own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column means the planned sample size would give an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the statistical model were correct. The 90% power column represents a higher planned chance of detecting that same specified effect, and therefore generally requires more participants. These are prospective planning probabilities, not probabilities that the trial's result is true.

Rows describing 100%, 75%, and 50% of the observed effect use progressively smaller effects as planning targets. Smaller effects are harder to distinguish from random variation and need more participants for the same target power. The illustrated counts are not the number enrolled in this trial and do not show whether its original design was adequate. In particular, they are not observed power: observed power is not a useful substitute for reading the estimates, confidence intervals, and analysis results.

Any curve accompanying these illustrations should be read as a planning aid that relates the effect targeted to the required sample size under the listed assumptions. It does not forecast the trial's outcome or supply a new result. Because the observed effect is used as the reference for these illustrations, the figures should not be mistaken for independent evidence about the treatment comparison.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.900; treatment proportion p₁ = 0.910; average p̄ = 0.905.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4150 = 0.8133.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4149 = 0.3492.
4. n = (0.8133 + 0.3492)² / (0.0097)² = 14,352.4, rounded up to 14,353 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
p0 <- 0.9                          # control proportion
p1 <- 0.909703504043127                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(936390)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 14,353 (80% power), 19,214 (90% power)
 75% of observed effect: n per arm = 25,807 (80% power), 34,548 (90% power)
 50% of observed effect: n per arm = 58,719 (80% power), 78,608 (90% power)
power.prop.test: 14352.4 
Simulated power at n = 14,353 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 sponsor's primary analysis is the registry's reported log-rank comparison of survival time. It gives a hazard ratio of 0.85, a 95% confidence interval from 0.65 to 1.11, and p = 0.22. This is the trial's posted inferential analysis for the primary endpoint and should be distinguished from the simple recalculation using the two five-year percentages.

The recalculated comparison gives an unadjusted risk difference of 0.010, a 95% confidence interval from -0.020 to 0.040, and p = 0.523. It treats the reported five-year percentages as a fixed-time contrast and does not use the full event-time information in the way the log-rank analysis does. Differences in the estimate scale and statistical method explain why its result is not numerically identical to the sponsor's hazard-ratio analysis.

Both analyses are compatible with uncertainty that includes no difference: the sponsor's hazard-ratio interval includes 1, and the unadjusted risk-difference interval includes zero. Their p-values also do not indicate a statistically clear primary difference. The recalculation is a transparent, unadjusted check of the posted summary rates, not a replacement for the sponsor's time-to-event analysis. The record does not report enough detail to independently reproduce the sponsor analysis from individual participant data.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 21 outcome measures and 37 analyses, including the primary endpoint and multiple secondary endpoints. Examining many outcomes can increase the overall chance of false-positive results if each test is judged separately at a conventional threshold. In general, multiplicity procedures can adjust interpretation or testing thresholds to account for a family of comparisons. Whether the trial specified or applied such a procedure is not reported in the registry record.

The record identifies overall survival as the primary outcome and states that the analysis was planned after 218 deaths were reported. It does not report a complete hierarchy of primary and secondary hypotheses, a prespecified family of tests, interim-analysis details, stopping rules, or a statistical analysis plan. The fact that an analysis was planned after a stated death count does not by itself establish whether interim looks occurred or how they were handled.

The primary population is described as eligible participants, and the outcome analysis lists 750 participants in one arm and 742 in the other. The registry does not explain exclusions, provide a detailed analysis-population definition, or state whether the primary analysis followed an intention-to-treat principle. The method used to handle missing outcome information beyond censoring at last known follow-up is not reported. The record also does not describe the amount or reasons for loss to follow-up by arm.

For overall survival, the stated use of Kaplan-Meier estimation implies that participants without an observed death are censored at their last known follow-up. In general, the validity of this approach depends on censoring not being informative in a way that biases the comparison. No censoring diagnostics or sensitivity analyses are reported. For secondary outcomes, the registry lists both log-rank and Gray's tests for some events, but does not fully describe competing-event definitions or missing-data handling.

These reporting gaps do not negate the posted results, but they limit assessment of how analyses were selected, how missing information may have affected estimates, and how strongly secondary findings should be interpreted. The record does not provide enough detail to resolve those questions.

16. 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: myocardial ischemia (0.7%), urinary retention (0.5%), diarrhea (0.4%), proctitis (0.4%), urinary frequency (0.4%).

The registry reports serious adverse events among 733 participants at risk in the radiation-alone group and 725 at risk in the combined-treatment group. It lists 20 participants with serious adverse events in the radiation-alone group and 33 in the combined-treatment group. Other adverse events are listed for 597 of 733 and 647 of 725 participants, respectively. The record also lists 119 deaths in the radiation-alone group and 100 in the combined-treatment group.

The most frequently listed serious-event terms include myocardial ischemia (0.7%), urinary retention (0.5%), diarrhea (0.4%), proctitis (0.4%), urinary frequency (0.4%), and rectal hemorrhage (0.3%). These terms and percentages describe the posted safety record; they do not establish that an event was caused by a treatment. The registry summary does not provide event timing, severity grades beyond the serious-event classification, duration, or participant-level details.

The safety denominators differ from the primary outcome arm sizes. The record does not explain the eligibility or observation rules used for the safety denominators, so those figures should be read as the counts and denominators reported for adverse events rather than assumed to match the primary analysis population. These summaries do not by themselves support a causal comparison or establish the balance of all harms and benefits.

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

The posted primary result is a comparison of five-year overall survival between two randomized treatment groups. The Kaplan-Meier estimates are 90.0% with radiation therapy alone and 91.0% with radiation therapy plus short-term androgen-deprivation therapy. The sponsor's log-rank comparison has a hazard ratio of 0.85, a 95% confidence interval from 0.65 to 1.11, and p = 0.22. The results do not provide clear statistical evidence of a difference in overall survival in the reported analysis.

This is not proof that the treatments are identical. The confidence interval allows a range of relative effects, including no difference, and the fixed-time risk-difference interval also spans zero. The registry record does not state what size of survival difference would be clinically important, so the results cannot be judged against a stated clinical threshold. A nonsignificant superiority test does not establish equivalence or noninferiority.

The secondary results indicate lower reported percentages for some disease-related outcomes in the combined-treatment arm, including biochemical failure, local recurrence, and distant metastasis. Those endpoints are not interchangeable with overall survival. Their analyses are secondary, and the registry record does not report whether multiple testing was addressed. Their p-values should therefore be interpreted with caution and should not be used to recast the primary result.

The findings apply to the treatment strategies and population described in this trial record: people with intermediate-risk prostate cancer receiving dose-escalated radiation, with or without the described short-term androgen-deprivation therapy. The record does not provide sufficient information to extend conclusions to other populations, treatment regimens, or clinical settings. It also does not fully report subgroup results, missing-data procedures, or long-term estimates beyond the stated five-year rates in the primary summary.

Overall, the posted data support a precise description of the observed estimates and their uncertainty, but not a definitive claim that adding therapy does or does not change survival. The primary analysis and secondary outcomes address different questions and should be read separately.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary endpoint is time-to-event overall survival, while the posted headline estimates are five-year survival percentages. A time-specific estimate and a log-rank comparison use related but distinct aspects of follow-up. The recalculated absolute contrast therefore need not match the sponsor's hazard-ratio analysis, and the two results should not be treated as competing calculations of exactly the same quantity.

The record also illustrates why point estimates alone are insufficient. The arm-specific five-year survival estimates are close, but interpretation depends on their confidence intervals and on the sponsor's time-to-event result. Both the hazard-ratio interval and the unadjusted risk-difference interval include their respective null values. The evidence is consequently better described in terms of estimates and uncertainty than as a binary declaration of success or failure.

Another statistical lesson is the separation between a primary endpoint and multiple secondary measures. Several disease-related outcomes have reported differences and small p-values, while the primary overall-survival analysis does not show a statistically clear difference. This pattern can arise because endpoints capture different events and have different statistical properties. It also makes transparent multiplicity reporting important: the registry lists many outcomes and analyses, but whether adjustment was used is not reported.

Finally, planning illustrations based on observed effects are not a substitute for the trial's original design assumptions. The registry reports a planned analysis after 218 deaths, but does not provide the original sample-size justification or a detailed analysis plan. Keeping design information, observed estimates, and post hoc planning illustrations distinct is essential to avoid overstating what the record establishes.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific details needed for a full appraisal are not reported in the registry record. Although the study is described as randomized, the record does not explain the sequence-generation or allocation-concealment procedures. Masking is listed as none. The available description does not give a complete account of adherence, treatment deviations, or the extent to which assigned treatments were received.

The treatment description includes alternative radiation approaches and lists several androgen-deprivation drugs, but the combined-arm description is incomplete. The full drug schedule and details of how treatment choices were made are not reported in the registry record. This limits evaluation of how uniform the treatment strategies were across participants and how precisely the findings map to a particular regimen.

The primary result reports five-year survival rates, with maximum follow-up at analysis of 10.3 years. The record does not supply the final death count, arm-specific follow-up distributions, censoring patterns, or detailed sensitivity analyses. It also does not report proportional-hazards diagnostics for the hazard-ratio analysis. These omissions make it difficult to assess the robustness of the time-to-event comparison from the posted summary alone.

The analysis population is described as eligible participants, but there is no full account of exclusions or a statement that the primary analysis followed an intention-to-treat approach. Missing-data procedures and loss-to-follow-up details are not reported. The record lists multiple outcomes and analyses but does not state whether multiplicity was addressed, and 3 of the 21 listed outcome measures are not among the 18 posted secondary outcomes.

Finally, the registry record does not report a clinically important threshold for overall survival or the original sample-size justification. These gaps constrain interpretation of clinical importance, precision, and the strength of secondary claims. They do not alter the numerical results, but they limit the conclusions that can be drawn from the record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Radiation Therapy With or Without Androgen-Deprivation Therapy in Treating Patients With Prostate Cancer — NCT00936390.
• Registry record last updated 2026-03-06; status last verified 2025-09.
• Results first posted 2022-10-06.
• 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

NCT00936390 is a completed randomized phase III parallel-arm trial sponsored by the Radiation Therapy Oncology Group. It enrolled 1,538 participants with intermediate-risk prostate cancer and compared dose-escalated radiation therapy alone with dose-escalated radiation therapy plus short-term androgen-deprivation therapy. Masking was listed as none.

The primary outcome was five-year overall survival estimated by Kaplan-Meier. The reported rates were 90.0% for radiation alone and 91.0% for the combined approach. The sponsor's log-rank analysis reported a hazard ratio of 0.85, a 95% confidence interval from 0.65 to 1.11, and p = 0.22. The unadjusted recalculation of the five-year percentages gave a risk difference of 0.010, with a 95% confidence interval from -0.020 to 0.040 and p = 0.523.

Some posted secondary disease-related outcomes were lower in the combined-treatment arm, but multiplicity procedures, missing-data details, and the original sample-size justification are not reported in the registry record. The primary result does not establish equivalence, and secondary results should be interpreted in light of their status and the multiple analyses.