Radiation Therapy With or Without Antiandrogen Therapy in Treating Patients With Stage I or Stage II Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Radiation Therapy With or Without Antiandrogen Therapy in Treating Patients With Stage I or Stage II Prostate Cancer (NCT00002597), a randomized phase 3 study. The primary outcome is Overall Survival Rate (10-year).

2. Clinical Question

The registry describes a randomized phase III trial of radiation therapy with or without antiandrogen therapy in patients with stage I or stage II prostate cancer. Its rationale states that androgens can stimulate prostate cancer cell growth and that hormone therapy may reduce androgen production. The trial compared radiation therapy alone with radiation therapy accompanied by total androgen suppression. The registry record does not provide further detail on eligibility criteria or the clinical characteristics of participants beyond the stated stage and prognosis descriptions.

The primary outcome was overall survival, assessed from randomization through 10 years. The registry defines this outcome as time from randomization to death from any cause and says that survival rates were estimated with the Kaplan–Meier method. Other outcomes addressed cancer-specific survival and different kinds of disease progression or failure. Those measures provide context about cancer outcomes but do not replace the primary question about survival from any cause.

3. Trial Design

This was a phase III, randomized, parallel-group trial with no masking. The registry lists the Radiation Therapy Oncology Group as sponsor and describes total enrollment as 2028. The record gives a start date of 1994-10, a primary completion date of 2011-07, and a completed status. These dates describe the registry record; further details about the conduct of follow-up are not reported in the registry record.

The treatment groups were neoadjuvant total androgen suppression plus radiation therapy and radiation therapy alone. In the combination group, the registry describes flutamide with Zoladex or Lupron beginning two months before radiation and continuing during it. The other group received radiation therapy alone. The record also lists the study interventions as flutamide, Zoladex, Lupron, and radiation therapy.

The primary outcome analysis included all eligible patients, according to the outcome description. The reported arm-level outcome counts are 987 for hormone therapy plus radiation therapy and 992 for radiation therapy alone. These outcome-specific counts should not be treated as a complete accounting of enrollment, randomization, or follow-up: a participant flow diagram and reasons for any differences are not reported in the registry record.

The record identifies nine outcome measures and nine analyses. It posts the primary 10-year overall survival result and eight secondary outcomes. The listed secondary outcomes concern disease-specific survival, local progression, distant failure, biochemical failure, clinical relapse, second biochemical relapse, disease-free survival, and positive re-biopsy at two years. Numerical results are posted for only three of those secondary outcomes in the record. Protocol details such as allocation concealment, stratification, adherence, crossover, and the original sample-size justification 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All eligible patients.

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: All eligible patients.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival Rate (10-year), measured over From date of randomization to 10 years.

The primary endpoint is the 10-year overall survival rate, expressed as a percentage. The registry defines overall survival as the time from randomization to death from any cause and specifies that survival rates were estimated using the Kaplan–Meier method. The outcome timeframe is from randomization to 10 years, and the population is all eligible patients.

Overall survival is a time-to-event outcome: the analysis uses the timing of deaths as well as whether deaths occurred. Participants who have not had the event by their last observed time may contribute information up to that time; the general statistical term for this is censoring. The registry does not report the details of censoring, follow-up completeness, or how participants lost to follow-up were handled.

As a general statistical point, overall survival is useful because it captures death from any cause rather than requiring investigators to attribute a death to the cancer or treatment. That broad definition also means the endpoint does not, by itself, identify the cause of any difference in survival. The 10-year rates give a fixed-time view of survival, while a time-to-event comparison can use the event timing over follow-up. The registry reports both arm-specific Kaplan–Meier estimates and a log-rank comparison.

7. Results Posted in the Registry

• Radiation Therapy Alone: 56.8% (563/992) versus 61.9% (611/987) on control; risk difference -5.2 percentage points (95% CI -9.5 to -0.8), risk ratio 0.92 (0.85–0.99); unadjusted two-proportion z-test p = 0.020.

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.

Disease-specific Survival Rate (10 Years)

• 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:
  • Radiation Therapy Alone: 92.6% (919/992) versus 95.7% (945/987) on control; risk difference -3.1 percentage points (95% CI -5.2 to -1.0), risk ratio 0.97 (0.95–0.99); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Radiation Therapy Alone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Local Progression Rate (10 Years)

• 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:
  • Radiation Therapy Alone: 16.1% (160/992) versus 10.9% (108/987) on control; risk difference 5.2 percentage points (95% CI 2.2 to 8.2), risk ratio 1.47 (1.17–1.85); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Radiation Therapy Alone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Distant Failure Rate (10 Years)

• 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:
  • Radiation Therapy Alone: 8.0% (79/992) versus 5.5% (54/987) on control; risk difference 2.5 percentage points (95% CI 0.3 to 4.7), risk ratio 1.46 (1.04–2.03); unadjusted two-proportion z-test p = 0.027.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Radiation Therapy Alone than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes span cancer-specific survival, progression, distant failure, biochemical and clinical relapse, disease-free survival, and re-biopsy findings. Numerical results in the registry record cover disease-specific survival, local progression, and distant failure. Across those reported outcomes, the observed pattern generally points in the same direction as the primary result: the combination group has higher disease-specific survival estimates and lower progression or failure estimates than the radiation-alone group. These outcomes add disease-control context to the overall-survival comparison, but they are not substitutes for it.

Secondary endpoints can help describe how outcomes differ beyond death from any cause. Their definitions, time origins, and statistical methods vary, however, and the registry does not report full endpoint definitions or analysis details for every listed measure. The registry reports Gray's test analyses for the three numerically posted secondary outcomes. Their estimates and tests should be interpreted according to the outcome and method used, rather than combined into a single overall measure of benefit.

There are multiple listed outcomes and analyses. If each is examined as a separate hypothesis test, the chance of at least one apparently notable result can increase. This is a general statistical concern, not a claim that the reported findings are false. The registry record does not report whether secondary analyses were prespecified in a hierarchy, adjusted for multiplicity, or treated as exploratory. Consequently, unadjusted secondary results carry less inferential weight than a clearly specified primary endpoint analyzed under a prespecified plan.

The registry lists additional secondary outcomes but does not post numerical results for all of them in the record considered. Their absence should not be interpreted as evidence of no difference; their results and reasons for not being posted are not reported in the registry record.

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

• Disease-specific Survival Rate (10 Years)
• Local Progression Rate (10 Years)
• Distant Failure Rate (10 Years)
• Biochemical Failure Rate (10 Years)
• Clinical Relapse Rate (10 Years)
• Second Biochemical Relapse Rate (10 Years)
• Disease-free Survival Rate (10 Years)
• Positive Re-biopsy Rate at Two Years

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time to death from any cause, measured from randomization. The registry says that the 10-year survival rates were estimated with the Kaplan–Meier method. The sponsor's reported comparison used a log-rank test and presented a hazard ratio, confidence interval, and p-value. These methods address follow-up time rather than treating every participant as if observation ended at the same moment.

What does Kaplan–Meier estimation do?

As a general statistical explanation, Kaplan–Meier estimation builds an estimate of the probability of remaining event-free over time. It uses event times and accounts for participants whose observation ends before an event is recorded by including their observed time up to the point they are censored. This approach relies on assumptions about censoring, including that censoring does not systematically conceal a participant's subsequent event risk in a way that invalidates the estimate. Whether those assumptions were assessed, and how much follow-up was available at each time, are not reported in the registry record.

The resulting 10-year rate is a time-specific survival estimate. It is not necessarily the raw number alive at 10 years divided by the number initially assigned to that group. The record reports arm-specific estimates and their 95% confidence intervals, but does not report numbers at risk at each follow-up time or the detailed estimation output.

What does the log-rank comparison test?

As a general explanation, the log-rank test compares observed event timing between groups over the follow-up period. It is not limited to the 10-year endpoint and does not directly test a difference between two isolated percentages. The registry reports a log-rank method for the primary comparison. Its hazard ratio describes a relative comparison of event rates over time under the analysis framework; it should not be read as a percentage-point difference in 10-year survival.

The registry labels the reported analysis as superiority and gives a hazard ratio of 1.17, a 95% confidence interval from 1.01 to 1.35, and a p-value of 0.031. The listed group order is hormone therapy plus radiation therapy followed by radiation therapy alone. The record does not state the ratio's reference coding or report a fuller model specification. Therefore the arm-specific Kaplan–Meier estimates are important for understanding the direction of the observed absolute rates, while the reported analysis is the formal time-to-event comparison.

How should the recalculations be understood?

As a general statistical point, a simple unadjusted recalculation from posted event counts treats the data as a comparison of summary proportions. It does not incorporate event timing, censoring, or the Kaplan–Meier estimator. The posted results also include risk differences, risk ratios, odds ratios, and unadjusted p-values calculated from the summary counts. These can serve as descriptive cross-checks, but they answer a different and simpler question than the sponsor's time-to-event analysis. The registry does not flag a discrepancy between its analysis and the recalculation.

For the secondary outcomes, the registry reports Gray's test and hazard-ratio summaries for disease-specific survival, local progression, and distant failure. In general, Gray's test is used to compare cumulative incidence when competing events matter. A competing event is one that can prevent the event of interest from occurring or being observed in the same way. This distinction is relevant to outcomes such as disease-specific death, where death from another cause can preclude the event being studied. The record does not provide enough methodological detail to determine the specific competing-event definitions or modeling choices.

Confidence intervals describe a range of values compatible with the data under the method and assumptions used. A 95% confidence interval is not a statement that there is a 95% probability that the fixed true value lies inside this particular calculated interval. In repeated use of a method under its assumptions, intervals constructed in this way would cover the true value at the stated rate. The width reflects statistical precision, while validity also depends on design, measurement, missingness, and modeling assumptions.

Significance tests and confidence intervals are related but not interchangeable summaries. A p-value assesses how compatible the data are with a specified null hypothesis under a statistical model. It does not measure the size or clinical importance of an effect, and it does not give the probability that the null hypothesis is true. Estimates and intervals are therefore needed to describe magnitude and precision. The registry does not report the full statistical analysis plan, model diagnostics, or any interim-monitoring procedures.

11. Confidence Intervals and Precision

The 10-year overall survival estimate is 61.9% in the hormone-therapy-plus-radiation group, with a 95% confidence interval from 58.3% to 65.3%. In the radiation-alone group, the estimate is 56.8%, with a 95% confidence interval from 53.2% to 60.2%. Each interval conveys uncertainty around its group estimate; neither is a guarantee that the true value falls within the displayed endpoints.

The intervals have some overlap, so the arm-level estimates alone do not give a simple visual test of the between-group comparison. The sponsor's time-to-event analysis uses the full event-time information and reports a hazard ratio of 1.17, with a 95% confidence interval from 1.01 to 1.35. The registry labels that analysis as superiority. These summaries target different quantities: one gives survival estimates at 10 years, and the other compares event rates over follow-up.

Precision is not the same as validity. A confidence interval can be calculated precisely while still being affected by incomplete follow-up, measurement problems, or assumptions that do not hold. The registry record does not report follow-up completeness, numbers at risk over time, censoring patterns, or detailed missing-data handling. Those omissions limit assessment of how representative the stated precision is of all randomized participants.

Confidence intervals for the secondary outcomes also indicate uncertainty, and should be interpreted in light of the number of outcomes examined. A nominal interval or test for an individual outcome does not account for the possibility of many comparisons unless an adjustment is specified. Whether such adjustments were planned or used is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial's original sample-size justification. For the binary percentage outcomes, the figures are participants per arm. For time-to-event outcomes, the figures are total events, as specified in the planning assumptions. The displayed calculations use 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 80% power column gives the planned number of participants per arm, or total events for time-to-event outcomes, under which a study would have an 80% chance of detecting the assumed effect at the stated significance level if the assumptions held. The 90% power column makes the analogous illustration for a 90% chance. These are design-planning concepts, not guarantees that a study will reach a particular conclusion.

Rows that use 100% of the observed effect assume the full observed effect as the target for planning. Rows using 75% or 50% use smaller target effects. Smaller effects are harder to detect, so the planning figures require more participants or events. For example, the primary time-to-event planning figures are 1,427 total events for 80% power and 1,910 total events for 90% power when using 100% of the observed effect; the corresponding figures are 2,524 and 3,379 when using 75%, and 5,650 and 7,562 when using 50%.

These figures are not observed power. They are illustrations calculated from the posted effect and stated planning assumptions, and they do not establish what assumptions the investigators used when designing the trial. The original protocol's sample-size assumptions and justification are not reported in the registry record.

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 = 0.619; treatment proportion p₁ = 0.568; average p̄ = 0.593.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6947 = 1.3616.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6937 = 0.5839.
4. n = (1.3616 + 0.5839)² / (-0.0515)² = 1,426.6, rounded up to 1,427 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 <- 0.619047619047619                          # control proportion
p1 <- 0.567540322580645                          # 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(2597)
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 = 1,427 (80% power), 1,910 (90% power)
 75% of observed effect: n per arm = 2,524 (80% power), 3,379 (90% power)
 50% of observed effect: n per arm = 5,650 (80% power), 7,562 (90% power)
power.prop.test: 1426.6 
Simulated power at n = 1,427 per arm: 0.800 (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-reported primary analysis is a log-rank comparison, with a hazard ratio of 1.17 and a 95% confidence interval from 1.01 to 1.35. The registry labels the analysis as superiority and reports a p-value of 0.031. That time-to-event analysis should be distinguished from the unadjusted recalculation based on posted outcome counts. The recalculation uses summary proportions and does not reproduce the event-time analysis.

The arm-specific survival estimates give the absolute 10-year context: 61.9% for hormone therapy plus radiation therapy and 56.8% for radiation therapy alone. The registry does not flag a discrepancy between the sponsor's reported analysis and the recalculation. The sponsor's result therefore remains the appropriate record of the trial's stated time-to-event analysis; the recalculated summary is supplementary and answers a different statistical question.

The record does not provide the full analysis plan, detailed ratio coding, censoring rules, or model diagnostics. Those omissions mean that the sponsor's summary can be described as reported, but its technical choices cannot be independently reconstructed from the registry record alone. This distinction is especially important because a hazard ratio and a difference in fixed-time survival percentages are not interchangeable measures.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists nine outcome measures and nine analyses, including the primary overall-survival outcome and several secondary outcomes. It does not report whether the investigators used a formal strategy to control multiplicity, such as adjustment for multiple comparisons, a hierarchy of endpoints, or a distinction between confirmatory and exploratory tests. Without that information, the reported secondary p-values should be viewed as individual, unadjusted results rather than as evidence controlled across all outcome analyses.

The primary outcome population is described as all eligible patients. The registry record does not provide a detailed accounting of eligibility exclusions, randomized participants by arm, or the analysis population for each outcome. It also does not state whether the main analysis followed an intention-to-treat principle or how protocol deviations and treatment discontinuations were handled.

Missing outcome data, loss to follow-up, and censoring details are not reported in the registry record. For time-to-event endpoints, censoring is expected as a statistical feature when observation ends before an event, but the record does not describe its extent, timing, or handling. For the non-primary outcomes, the record does not state how participants with incomplete assessments were treated. These gaps limit assessment of whether missingness could affect the estimates.

The registry does not report interim analyses, stopping rules, data-monitoring procedures, or the original statistical analysis plan. It is therefore not possible to determine from this record whether the final analyses followed a prespecified sequence or whether any adjustments were made during the trial. These are reporting limitations; they do not establish that the procedures were absent from the trial itself.

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: late rt toxicity: bladder: nos (1.2%), late rt toxicity: hematologic: nos (0.8%), acute rt toxicity: hematologic: nos (0.7%), acute rt toxicity: bladder: nos (0.4%), late rt toxicity: bowel: nos (0.3%).

The registry reports serious adverse events affecting 33 of 1003 participants in the group described as receiving neoadjuvant total androgen suppression before and during radiation therapy, and 16 of 1003 in the radiation-alone group. It also reports other adverse events affecting 975 of 1003 and 955 of 1003, respectively. These are counts as posted; the record does not explain whether participants could contribute to more than one event category or how events were counted.

The most frequent serious-event terms listed include late radiation toxicity involving the bladder at 1.2%, late hematologic toxicity at 0.8%, and acute hematologic toxicity at 0.7%. Other listed terms include acute bladder toxicity at 0.4%, late bowel toxicity at 0.3%, and late toxicity in other categories at 0.3%. These entries describe the reported terms and percentages, not a complete safety profile.

Deaths in the adverse-event groups are not reported in the registry record. Definitions, severity grading, observation periods, attribution methods, and missing safety data are also not reported. These adverse-event counts should therefore be read as registry summaries, not as a complete basis for comparing safety or drawing clinical conclusions.

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

The posted results describe a randomized comparison of total androgen suppression with radiation therapy versus radiation therapy alone. The primary outcome estimates show 10-year overall survival of 61.9% in the combination group and 56.8% in the radiation-alone group. The sponsor-reported time-to-event analysis is labelled as a superiority analysis and reports a hazard ratio of 1.17 with a 95% confidence interval from 1.01 to 1.35.

These results describe the participants and analyses recorded in this trial. They do not specify the outcome for an individual patient, and the 10-year estimates do not reveal why deaths occurred. The hazard ratio is a relative time-to-event measure, not a direct estimate of how many more participants survive to 10 years. The registry record also does not provide enough information to assess all assumptions underlying follow-up and analysis.

The secondary outcomes suggest a broadly similar direction for the posted disease-specific and progression results, but multiple outcomes were examined and multiplicity handling is not reported. Those results therefore provide supporting context rather than a replacement for the primary endpoint. Safety summaries are also incomplete in the registry record and should not be treated as a comprehensive assessment.

The results do not, by themselves, establish how the findings apply to people outside the recorded eligibility and treatment context. Details about participant characteristics, treatment adherence, subsequent care, and follow-up completeness are not reported in the registry record. Nor do the registry results alone determine whether either regimen is appropriate for a particular person. The statistical findings describe a group comparison, with uncertainty, rather than offering medical advice.

18. Why This Trial Matters Statistically

This trial is statistically notable for pairing a fixed-time survival estimate with a time-to-event comparison. The 10-year Kaplan–Meier percentages are readily interpretable as survival estimates at a specified time, while the log-rank analysis uses event timing across follow-up. Those summaries answer related but distinct questions, so reading them together is more informative than treating one as a substitute for the other.

The record also illustrates why the analysis method matters. A simple recalculation from posted counts does not retain event timing or account for censoring in the same way as a survival analysis. It can provide a descriptive comparison, but it cannot independently reproduce the sponsor's log-rank result. The registry does not flag a discrepancy, yet the methods remain distinct.

The trial's secondary outcomes broaden the view from overall survival to cancer-specific outcomes and disease progression. At the same time, multiple endpoints raise questions about multiplicity and the strength of inference, especially when the registry record does not describe an adjustment plan or endpoint hierarchy. That is a useful reminder to distinguish the prespecified primary question from supportive or exploratory findings.

Finally, the registry record makes clear that reported estimates are only part of an appraisal. Confidence intervals communicate statistical precision, while missing information about participant flow, follow-up, censoring, missing data, and analysis plans limits how fully the results can be evaluated. Statistical interpretation depends both on the numerical estimates and on the design and reporting details available to assess them.

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 to assess the results are not reported in the registry record. These include participant characteristics beyond the broad stage and prognosis description, detailed eligibility rules, baseline comparability, allocation concealment, and any stratification factors. The record identifies randomization but does not explain how the allocation sequence was generated or implemented.

The primary outcome is defined and its estimator is named, but the record does not give numbers at risk over time, follow-up completeness, censoring patterns, or detailed handling of missing outcomes. It also does not provide enough information to reconstruct the reported hazard ratio's reference coding or full model specification. These omissions constrain independent evaluation of the time-to-event analysis.

Outcome-specific counts are not a substitute for a participant flow account. The registry does not report the reasons that outcome counts differ from total enrollment, nor does it describe treatment adherence, crossover, discontinuation, or subsequent therapies. Without those details, the relationship between assigned and received treatment cannot be fully evaluated.

The registry lists multiple secondary outcomes but does not report a multiplicity strategy, full results for every listed outcome, or the original analysis plan. The original sample-size justification, interim analyses, and stopping procedures are also not reported in the registry record. Safety summaries lack event definitions, attribution, observation details, and death counts. These are reporting limitations of the record and do not establish that such information was not collected during the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Radiation Therapy With or Without Antiandrogen Therapy in Treating Patients With Stage I or Stage II Prostate Cancer — NCT00002597.
• Registry record last updated 2018-06-14; status last verified 2018-05.
• Results first posted 2017-06-06.
• 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

The registry record describes a completed, randomized, parallel-group phase III trial with no masking, sponsored by the Radiation Therapy Oncology Group. Total enrollment was 2028. The trial compared total androgen suppression with radiation therapy against radiation therapy alone in stage I or stage II prostate cancer.

The primary outcome was 10-year overall survival from randomization, estimated with the Kaplan–Meier method. The posted estimates were 61.9% for hormone therapy plus radiation therapy and 56.8% for radiation therapy alone. The sponsor-reported log-rank analysis gave a hazard ratio of 1.17 with a 95% confidence interval from 1.01 to 1.35.

Numerical secondary results were posted for disease-specific survival, local progression, and distant failure. The registry also lists safety-event counts and selected serious adverse-event terms. Details about multiplicity, missing data, participant flow, and several analysis procedures are not reported in the registry record.