Intensity-Modulated Radiation Therapy With or Without Decreased Radiation Dose to Erectile Tissue in Treating Patients With Stage II Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Intensity-Modulated Radiation Therapy With or Without Decreased Radiation Dose to Erectile Tissue in Treating Patients With Stage II Prostate Cancer (NCT00084552), a randomized na study. The primary outcome is Erectile Dysfunction Rates.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, single-masked, parallel-group trial, with enrollment of 116. Its phase field is listed as NA, while the brief purpose describes the study as a randomized phase III trial. These are two different descriptions in the record; the phase field itself does not specify a phase. Fox Chase Cancer Center is listed as the sponsor, and the trial status is completed.

Participants were assigned to s-IMRT or ETS-IMRT. Both arms used intensity-modulated radiotherapy once daily, five days a week, for approximately 7.5 weeks. The ETS-IMRT description specifies dose restriction to erectile tissue; the s-IMRT description specifies conventional intensity-modulated radiotherapy. The registry record does not report the masking procedure or identify which individuals were masked.

The primary outcome was erectile dysfunction rates, with a stated timeframe of five years after completion of radiotherapy. The record describes two assessment approaches: the postage stamp test for nocturnal erections and the International Index of Erectile Function questionnaire. The questionnaire is described as a 15-item measure of erectile function and includes a companion questionnaire about the partner's view of changes in the sexual relationship since the patient's cancer diagnosis and therapy.

The registry record lists freedom from biochemical failure, acute GI toxicity, and acute GU toxicity as secondary outcomes. It does not report the trial's original sample-size justification, detailed randomization procedures, or a protocol for outcome analyses. Although overall enrollment is recorded as 116, the number contributing to an outcome varies in the posted results. The record notes that some patients did not submit follow-up questionnaires at 24 months post-treatment; it does not state how missing questionnaires were handled in the primary analysis.

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

Analysis population for the primary outcome, as defined in the registry: Some patients did not submit follow-up questionnaires at 24 months post-treatment

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 Erectile Dysfunction Rates, measured over 5 year duration after completion of radiotherapy.

The primary endpoint is titled erectile dysfunction rates and is reported as a count of participants. Its timeframe is five years after completion of radiotherapy. The registry description identifies two ways the study assessed erectile function. In the postage stamp test, a row of stamps is placed around the base of the penis, with the ends moistened and joined; a broken circle in the morning was recorded as evidence of a nocturnal erection. The International Index of Erectile Function is described as a 15-item questionnaire measuring erectile function. A companion questionnaire asks the partner how the sexual relationship changed after the patient's cancer diagnosis and therapy.

Using more than one assessment approach can capture different aspects of sexual function: one is an observation related to nocturnal erection, while the other is a questionnaire measure. That is a general measurement distinction, not evidence that either approach is more accurate in this trial. The registry record does not specify the threshold or decision rule used to classify a participant as having erectile dysfunction, nor does it explain how results from the test and questionnaire were combined. Those details matter when interpreting a participant count because the count depends on the endpoint definition and the available assessments.

The record also notes that some patients did not submit follow-up questionnaires at 24 months post-treatment. It does not describe whether the primary endpoint used the questionnaire, the postage stamp test, both, or another rule when information was incomplete. The posted count should therefore be read as the registry's reported primary outcome, without assuming an unreported classification or missing-data procedure.

7. Results Posted in the Registry

• ETS-IMRT: 75.0% (36/48) versus 73.0% (27/37) on control; risk difference 2.0 percentage points (95% CI -16.8 to 20.9), risk ratio 1.03 (0.80–1.33); unadjusted two-proportion z-test p = 0.832.

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 Patients With Freedom From 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:
  • ETS-IMRT: 91.9% (57/62) versus 90.7% (49/54) on control; risk difference 1.2 percentage points (95% CI -9.1 to 11.5), risk ratio 1.01 (0.91–1.13); unadjusted two-proportion z-test p = 0.819.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ETS-IMRT and the control. The interval gives the range of effects that remain compatible with the data.

Acute GI Toxicity

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ETS-IMRT: 9.7% (6/62) versus 1.9% (1/54) on control; risk difference 7.8 percentage points (95% CI -0.4 to 16.0), risk ratio 5.23 (0.65–42.05); unadjusted two-proportion z-test p = 0.077.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ETS-IMRT and the control. The interval gives the range of effects that remain compatible with the data.

Acute GU Toxicity

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • ETS-IMRT: 43.5% (27/62) versus 37.0% (20/54) on control; risk difference 6.5 percentage points (95% CI -11.3 to 24.3), risk ratio 1.18 (0.75–1.84); unadjusted two-proportion z-test p = 0.476.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ETS-IMRT and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover distinct domains: freedom from biochemical failure, acute GI toxicity, and acute GU toxicity. Taken together, they broaden the clinical questions recorded beyond erectile function, but they do not measure the same construct as the primary endpoint. The overall pattern in the posted comparisons is that estimates are uncertain, and the registry record does not report sponsor analyses for these outcomes. Their role is contextual rather than a substitute for the primary comparison.

Secondary outcomes can help describe a trial's broader result profile, but they generally carry less confirmatory weight when they are not the primary question. Multiple outcomes create more opportunities for an apparently notable result to arise by chance. The posted secondary p-values are unadjusted, and the registry record does not report a multiplicity strategy. That means they should not be treated as if they were protected by a prespecified family-wise testing plan.

The secondary results also differ in their stated timeframes and reporting scales. A percentage outcome at two years after treatment and toxicity counts with a five-year-after-treatment timeframe cannot be read as interchangeable evidence. Their denominators and endpoint definitions should be considered separately. General statistical caution applies when comparing several outcomes: a pattern across measures can motivate further questions, but does not establish a single overall treatment effect.

The primary result remains the direct evidence for the trial's stated main question about erectile dysfunction rates. Secondary findings may add context, but they do not resolve the primary interval's uncertainty, establish a mechanism, or prove that an observed difference in one domain carries over to another. Because the analysis plan and multiplicity handling are not reported, the secondary results are best viewed as descriptive and hypothesis-generating rather than definitive claims.

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

• Percentage of Patients With Freedom From Biochemical Failure
• Acute GI Toxicity
• Acute GU Toxicity

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help describe the observed group comparison, quantify its uncertainty, and distinguish what the data can support from what remains unknown. The posted results use participant counts for the primary endpoint and risk differences for the comparisons. The registry record does not report the sponsor's analysis plan, so the calculations described by the posted comparisons should not be mistaken for a confirmed description of the trial's original statistical methods.

What does a risk difference describe?

A risk difference compares the proportion with an outcome in one group with the proportion in another group. A value above zero indicates a larger observed risk in the first group under the comparison's coding; a value below zero indicates a smaller observed risk. A value of zero represents no difference in the compared risks. For the primary comparison, the estimate is 0.020, with ETS-IMRT compared against s-IMRT. Because erectile dysfunction is the outcome, the direction refers to the outcome as recorded, not to a judgment about the overall value of either treatment.

A risk difference is an absolute measure: it describes the separation between group risks rather than a ratio. That can make it useful for understanding the size and direction of a comparison. It remains an estimate based on the observations available for the endpoint, not a guaranteed effect in other participants or settings. The registry record does not report an adjusted primary estimate or a sponsor-reported hypothesis test for this endpoint.

What does the interval add?

A confidence interval expresses uncertainty around an estimate using a range of values compatible with the data under the calculation's assumptions. It is more informative than a point estimate alone because it shows whether the estimated effect is tightly or loosely determined. For the primary comparison, the interval runs from -0.168 to 0.209. Since the interval crosses zero, it includes no difference as well as differences in either direction. Its width indicates that the data are compatible with a broad range of effects. A confidence interval is not a guarantee that the true value lies inside its endpoints, and it does not by itself establish clinical importance.

For binary outcomes, uncertainty depends in part on how many participants contribute and how often the outcome is observed. When event counts are limited, estimates can be unstable and intervals can be wide. This is a general statistical point, not a separate finding about the validity of any individual participant's outcome. The primary outcome has endpoint-specific counts of 27 among 37 and 36 among 48, and the record notes that some follow-up questionnaires were not submitted at 24 months. The registry record does not explain the relationship between missing questionnaires and the primary endpoint's analysis denominator.

How should the p-value be read?

The primary unadjusted p-value is 0.832. A p-value is a measure of how unusual data at least as discrepant as those observed would be under a specified null model and the calculation's assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of the probability that the finding occurred by chance. A large p-value does not prove that the groups are equal. It can arise when the underlying difference is small, when data are imprecise, or both. The interval helps make that uncertainty visible, whereas the p-value compresses the comparison into a single measure.

“Unadjusted” means that the reported p-value has not been adjusted for the consideration of multiple outcomes or comparisons. The registry record lists several outcomes, and no multiplicity adjustment is reported. The p-value should therefore be read as a result for its particular comparison, not as a corrected statement about the family of trial outcomes. The record also lists no reported analyses for the posted secondary outcomes.

Why does outcome definition matter?

The primary outcome is named erectile dysfunction rates, but its description gives information about a postage stamp test and the International Index of Erectile Function questionnaire without setting out a classification threshold. A statistical comparison is only as interpretable as the endpoint being compared. If the registry record does not say how measures were combined, how questionnaire responses were scored into the reported count, or how missing responses were handled, those methodological details remain unknown. The analysis should not be reconstructed by guessing a rule that is absent from the record.

The posted secondary outcomes also have different measurement forms and timeframes. Freedom from biochemical failure is reported as a percentage of participants at two years after treatment, while acute GI and acute GU toxicity are reported as participant counts with a five-year-after-treatment timeframe. The interpretation of a count, a percentage, and a risk difference depends on the outcome definition and denominator. No pooled or combined outcome should be inferred across these measures.

What can the posted calculations establish?

The comparisons provide descriptive estimates, intervals, and unadjusted p-values for the outcomes. They do not reveal whether the original investigators used the same calculations, adjusted for baseline factors, or followed a prespecified analysis plan. The registry record does not report those details. It also does not report an interim analysis plan, the original sample-size justification, or analysis-population rules. These omissions do not invalidate the posted numbers, but they limit what can be said about the trial's full inferential framework. Statistical interpretation should therefore distinguish the observed posted comparisons from unreported design and analysis decisions.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an estimate. The primary risk-difference estimate is 0.020, and its interval runs from -0.168 to 0.209. The interval spans zero and values on either side, so the observed data do not pin down whether the difference favors s-IMRT or ETS-IMRT. The estimate is only one point within a much wider range of values compatible with the calculation.

The interval's width matters alongside the p-value. A p-value of 0.832 does not show that the true difference is exactly zero; the interval shows that a range of positive and negative differences remains compatible with the data. Conversely, the interval does not establish that every value within it is equally likely or clinically important. The registry record does not supply a threshold for a clinically meaningful difference, so the interval cannot be classified as excluding or including such a threshold.

Participant counts available for an endpoint affect precision, and the primary comparison uses 37 participants in s-IMRT and 48 in ETS-IMRT. Overall enrollment was 116, but the primary comparison has different endpoint-specific group counts. The record notes incomplete follow-up questionnaires at 24 months and does not describe their handling in this analysis. Those details make it important to distinguish enrollment from the outcome-specific data used in the comparison.

Confidence intervals are generally preferable to a significance label alone because they convey both direction and uncertainty. Here, the interval does not offer a narrowly defined effect estimate. The result should be read as inconclusive about the direction and size of a group difference, rather than as evidence that the approaches are equivalent or that a meaningful difference is absent.

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 sample-size figures are planning illustrations based on the observed effect, not the trial's original design justification. For these posted binary outcomes, the figures are participants per arm. The general calculation assumptions stated for the illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each planning row is the stated fraction of the observed effect. Time-to-event tables use total events under the stated Schoenfeld approach, but the posted outcomes are binary, so the displayed planning figures are per-arm participant counts.

The 80% power column gives the planned number of participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column describes a higher target chance of detection under the same planning framework. Power is a design property calculated before a study, not a probability that a particular observed result is correct. These figures do not report the power achieved by this trial; they are not observed power.

Rows that plan for 100% of the observed effect use the observed estimate as the target effect. Rows planning for 75% or 50% use smaller target effects. A smaller effect is harder to distinguish from random variation, so it requires more participants per arm under the stated assumptions. The planning numbers can therefore rise substantially as the target effect is reduced.

The figures should be treated as conditional illustrations rather than a recommendation or a reconstruction of the trial's intended enrollment. The registry record does not report the trial's own sample-size assumptions or justification. In particular, the calculations do not account for unreported choices about the primary endpoint definition, missing follow-up data, adjustment for other outcomes, or other design features. Readers can use the rows to understand how planning needs depend on a target effect, while keeping those limitations in mind.

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 = 0.730; treatment proportion p₁ = 0.750; average p̄ = 0.740.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6204 = 1.2160.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6203 = 0.5220.
4. n = (1.2160 + 0.5220)² / (0.0203)² = 7,351.9, rounded up to 7,352 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 <- 0.72972972972973                          # control proportion
p1 <- 0.75                          # 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(84552)
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 = 7,352 (80% power), 9,842 (90% power)
 75% of observed effect: n per arm = 13,154 (80% power), 17,608 (90% power)
 50% of observed effect: n per arm = 29,779 (80% power), 39,865 (90% power)
power.prop.test: 7351.9 
Simulated power at n = 7,352 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes or comparisons. Even when each individual test uses a conventional threshold, the chance of at least one apparently unusual result can increase across a group of tests. The registry record lists one primary outcome and three secondary outcomes, and the primary assessment description includes more than one measurement instrument. It does not report whether the instruments generated separate analyses, how they were combined, or whether repeated assessments were tested separately.

The posted p-values are unadjusted. The registry record does not report a plan for controlling multiplicity, such as a hierarchy of hypotheses or an adjustment across outcomes. This absence does not change the numerical estimates, but it affects how much confirmatory weight should be placed on isolated secondary findings. The primary outcome should remain the central comparison, while unadjusted secondary results warrant caution.

Missing data are also relevant. The record states that some patients did not submit follow-up questionnaires at 24 months post-treatment. It does not state how many questionnaires were missing, why they were missing, whether missingness differed by group, or what method was used to handle it. The record therefore does not establish whether the primary outcome analysis used imputation, complete cases, another approach, or a combination of assessments. No assumption about the direction of any resulting bias can be made from the registry record.

The outcome-specific denominators reinforce the need to distinguish enrollment from analysis populations. For the primary comparison, the posted group counts are 37 and 48; other outcomes use different group counts. Those differences may reflect outcome availability or other analysis choices, but their explanation is not reported in the registry record. The record does not identify an intention-to-treat population, a per-protocol population, or another formal analysis population.

These omissions limit assessment of robustness and of the intended inferential framework. The original sample-size justification, interim analysis plans, and detailed statistical analysis plan are not reported in the registry record. They should not be inferred from the posted p-values, intervals, or planning illustrations.

15. 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 0% reporting threshold.

The serious adverse event figures report zero affected participants in s-IMRT among 54 at risk and zero in ETS-IMRT among 62 at risk. The death count is zero in each group, and no top serious adverse event terms are listed. These are the registry's reported figures for the stated safety fields.

Zero reported serious events in these groups means that the registry record lists no serious events for the recorded observation, not that the possibility of serious harm is ruled out. A safety comparison depends on the event definitions, observation period, completeness of reporting, and the number of participants monitored. The registry record does not provide detailed serious-event definitions or further event descriptions. The reported safety counts should be interpreted as a record of what was posted, not as proof of absence of risk.

The serious-event denominators differ from the primary outcome denominators. They should not be combined or treated as the analysis population for erectile dysfunction. Nor do the serious-event fields summarize every possible toxicity: acute GI and acute GU toxicity are listed separately as secondary outcomes. Serious adverse events and those other toxicity measures are distinct types of reporting.

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

The posted primary comparison estimates a risk difference of 0.020 for ETS-IMRT relative to s-IMRT, with an interval from -0.168 to 0.209 and an unadjusted p-value of 0.832. The estimate is compatible with differences in either direction, and its interval includes no difference. The central statistical message is uncertainty: the posted data do not locate a narrow effect range or establish which approach has the lower erectile dysfunction rate.

That conclusion is not the same as saying the groups are equivalent. Equivalence requires a prespecified margin defining differences small enough to count as practically equivalent, together with an analysis designed to test that question. The registry record does not report such a margin or an equivalence analysis. A nonsignificant p-value alone cannot demonstrate equivalence, and a broad interval is not evidence that an important difference is impossible.

Nor does the result prove that one approach improves or worsens erectile function. It describes a comparison using the posted participant counts and the reported risk-difference calculation. The endpoint definition is not fully specified in the registry record, and the record notes missing questionnaire submissions at 24 months without explaining how missing information was handled. Those limitations constrain interpretation of how broadly the estimate applies.

The secondary outcomes add information about other recorded domains, but they are not substitutes for the primary endpoint and their p-values are unadjusted. They should not be combined into a single verdict about the interventions. Serious adverse event fields list no affected participants, but those figures likewise do not establish that risk is absent or summarize every type of toxicity.

In practical terms, the registry record supports a cautious description of the observed data and their uncertainty, not a treatment recommendation. It does not report enough detail to reconstruct the complete analysis plan, outcome classification, or missing-data strategy. Any broader causal or clinical conclusion would go beyond what these posted results establish.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its main comparison illustrates the difference between an estimated effect and the certainty around that estimate. The risk difference is a single summary of the observed group contrast, while the interval shows that many materially different values remain compatible with the data. A p-value alone would conceal much of that range. Reading both together discourages the mistaken conclusion that a nonsignificant result proves no difference.

The endpoint also illustrates why measurement and analysis populations matter. Erectile dysfunction rates are reported as participant counts, but the registry description names both a physical test and a questionnaire without giving the classification threshold or explaining how their results were combined. Some participants did not submit follow-up questionnaires at 24 months, and the missing-data method is not reported. Statistical estimates can only be interpreted fully when the endpoint and the data contributing to it are clearly defined.

The differing outcome-specific denominators show why enrollment should not automatically be equated with the number analyzed for every endpoint. Each outcome may have its own available data, and the record does not identify formal analysis populations. This makes transparency about denominators and missingness central to interpreting clinical trial results.

Finally, the secondary outcomes and planning illustrations underscore separate statistical issues. Unadjusted secondary tests do not carry the same confirmatory weight as a prespecified primary analysis when multiplicity handling is unreported. Planning figures based on observed effects can illustrate how sample requirements depend on the target effect, but they are not the original design rationale or evidence of achieved power. These distinctions help readers avoid drawing stronger conclusions than the registry record supports.

18. 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.

Several trial-specific details needed for a fuller assessment are not reported in the registry record. The primary outcome description identifies a postage stamp test and the International Index of Erectile Function questionnaire, but does not state the threshold for classifying erectile dysfunction or how the two sources contributed to the participant count. The role of the partner questionnaire in the primary endpoint is also not defined.

The record notes that some patients did not submit follow-up questionnaires at 24 months post-treatment, but it does not quantify this missingness or describe reasons, group patterns, or analytic handling. It also does not explain why the primary comparison denominators differ from the denominators reported for other outcomes. The analysis population and whether participants were analyzed according to their assigned group are not reported.

The registry record does not give a detailed randomization procedure, masking procedure, original sample-size justification, interim analysis plan, or complete statistical analysis plan. The phase field is listed as NA even though the brief purpose describes a randomized phase III trial. This difference in record descriptions should be noted rather than resolved by assumption.

The treatment descriptions specify the radiotherapy approach and approximate schedule but do not give detailed dose parameters. The record's description of the population is limited to stage II prostate cancer and the official title's favorable to intermediate risk wording. It does not provide additional eligibility or baseline clinical detail in the registry record recorded for these results. These limitations restrict assessment of generalizability and make it difficult to determine how closely the posted comparisons follow the trial's original protocol.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Intensity-Modulated Radiation Therapy With or Without Decreased Radiation Dose to Erectile Tissue in Treating Patients With Stage II Prostate Cancer — NCT00084552.
• Registry record last updated 2021-02-25; status last verified 2021-02.
• Results first posted 2021-02-25.
• 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.

22. Record Summary

The registry record describes a completed, randomized, single-masked, parallel-group trial sponsored by Fox Chase Cancer Center, with enrollment of 116. The phase field is listed as NA; the brief purpose describes the study as a randomized phase III trial. The comparison was conventional intensity-modulated radiotherapy, s-IMRT, versus intensity-modulated radiotherapy with erectile-tissue dose restriction, ETS-IMRT.

The primary outcome was erectile dysfunction rates over five years after completion of radiotherapy. The posted primary comparison reports a risk difference of 0.020, with an interval from -0.168 to 0.209 and an unadjusted p-value of 0.832. The interval includes no difference and extends in both directions, leaving substantial uncertainty about the size and direction of the comparison.

Secondary outcomes were freedom from biochemical failure, acute GI toxicity, and acute GU toxicity. The record notes incomplete questionnaire submission at 24 months, but does not report the missing-data method, analysis populations, multiplicity plan, or original sample-size justification.