A Study of Immediate 9 Months Adjuvant Hormone Therapy With Triptorelin 11.25 mg Versus Active Surveillance After Radical Prostatectomy in High Risk Prostate Cancer Patients.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Immediate 9 Months Adjuvant Hormone Therapy With Triptorelin 11.25 mg Versus Active Surveillance After Radical Prostatectomy in High Risk Prostate Cancer Patients. (NCT01753297), a randomized phase 4 study. The primary outcome is Number of Subjects With BR Events.

2. Clinical Question

The clinical comparison is between an immediate adjuvant hormone-therapy approach and active surveillance following surgery. It is not a comparison of surgery with no surgery: radical prostatectomy is part of the clinical context for both groups. The main reported primary result is a count of participants with biochemical relapse events rather than a reported median time to relapse or a complete survival curve.

The registry describes a minimum monitoring period of 36 months for each participant and a maximum duration of 78 months, with the final analysis performed after the required 61 biochemical relapse events were observed across the global study. The clinical question is therefore about observed biochemical relapse events during the study’s follow-up, not about every possible outcome after surgery or about long-term outcomes beyond the monitoring described in the record.

3. Trial Design

This was a Phase 4, randomized, open-label, parallel-group, controlled study sponsored by Ipsen. It enrolled 226 participants and is listed as completed. The study involved China and Russia. The registry gives a start date of 2012-12-11 and a primary completion date of 2019-09-09.

Participants were assigned to immediate triptorelin or active surveillance after radical prostatectomy. The triptorelin group was planned to receive treatment beginning 8 weeks after surgery, over 9 months, as 3 injections. The comparator group was not to receive triptorelin. The registry states that participants in both groups would be followed every 3 months to monitor signs of disease progression, with a minimum monitoring period of 36 months per participant. It also reports a maximum duration of 78 months, with the last participant censored.

Randomization supports a comparison based on assigned group, while the open-label design means masking was not used. The registry describes the primary efficacy population as intention-to-treat: all randomized participants were analysed according to the group to which they were assigned, regardless of the treatment approach followed. Arm sizes in the primary outcome results were 117 for active surveillance and 109 for triptorelin.

The primary analysis was performed after 61 biochemical relapse events had been observed at the global study level. The record does not report the original sample-size justification or the trial’s original design assumptions. It also does not report a detailed sequence of randomization procedures, allocation concealment procedures, or an interim-analysis plan. Those details should not be inferred from the randomized, open-label, parallel-group description.

The registry lists 14 outcome measures and 17 analyses, with 11 secondary results posted. The posted outcome information includes biochemical relapse event counts, time-to-event outcomes, and other measures. Not every listed secondary measure has a numerical result in the outcome information available in the record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Subjects had to have undergone RP no more than 8 weeks prior to randomisation, with post-RP prostate specific antigen (PSA) levels ≤0.2 nanograms/millilitre (ng/mL). The screening visit took place 6 weeks after RP (i.e. 2 weeks prior to randomisation). No other treatment for prostate cancer was permitted.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The ITT population consisted of all randomised subjects analysed according to the group to which they were randomised (i.e. regardless of treatment approach followed).

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: Intention-to-Treat (ITT) population consisted of all randomised subjects analysed according to the group to which they were randomised (i.e. regardless of treatment approach followed).

6. Primary Endpoint

The registry lists the primary outcome as Number of Subjects With BR Events, measured over Baseline (Day 1) and every 3 months until end of study with final analysis performed after required 61 BRs were observed on global study level. Minimum monitoring period of 36 months for each subject; maximum duration of 78 months (last subject censored)..

The primary outcome is the number of participants with biochemical relapse events. In this study, biochemical relapse was defined as an increased PSA >0.2 ng/mL confirmed by a second measurement performed 4 to 6 weeks later. The registry reports the number of participants with such events in each randomized group.

Biochemical relapse is a laboratory-based indicator used to identify a return of detectable disease activity after radical prostatectomy. General: a prespecified event definition makes the outcome more reproducible by setting a threshold and confirmation requirement, rather than relying on an unstructured judgment that relapse occurred. Requiring a second measurement also distinguishes a confirmed event from an isolated elevated result.

The primary efficacy analysis is described as biochemical relapse-free survival, and it was performed after 61 relapse events had been observed across the study. The reported primary outcome result is a count, however, not a reported median time to biochemical relapse or a hazard ratio. A count indicates how many participants met the event definition during the observed follow-up; it does not by itself describe when the events occurred or how follow-up time differed among participants.

Time-to-event outcomes can use both the event and information about when it occurred, including censoring when a participant’s event status is not observed through the end of follow-up. General: this can make use of follow-up information that a simple event count does not capture. The registry reports separate time-to-event analyses for some secondary measures, but the primary result should be interpreted according to the event counts and definition actually posted.

7. Results Posted in the Registry

• Triptorelin: 23.9% (26/109) versus 29.9% (35/117) on control; risk difference -6.1 percentage points (95% CI -17.6 to 5.5), risk ratio 0.80 (0.52–1.23); unadjusted two-proportion z-test p = 0.305.

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.

Median Time to Event-Free Survival (EFS)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Active Surveillance vs Triptorelin: hazard ratio 1.52 (95% CI 0.24–9.59), reported p = 0.653 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Active Surveillance vs Triptorelin and the control. The interval gives the range of effects that remain compatible with the data.

Median Time to PSA Doubling Time (PSADT)

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Active Surveillance vs Triptorelin: hazard ratio 1.72 (95% CI 0.44–6.73), reported p = 0.435 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Active Surveillance vs Triptorelin and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover time to event-free survival, time to PSA doubling time, overall survival, disease-specific mortality, and changes in PSA levels. The available numerical time-to-event results are for event-free survival and PSA doubling time. The registry lists other secondary measures but does not provide numerical results for every listed measure in the outcome information summarized by the record.

The available secondary time-to-event analyses do not establish a clear separation between assigned groups: their reported p-values are not small, and their confidence intervals are broad. This pattern is compatible with substantial uncertainty. It does not independently confirm the primary result, nor does it establish that the groups have the same time-to-event experience. The primary biochemical-relapse counts remain the central result for the primary question, while the secondary outcomes add context about other dimensions of follow-up.

General: secondary outcomes can help assess whether a primary finding is accompanied by a consistent pattern across related measures. Their interpretation is strongest when outcomes, analysis methods, and hypotheses are prespecified and when multiplicity is addressed. When many outcomes or comparisons are examined, some apparently notable results may arise by chance, even when no underlying differences exist. Conversely, adjusting for many comparisons can reduce the ability to detect real effects.

The registry record does not report a multiplicity adjustment or a complete statistical analysis plan for the secondary results. Accordingly, secondary findings should generally carry less weight than the primary analysis, particularly when many outcomes and analyses are listed. The secondary measures are best treated as complementary and potentially exploratory rather than as independent, definitive confirmations of a treatment effect.

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

• Median Time to Event-Free Survival (EFS)
• Q1 Time to EFS
• Median Time to Overall Survival (OS)
• Q1 Time to OS
• Time to Disease-specific Mortality
• Median Time to PSA Doubling Time (PSADT)
• Q1 Time to PSADT
• Percent Change From Baseline in PSA Levels

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the registry’s biochemical-relapse definition during observed follow-up or did not. The study reports the event count and total participants in each randomized group. A risk-difference comparison expresses the contrast in event probabilities between groups. General: a risk difference is an absolute-scale measure, while a risk ratio or odds ratio expresses a relative-scale contrast. These measures answer related questions but have different interpretations.

What does the primary p-value mean?

The unadjusted p-value of 0.305 is a recalculation based on the posted summary counts. General: a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model, assuming the model’s conditions. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A result that is not statistically significant does not prove equality or rule out a difference. No adjusted primary analysis is reported in the posted outcome information.

How do confidence intervals help?

A confidence interval gives a range of values compatible with the data and the method used to construct it. General: a narrower interval indicates greater precision, while a wider interval indicates greater uncertainty. For the primary binary comparison, the confidence interval crosses the no-difference value, so it allows for effects in either direction. The interval should be read alongside the point estimate, event counts, and study design rather than as a boundary that makes all values outside it impossible.

What does a Cox model estimate?

The secondary time-to-event analyses include Cox regression hazard ratios. General: a hazard ratio compares the instantaneous event rates between groups over follow-up, conditional on the model’s assumptions; it is not the same quantity as a ratio of the total event counts. A hazard ratio can be difficult to interpret if the relative event rates change over time, and its interpretation depends on the proportional-hazards assumption. The registry identifies the method as Cox regression but does not report whether that assumption was assessed or whether any alternative model was used.

The event-free survival comparison also has a log-rank analysis. General: the log-rank test compares event-time distributions between groups while accounting for censoring. The Cox regression and log-rank analyses are related time-to-event methods, but they are not identical procedures and need not produce identical p-values. The reported results include both a log-rank p-value and a Cox estimate with its confidence interval and p-value.

What is censoring?

In a time-to-event analysis, a participant may not have a recorded event by the end of their available follow-up. That observation is generally treated as censored at the last time the participant was known to be event-free, rather than as proof that an event could never occur. General: survival methods rely on assumptions about censoring, including that the censoring process does not make the remaining event experience systematically unrepresentative in a way the analysis fails to address. The registry gives a maximum duration of 78 months and notes that the last participant was censored, but it does not report detailed censoring patterns or diagnostics.

The record labels the primary analysis population as intention-to-treat. This means randomized participants are analysed according to their assigned group, regardless of the treatment approach followed. General: retaining the randomized assignment for analysis helps preserve the comparability created by randomization. It does not eliminate all possible missing-data concerns, and interpretation still depends on the completeness and handling of outcome information.

Why can event rates vary more than a simple model expects?

General: over-dispersion occurs when observed variation is greater than a statistical model assumes. It can make standard errors too small if ignored, resulting in confidence intervals that are too narrow and tests that are too optimistic. This is a general consideration for count outcomes and is not a reported finding about this trial. The registry reports participant counts for the primary outcome and does not report an over-dispersion analysis.

The registry does not report the detailed statistical analysis plan, model diagnostics, missing-data methods, or whether the secondary analyses were adjusted for multiple comparisons. Those items are not reported in the registry record. The analyses can therefore be described by their named methods and posted estimates, but unreported modeling choices should not be presumed.

11. Confidence Intervals and Precision

The primary binary comparison is uncertain. Its confidence interval spans the no-difference value and allows for contrasts in either direction. The observed event counts are therefore compatible with a range of possible underlying effects, rather than establishing a precise difference between assigned groups. The simple unadjusted recalculation has p = 0.305, which is consistent with the interval’s lack of a clear separation from no difference.

The time-to-event estimates are also imprecise. For event-free survival, the reported Cox hazard ratio is 1.52 and its 95% confidence interval extends from 0.24 to 9.59. For PSA doubling time, the hazard ratio is 1.72 and its 95% confidence interval extends from 0.44 to 6.73. In both cases the interval covers a broad range of possible relative event rates, so the point estimate should not be read as a precise measure of the contrast.

General: a confidence interval reflects sampling uncertainty under the analysis method; it does not automatically include every source of uncertainty, such as departures from model assumptions, outcome measurement issues, or missing information. Broad intervals often arise when the available event information is limited for the question being estimated. The PSA doubling time analysis includes 38 participants in the active-surveillance group and 27 in the triptorelin group, fewer than the full primary-outcome arm sizes.

The registry does not report confidence intervals for every outcome, nor does it provide numerical medians for the posted event-free survival and PSA doubling time results. Such unreported quantities cannot be recovered from the estimates shown. The precision of an estimate should be judged from the interval and the analysis population actually reported, not from the apparent difference between point estimates 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 are calculations based on observed effects, not the original trial design assumptions. For the binary comparison, the displayed quantities are participants per arm. For the time-to-event comparisons, they are total events across the study, not participants per arm. These are different planning scales and should not be compared as though they were the same quantity.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. The original sample-size justification and the trial’s own design assumptions are not reported in the registry record.

The 80% power column gives an illustrative sample size or event total for a design that would have an 80% probability of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column describes the corresponding planning target for a 90% probability. Power is a property of a proposed design under assumptions; it is not a measure of whether the observed result is true.

The rows that plan for 75% or 50% of the observed effect represent smaller effects than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation and therefore require more participants or events for the same power target. These values are planning illustrations, not observed power.

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 = 0.299; treatment proportion p₁ = 0.239; average p̄ = 0.269.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6270 = 1.2289.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6255 = 0.5265.
4. n = (1.2289 + 0.5265)² / (-0.0606)² = 838.7, rounded up to 839 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 <- 0.299145299145299                          # control proportion
p1 <- 0.238532110091743                          # 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(1753297)
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 = 839 (80% power), 1,123 (90% power)
 75% of observed effect: n per arm = 1,519 (80% power), 2,032 (90% power)
 50% of observed effect: n per arm = 3,475 (80% power), 4,651 (90% power)
power.prop.test: 838.7 
Simulated power at n = 839 per arm: 0.801 (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

The registry lists 14 outcome measures and 17 analyses, with 11 secondary results posted. Considering multiple outcomes and analyses raises the issue of multiplicity: the more statistical comparisons made, the greater the chance that at least one result will appear unusual by chance alone. General: common approaches include prespecifying a hierarchy of outcomes or adjusting significance thresholds, but the appropriate approach depends on the trial’s aims and analysis plan.

The registry does not report whether the secondary analyses were adjusted for multiplicity, whether a hierarchy among secondary outcomes was prespecified, or how many analyses were planned before results were known. These details are not reported in the registry record. The secondary p-values should therefore not be treated as though they necessarily represent a single confirmatory testing strategy.

The primary analysis population is described as intention-to-treat and includes all randomized participants analysed according to assigned group, regardless of treatment approach followed. That definition supports interpretation of the randomized comparison. The posted outcome counts include 117 participants in the active-surveillance group and 109 in the triptorelin group. The record does not provide a detailed account of missing outcome data, exclusions from individual secondary analyses, or the methods used to address missing values.

For time-to-event analyses, incomplete follow-up is handled through censoring in the usual framework, but the registry does not describe the censoring distribution or provide diagnostics for assumptions about censoring. It reports a maximum duration of 78 months and says the last participant was censored. This does not by itself explain the amount or pattern of follow-up for all participants.

General: missingness can affect an estimate when the likelihood that an outcome is unavailable is related to the outcome or to participant characteristics. An intention-to-treat label does not, by itself, show how such missingness was addressed. The registry record does not report sensitivity analyses for missing data, detailed analysis-population counts for every outcome, or the original statistical analysis plan. Conclusions about these procedures should therefore remain limited to the information explicitly described.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: alanine aminotransferase increased (1.0%), papillary thyroid cancer (1.0%), urethral stenosis (1.0%), inguinal hernia, obstructive (0.9%), salivary gland calculus (0.9%).

The registry reports serious adverse events for safety populations, separated into the period prior to Month 12 and the period posterior to Month 12. Prior to Month 12, 11 of 112 participants in the active-surveillance safety population had a serious adverse event, compared with 3 of 105 in the triptorelin safety population. Posterior to Month 12, the overall safety population included 2 serious adverse events among 217 participants at risk.

The record also reports other adverse events: 27 of 112 participants in the active-surveillance group and 31 of 105 in the triptorelin group prior to Month 12, and 7 of 217 in the overall safety population posterior to Month 12. The death counts reported for these groups are 1, 0, and 2, respectively. These are separate registry-reported counts; they should not be read as a causal comparison without accounting for the different time periods, populations, follow-up, and event definitions.

General: safety counts describe events observed and reported in the specified population and period. They do not by themselves establish that an event was caused by treatment, nor do they provide a complete account of event severity or duration. The record lists several serious-event terms, but the counts and percentages should be interpreted in the context of the stated safety groups and time windows.

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

The primary results describe the number of participants meeting a specified biochemical-relapse definition during observed follow-up: 35 of 117 in active surveillance and 26 of 109 in the triptorelin group. The unadjusted comparison is not statistically clear, and the confidence interval is broad enough to allow effects in either direction. The evidence therefore does not precisely determine the difference between the randomized groups.

Not finding a statistically clear difference is not the same as showing that the approaches are equivalent. Equivalence or noninferiority requires a prespecified margin and an analysis designed to test that question; no such framework is reported in the registry record. Nor does a nonsignificant comparison prove that there is no clinically meaningful effect. The posted estimates have uncertainty that should remain part of the interpretation.

The outcome is biochemical relapse, defined using PSA and confirmation. It is not itself a direct measure of every aspect of cancer progression, quality of life, treatment burden, or long-term survival. The registry lists several secondary outcomes, but numerical results are not posted for every listed measure. The event-free survival and PSA doubling time analyses also have broad intervals, so they do not resolve the uncertainty in the primary comparison.

These findings apply to the study population and the follow-up described in the registry: high-risk prostate cancer patients after radical prostatectomy, in a multinational study involving China and Russia, with follow-up every 3 months and a minimum monitoring period of 36 months. General: applying trial results to people outside the enrolled population requires considering similarities in disease, treatment context, and care. The record alone does not establish how well these results apply to other settings or groups.

The registry describes randomized assignment, which supports a comparative interpretation, but the open-label design and the incomplete reporting of analysis details remain relevant context. No medical recommendation follows from the event counts alone. The most defensible conclusion is about what the posted estimates show and how much uncertainty surrounds them.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison should be read through both the effect estimate and its precision. The primary event counts differ numerically between groups, but the comparison is not statistically clear and the confidence interval permits a range of underlying effects. Reporting the counts without uncertainty could invite an overly confident interpretation of a modest-looking numerical contrast.

It also shows the distinction between a binary event count and a time-to-event analysis. A count records whether participants experienced the defined event during observation. A time-to-event method also considers when events occurred and how long participants were observed before an event or censoring. These approaches address related but nonidentical questions, and one cannot substitute for the other.

The registry’s secondary results provide useful context but do not erase the limits of the primary result. Multiple outcomes and analyses make prespecification and multiplicity important, while details of those procedures are not reported in the registry record. Wide confidence intervals in the secondary time-to-event analyses further emphasize that a point estimate is not a precise summary of an uncertain comparison.

Finally, the example underscores the difference between study-planning illustrations and observed evidence. A planning calculation based on an observed effect is not the trial’s original sample-size justification and does not indicate the probability that the observed result is correct. Clear separation of design assumptions, posted results, and uncertainty is central to responsible interpretation of clinical-trial statistics.

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.

The registry’s reporting limits how much can be concluded about the analysis. It does not report the original sample-size justification, the trial’s original design assumptions, a detailed statistical analysis plan, or whether an interim-analysis plan was used. These details should not be inferred from the fact that the primary analysis was performed after 61 biochemical relapse events.

The primary comparison is based on event counts and a simple unadjusted recalculation. The record does not provide a primary confidence interval in the posted outcome information, though the recalculated comparison has an interval. The analysis should not be mistaken for a fully documented sponsor analysis plan. The record does not report all model specifications, diagnostic checks, or sensitivity analyses.

For the secondary outcomes, not all listed measures have numerical results posted. The event-free survival and PSA doubling time analyses have broad confidence intervals, and the reported medians are unavailable. The registry does not report detailed censoring patterns, methods for missing data, or checks of Cox model assumptions. It also does not report whether multiplicity was addressed for the secondary analyses.

The study was open-label, with no masking. That design feature is explicit in the registry and is relevant context, though the extent to which it affected outcome measurement cannot be determined from the posted information. The primary endpoint has a laboratory-based definition with confirmation, but other outcomes may involve different measurement considerations not detailed in the record.

These limitations do not invalidate the posted results. They constrain how narrowly the results can be interpreted and make it important to distinguish reported estimates from unreported methods or assumptions.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Immediate 9 Months Adjuvant Hormone Therapy With Triptorelin 11.25 mg Versus Active Surveillance After Radical Prostatectomy in High Risk Prostate Cancer Patients. — NCT01753297.
• Registry record last updated 2020-12-09; status last verified 2020-12.
• Results first posted 2020-12-09.
• 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 describes a completed, randomized, open-label, parallel-group Phase 4 study of 226 high-risk prostate cancer patients after radical prostatectomy. It compared immediate triptorelin 11.25 mg for 9 months with active surveillance and included participants in China and Russia.

The primary result reports biochemical relapse events in 35 of 117 active-surveillance participants and 26 of 109 triptorelin participants. The registry defines relapse as PSA >0.2 ng/mL confirmed by a second measurement 4 to 6 weeks later. The simple unadjusted comparison is not statistically clear, and the estimate is imprecise.

Posted secondary time-to-event analyses also have broad confidence intervals. The registry does not report the original design assumptions, a detailed statistical analysis plan, multiplicity procedures, or full missing-data methods. The results should be read as uncertain comparative estimates, not as proof of equivalence or absence of an effect.