A Study to Evaluate the Safety and Efficacy of Relugolix in Men With Advanced Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Safety and Efficacy of Relugolix in Men With Advanced Prostate Cancer (NCT03085095), a randomized phase 3 study. The primary outcome is Sustained Castration Rate.

2. Clinical Question

The clinical question is framed around sustained testosterone suppression, not simply a single measurement at the end of treatment. The primary outcome covers Week 5 Day 1 (Day 29) through Week 49 Day 1 (Day 337), and the registry defines the rate as the cumulative probability of testosterone suppression to < 50 ng/dL. The results therefore concern the endpoint and follow-up period as defined in the registry; they do not, on their own, address every possible clinical outcome or longer-term experience.

3. Trial Design

The registry describes HERO as a multinational, Phase 3, randomized, open-label, parallel-group study of relugolix and leuprolide acetate in men with advanced prostate cancer. It is marked completed. The recorded start date is 2017-04-18, and the primary completion date is 2019-10-25. Enrollment is listed as 1134 participants.

The two listed treatment groups received relugolix or leuprolide acetate, each described as lasting 48 weeks. The study summary specifies relugolix 120 mg orally once daily. It does not give the leuprolide acetate dosing schedule, so details beyond the named treatment and duration are not reported in the registry record. The registry identifies the allocation as randomized, the model as parallel, and masking as none; this means the study was open-label rather than blinded according to the record.

The primary endpoint analysis population is defined as all randomized participants who received at least 1 dose of study drug. The registry reports 622 participants in the relugolix endpoint group and 308 in the leuprolide acetate endpoint group. These are the group sizes attached to the primary outcome results, not a complete account of the disposition of everyone enrolled. Reasons for any difference between total enrollment and the reported endpoint group counts are not reported in the registry record.

The registry lists 27 outcome measures and 9 analyses, and reports 25 secondary outcomes as posted. The primary outcome is sustained castration rate; secondary measures include castration rates at earlier time points, prostate-specific antigen response measures, follicle-stimulating hormone, and testosterone recovery. The complete protocol, detailed schedule of assessments, original statistical analysis plan, and details of any interim analyses are not reported in the registry record. The record identifies the study design and outcomes but does not establish why the enrollment target was chosen or how it was justified.

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: The primary analysis of efficacy and safety included 934 participants. The primary analysis excluded additional participants with metastatic disease and a cohort of participants enrolled in China and Taiwan who will be included in the final analysis of the study (N=200).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants who received at least 1 dose of study drug.

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 randomized participants who received at least 1 dose of study drug in the primary analysis part of the study.

6. Primary Endpoint

The registry lists the primary outcome as Sustained Castration Rate, measured over From Week 5 Day 1 (Day 29) to Week 49 Day 1 (Day 337).

The primary endpoint is sustained castration rate, reported as a percentage of participants. The registry defines it as the cumulative probability of testosterone suppression to < 50 ng/dL, estimated separately for each treatment group using the Kaplan-Meier method. The endpoint timeframe runs from Week 5 Day 1 (Day 29) to Week 49 Day 1 (Day 337). It is therefore a time-to-event-style estimate of maintaining or reaching the specified testosterone suppression during a defined follow-up period, rather than only a simple comparison of measurements at one visit.

General: A threshold-based endpoint translates a laboratory measurement into a defined state for analysis. A sustained rate can describe the probability of meeting that threshold over time while accounting for the timing of observations and events under the method used. Kaplan-Meier estimation is commonly used when follow-up times or event times vary; its interpretation depends on the event definition and the assumptions about censoring. The registry record does not provide enough detail to assess every implementation assumption or how censoring was handled.

The registry states an efficacy evaluation criterion: the lower bound of the 95% confidence interval for the relugolix group’s cumulative probability had to be at least 90%. The relugolix estimate is 96.7%, with a 95% confidence interval from 94.9% to 97.9%. The interval’s lower bound is above the stated threshold. This comparison describes the registry’s stated criterion and the posted estimate; it does not substitute for the full sponsor analysis or establish conclusions beyond this endpoint and its defined population.

7. Results Posted in the Registry

• Leuprolide Acetate: 89.0% (274/308) versus 96.6% (601/622) on control; risk difference -7.7 percentage points (95% CI -11.4 to -3.9), risk ratio 0.92 (0.88–0.96); unadjusted two-proportion z-test p = <0.001.

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.

Castration Rate At Week 1 Day 4

• 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:
  • Leuprolide Acetate: 0.0% (0/308) versus 56.1% (349/622) on control; risk difference -56.1 percentage points (95% CI -60.0 to -52.2); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Leuprolide Acetate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Castration Rate At Week 3 Day 1

• 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:
  • Leuprolide Acetate: 12.0% (37/308) versus 98.7% (614/622) on control; risk difference -86.7 percentage points (95% CI -90.4 to -83.0), risk ratio 0.12 (0.09–0.16); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Leuprolide Acetate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Confirmed Prostate-specific Antigen (PSA) Response Rate

• 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:
  • Leuprolide Acetate: 19.8% (61/308) versus 79.4% (494/622) on control; risk difference -59.6 percentage points (95% CI -65.1 to -54.1), risk ratio 0.25 (0.20–0.31); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Leuprolide Acetate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover early castration rates, prostate-specific antigen response, follicle-stimulating hormone, profound castration, and testosterone recovery. The results that are reported include outcomes at early time points and a confirmed prostate-specific antigen response measure. Taken together, the set addresses related but distinct aspects of the biological response and its timing. The overall pattern is consistent with the primary result in the limited sense that multiple posted early response measures favor higher observed rates in the relugolix group than in the leuprolide acetate group.

These secondary outcomes complement rather than replace the primary endpoint. The primary question concerns sustained suppression over a defined period, while the secondary measures ask about specific time points, response definitions, or other laboratory outcomes. Agreement in direction across related outcomes can add context, but it does not make them equivalent measures or prove that each is independently confirmatory. The registry record does not report the full statistical analysis plan or the precise prespecified hierarchy among secondary outcomes.

Some secondary comparisons have small unadjusted p-values, including sponsor-reported values of p < 0.001 and count-based values of p < 0.001 for certain outcomes. Those results require caution because many outcomes and time points were examined. When multiple hypotheses are tested, the chance of at least one apparently notable result can increase unless the analysis accounts for multiplicity. Whether and how the sponsor controlled that issue is not reported in the registry record. The listed p-values should therefore be read as outcome-specific results, not as a single overall test of all secondary endpoints.

The registry reports 25 secondary outcomes as posted, while the named outcomes include several different domains. Not every result or analysis detail is reproduced in the summary information. Missing definitions, analysis populations, and multiplicity procedures limit comparisons across endpoints. The secondary results can describe the breadth and timing of measured responses, but the primary endpoint remains the central outcome for the stated study question.

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

• Castration Rate At Week 1 Day 4
• Castration Rate At Week 3 Day 1
• Confirmed Prostate-specific Antigen (PSA) Response Rate
• Profound Castration Rate At Week 3 Day 1 (Day 15)
• Follicle-stimulating Hormone (FSH) Level
• PSA Response Rate At Week 3 Day 1
• PSA Response Rate At Week 5 Day 1
• Testosterone Recovery Rate

9. Statistical Interpretation

10. Statistical Methods Explained

General: Randomization is intended to make treatment groups comparable on average with respect to measured and unmeasured characteristics at allocation. It does not guarantee that groups will be identical, and it does not eliminate the need to define an analysis population and outcome methods. The registry identifies this study as randomized and parallel-group. The record does not report the randomization sequence method, allocation concealment details, or stratification factors.

What does the Kaplan-Meier estimate represent?

General: Kaplan-Meier estimation uses information on the timing of events and the time participants remain under observation to estimate an event-related probability over follow-up. Participants whose event status is not observed through the end of their available follow-up may be censored rather than counted as having experienced the event. The method relies on assumptions about the censoring process. The registry identifies the primary sustained castration rate as a Kaplan-Meier estimate but does not report the detailed censoring rules, how missing visits were handled, or the exact event-time implementation.

The primary outcome is defined as the cumulative probability of testosterone suppression to < 50 ng/dL over the period from Week 5 Day 1 (Day 29) to Week 49 Day 1 (Day 337). The stated efficacy criterion concerns the lower bound of the relugolix group’s 95% confidence interval, which had to be at least 90%. The record reports a relugolix estimate of 96.7% and a confidence interval of 94.9% to 97.9%. This criterion is a decision rule described in the registry; it should be distinguished from a comparison between treatment groups.

What does the confidence interval add?

General: A confidence interval gives a range of estimates compatible with the data under the method and assumptions used. A narrower interval indicates greater statistical precision for the parameter being estimated, while a wider interval indicates more uncertainty. It does not mean that individual outcomes fall within the interval, and a 95% confidence interval is not a guarantee that the true value lies within the particular calculated range. The registry reports 95% confidence intervals for the primary group estimates and for the count-based re-calculation. The different methods and estimands mean those intervals describe different quantities.

How is the count-based comparison different?

The simple re-calculation uses the recorded counts: 601 of 622 participants for relugolix and 274 of 308 for leuprolide acetate. Its risk difference is -0.077 when expressed for leuprolide acetate relative to relugolix, with a 95% confidence interval from -0.114 to -0.039 and p < 0.001. General: A risk difference compares the proportions with an event between groups. An unadjusted calculation uses the group counts directly and does not account for time to event or adjust for other variables. Here it is not the same estimand as the Kaplan-Meier primary endpoint, and its proportions do not exactly match the posted primary rate estimates. The registry’s own analysis should be interpreted according to the analysis it reports rather than replaced by this simpler calculation.

The registry’s sponsor-reported analyses include a non-inferiority result with a treatment difference of 7.9 and a 95% confidence interval from 4.1 to 11.8, as well as a superiority result with p < 0.001 from a two-sided t-test. The record does not give the non-inferiority margin, a p-value for that non-inferiority result, or an effect estimate for the superiority test. Those missing details limit independent assessment of the sponsor’s analysis specifications from the registry record alone.

Why can binary outcomes require care?

General: A binary outcome classifies participants into event and no-event categories. The estimated proportion depends on how the event is defined, the population included, and the time at which or period over which it is assessed. When outcomes are rare or very common, intervals and comparisons can behave differently from those for outcomes with proportions near the middle of the possible range. For time-based outcomes, reducing follow-up to a single event/no-event count can discard timing information. This is one reason a direct count-based comparison should not be conflated with a Kaplan-Meier estimate.

General: Over-dispersion matters when variation in observed data is greater than a model expects. If an analysis assumes less variation than is actually present, its standard errors may be too small and its confidence intervals too narrow. The registry’s primary outcome description names Kaplan-Meier estimation; it does not report a model-based count analysis or an over-dispersion adjustment for that endpoint. This general issue should not be taken as evidence that over-dispersion occurred in this trial.

What do the p-values say?

General: A p-value measures how incompatible observed data are with a specified null hypothesis under a particular statistical model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an effect. The registry reports sponsor superiority p < 0.001 for the primary outcome and p-values for some secondary outcomes. A separate unadjusted count-based re-calculation reports p < 0.001. These values are attached to different analyses and should not be treated as interchangeable.

The registry does not report the original statistical analysis plan, details of multiplicity control, handling of missing outcome data, or interim-analysis procedures. Those items are important when judging whether the reported inferential results correspond to prespecified analyses and how uncertainty was managed across multiple outcomes. In their absence, interpretation should stay close to the endpoint definitions and analyses explicitly described in the record.

11. Confidence Intervals and Precision

The primary estimate for relugolix is 96.7%, with a 95% confidence interval from 94.9% to 97.9%. The interval gives a range of plausible values for the cumulative probability under the Kaplan-Meier method and the registry’s analysis assumptions. Its lower bound is 94.9%, compared with the registry’s stated efficacy threshold of 90%. For leuprolide acetate, the estimate is 88.8%, with a 95% confidence interval from 84.6% to 91.8%. The intervals describe uncertainty around the group-specific estimates; they are not prediction ranges for individual participants.

General: Precision depends on factors such as the amount of information available, event frequency, follow-up, and the analysis method. A confidence interval is useful because a point estimate alone does not show how uncertain the estimate is. The reported interval for relugolix is concentrated around its estimate, whereas the interval for leuprolide acetate covers a broader range of percentages. This describes their reported precision, not the cause of any difference in precision.

The unadjusted count-based risk difference has a 95% confidence interval from -0.114 to -0.039. It is a separate calculation based on group event counts, not the same time-based estimand as the primary Kaplan-Meier result. Its interval should therefore be interpreted within that count-based analysis rather than substituted for the primary group confidence intervals.

General: Confidence intervals do not account for every possible source of uncertainty. They do not, by themselves, address missing-data bias, measurement issues, deviations from the analysis plan, or the effect of examining multiple outcomes. The registry record does not report enough detail to evaluate all these sources. Statistical precision is consequently only one part of the overall interpretation.

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 display gives planning illustrations based on fractions of the observed effect. The primary comparison rows are expressed as participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The sample-size illustrations are not the original trial’s design calculations. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which a study would have an 80% chance of rejecting the null hypothesis if the assumed effect and planning conditions held. The 90% power column gives the corresponding number per arm for a 90% chance under those same conditions. General: Power is a planning probability tied to a specified effect, significance level, allocation, and statistical method. It is not a measure of the probability that a particular result is true.

Rows that plan for 75% or 50% of the observed effect use smaller target effects than the row planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation under otherwise similar assumptions, so they require more participants per arm in these illustrations. The displayed counts vary by endpoint and assumed effect fraction; they should be read as conditional planning examples rather than evidence about what the trial was designed to detect.

These figures are not observed power. They do not describe the probability that the completed study detected its actual effect. The observed sample size, estimated effect, and confidence interval are more informative for interpreting the completed results than a retrospective power calculation.

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 = 0.966; treatment proportion p₁ = 0.890; average p̄ = 0.928.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3657 = 0.7168.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3617 = 0.3044.
4. n = (0.7168 + 0.3044)² / (-0.0766)² = 177.6, rounded up to 178 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 <- 0.966237942122186                          # control proportion
p1 <- 0.88961038961039                          # 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(3085095)
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 = 178 (80% power), 238 (90% power)
 75% of observed effect: n per arm = 278 (80% power), 371 (90% power)
 50% of observed effect: n per arm = 535 (80% power), 716 (90% power)
power.prop.test: 177.6 
Simulated power at n = 178 per arm: 0.821 (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 registry includes sponsor-reported analyses for the primary endpoint. The non-inferiority analysis reports a treatment difference of 7.9 with a 95% confidence interval from 4.1 to 11.8. A separate superiority analysis is reported with a two-sided t-test and p < 0.001. The registry does not give the non-inferiority margin, a p-value for that result, or an effect estimate for the reported superiority test. It also does not provide enough detail to reconstruct the full sponsor analysis specification.

The count-based re-calculation is a simple unadjusted comparison of the posted event counts, yielding a risk difference of -0.077 for leuprolide acetate relative to relugolix, with a 95% confidence interval from -0.114 to -0.039 and p < 0.001. It does not reproduce the Kaplan-Meier method used to estimate the primary endpoint. In particular, the primary registry rates and the event-count proportions are not identical quantities, so a difference between them is not, by itself, evidence of a conflict in results.

The record does not flag a discrepancy between the sponsor analysis and the re-calculation. The sponsor-reported analysis remains the relevant registry analysis for its stated inferential framework, while the re-calculation is useful as a transparent, unadjusted check based on the counts. Neither should be expanded beyond the endpoint, population, and methods it represents. Further details such as the non-inferiority margin and full analysis plan are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 27 outcome measures, reports 25 secondary outcomes as posted, and identifies 9 analyses. Testing multiple outcomes or multiple time points creates a multiplicity issue: even when each test uses a conventional significance threshold, the chance of at least one small p-value across a collection of tests can be greater than for a single test. General: Prespecified hierarchies, adjusted testing procedures, or a clear separation between confirmatory and exploratory outcomes can help manage this issue. The registry record does not report whether such a plan was used for the secondary outcomes or how any adjustment was performed.

The primary outcome description identifies the analysis population as all randomized participants who received at least 1 dose of study drug. This is the population stated for the primary outcome, but the registry does not report full analysis-population definitions for each secondary endpoint. It also does not report the number of participants with missing measurements at each visit, reasons for missing data, imputation methods, censoring rules, or sensitivity analyses for missingness. Those details matter because missing data can affect both estimates and uncertainty, particularly when the likelihood of missingness is related to participants’ outcomes or follow-up.

The record identifies a Kaplan-Meier method for the primary outcome, but does not fully describe the assumptions and operational details used to handle censoring. The validity of a time-to-event estimate can depend on whether participants with incomplete follow-up are censored appropriately. Without the underlying protocol and analysis plan, the registry summary does not permit a full independent audit of these decisions.

Interim analyses, any associated stopping rules, and any adjustments to inference for interim looks are not reported in the registry record. The original statistical analysis plan and the rationale for the enrollment target are also not reported. These absences do not show that such procedures were or were not used; they limit what can be established from the registry record. Inference should therefore be based on the reported definitions and analyses, with uncertainty about unreported procedures kept explicit.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaemia (1.0%), cardio-respiratory arrest (1.0%), transient ischaemic attack (1.0%), acute myocardial infarction (0.8%), inguinal hernia (0.6%).

The registry reports serious adverse events in 76 of 622 participants in the relugolix group and 47 of 308 participants in the leuprolide acetate group. It reports deaths in 7 and 9 participants, respectively. These counts describe what the registry records for the groups; they do not establish that a serious event or death was caused by a study drug. The record does not provide a causal assessment in the information.

The registry lists anaemia, cardio-respiratory arrest, and transient ischaemic attack at 1.0% each among the leading serious adverse event terms. Acute myocardial infarction is listed at 0.8%, and inguinal hernia and urinary tract infection at 0.6% each. The group attribution for these listed terms is not specified in the registry record, so they should not be assigned to one treatment group based on these figures alone.

General: Serious adverse event counts are descriptive safety information. Interpretation depends on the event definitions, observation period, exposure, event ascertainment, and handling of multiple events in the same participant. The registry figures do not by themselves quantify comparative risk or establish causation. Detailed event narratives, severity grades, relatedness assessments, and exposure-adjusted analyses are not reported in the registry record.

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

The reported primary result is a high Kaplan-Meier estimate of sustained testosterone suppression to < 50 ng/dL in the relugolix group over the stated period from Week 5 Day 1 (Day 29) to Week 49 Day 1 (Day 337). Its estimate is 96.7%, with a 95% confidence interval from 94.9% to 97.9%. The leuprolide acetate estimate is 88.8%, with a 95% confidence interval from 84.6% to 91.8%. The relugolix interval’s lower bound is above the registry’s stated 90% efficacy criterion.

Those statistics describe the registry-defined endpoint in the primary analysis population. They do not establish how participants would fare on outcomes that were not measured, how results would look beyond the study timeframe, or whether an individual participant would have the same outcome. They also do not turn the endpoint into a direct measure of every potential benefit or harm. The clinical significance of a laboratory threshold and its relationship to other outcomes are questions beyond the numerical result alone.

The sponsor-reported primary analyses include a non-inferiority result and a superiority p-value, while a simple unadjusted re-calculation based on event counts gives a separate risk-difference estimate. These analyses use different statistical formulations and should not be conflated. The registry does not report the non-inferiority margin or complete analysis plan, so the sponsor’s inferential framework cannot be fully reconstructed from the record alone.

The safety information is also descriptive: the registry reports serious adverse event counts, deaths, and selected serious event terms, but those data alone do not determine causation or provide a complete comparative safety assessment. Questions about the balance of outcomes require the full clinical context and detailed study reports, which are not reported in the registry record. The posted statistics support a bounded interpretation of the measured endpoint and recorded events, not medical advice or conclusions outside the study’s design and reported follow-up.

18. Why This Trial Matters Statistically

Statistically, this trial is useful for examining how a time-based endpoint can differ from a simple event-count comparison. The primary sustained castration rate is estimated with Kaplan-Meier methods across a defined follow-up period, while the unadjusted re-calculation uses the posted event counts as a binary comparison. Those methods target different quantities: one uses timing and follow-up information, and the other compares counts directly. Reading them as interchangeable would obscure what each estimate represents.

The registry also gives a concrete example of separating a criterion applied to a group-specific estimate from a between-group test. The stated efficacy criterion is based on the lower bound of the relugolix group’s 95% confidence interval being at least 90%. The sponsor-reported non-inferiority and superiority analyses address comparisons between treatment groups. These are related but not identical statistical questions, and the distinction is important when interpreting claims attached to a trial endpoint.

Another statistical lesson concerns precision. The group estimates are accompanied by 95% confidence intervals, which show uncertainty rather than merely presenting point estimates. The sample-size illustrations show how planning requirements change when the target effect is set to a smaller fraction of the observed effect. Those illustrations are conditional calculations, not evidence about the original trial’s design rationale or the probability that the completed study succeeded.

Finally, the record demonstrates why registry results should be read with attention to what is not reported. Multiplicity procedures, missing-data methods, interim analyses, the non-inferiority margin, and the original sample-size justification are not reported in the registry record. Recognizing those gaps helps keep statistical interpretation appropriately specific and avoids treating a collection of endpoint results as a complete account of the study’s design and analysis.

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.

The registry record does not report the full protocol or statistical analysis plan. As a result, the prespecified hierarchy of outcomes, detailed analysis populations beyond the primary endpoint definition, and procedures for missing data cannot be assessed from the record. The primary outcome is described as a Kaplan-Meier estimate, but operational details such as censoring rules and handling of measurements outside scheduled visits are not reported.

The sponsor-reported non-inferiority result lacks a reported margin in the registry summary. Without that margin and the complete analysis specification, the non-inferiority framework cannot be independently assessed from the reported treatment difference and confidence interval alone. The superiority analysis gives p < 0.001 from a two-sided t-test, but its effect estimate and confidence interval are not reported in the registry record.

The record does not report how multiplicity was handled across the many outcomes and assessment times, whether interim analyses were conducted, or whether inference was adjusted for any interim looks. The original sample-size assumptions and justification are also not reported. The displayed planning illustrations are based on the observed effect and stated generic assumptions rather than the trial’s original design rationale.

The primary endpoint population is described as randomized participants who received at least 1 dose, and the result counts differ from total enrollment. The reasons for the difference are not reported in the registry record. Detailed participant disposition, missing measurements, treatment discontinuations, and sensitivity analyses are not included in the summary information. Safety listings likewise do not provide detailed causal assessments or complete event-level context. These limitations constrain interpretation of the posted estimates; they do not, by themselves, demonstrate bias or invalidate the reported analyses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Safety and Efficacy of Relugolix in Men With Advanced Prostate Cancer — NCT03085095.
• Registry record last updated 2022-01-18; status last verified 2022-01.
• Results first posted 2021-03-25.
• 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.

23. Record Summary

NCT03085095 is a completed, randomized, open-label, parallel-group Phase 3 study of relugolix and leuprolide acetate in men with advanced prostate cancer. Enrollment is listed as 1134. The primary outcome is the Kaplan-Meier estimated sustained castration rate from Week 5 Day 1 (Day 29) to Week 49 Day 1 (Day 337), defined by testosterone suppression to < 50 ng/dL.

The primary estimate is 96.7% for relugolix, with a 95% confidence interval from 94.9% to 97.9%, and 88.8% for leuprolide acetate, with a 95% confidence interval from 84.6% to 91.8%. The registry’s stated relugolix efficacy criterion requires the lower confidence bound to be at least 90%. Sponsor-reported analyses include a non-inferiority treatment difference of 7.9, with a 95% confidence interval from 4.1 to 11.8, and a superiority p-value of p < 0.001.

The record also reports secondary outcomes and safety counts. Details of the original sample-size justification, multiplicity procedures, missing-data methods, interim analyses, and the non-inferiority margin are not reported in the registry record.