A Comparative Study of Degarelix Three-month Depot in Three Different Dosing Regimens in Patients With Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Comparative Study of Degarelix Three-month Depot in Three Different Dosing Regimens in Patients With Prostate Cancer (NCT00116753), a randomized phase 2 study. The primary outcome is Number of Participants With Testosterone Level <=0.5 ng/mL From Day 28 Until the End of the Study.

2. Clinical Question

The study compared three schedules of degarelix, asking whether the proportion of participants with testosterone values at or below 0.5 ng/mL from Day 28 through the end of follow-up differed among the regimens. The registry describes the study rationale as evaluating dosing regimens intended to produce and maintain testosterone suppression over a three-month interval, while also gathering confirmatory safety evidence.

3. Trial Design

This was a randomized, open-label, multicenter, parallel-group phase 2 study of three degarelix regimens in patients with prostate cancer. The registry lists an enrollment of 460 and the study status as completed. The recorded study start is 2005-01, and primary completion is recorded as 2006-11. Ferring Pharmaceuticals is listed as the sponsor.

All three groups received degarelix. The regimens shared a 240 mg initiation dose at 40 mg/mL. The first group then received 240 mg at 40 mg/mL at months 1, 3, 6 and 9. The second used 240 mg at 60 mg/mL at those same maintenance months. The third used 240 mg at 60 mg/mL at months 1, 4, 7 and 10. Thus, the comparisons vary maintenance concentration, schedule timing, or both; they are not comparisons of degarelix with an untreated or different-drug control.

Random allocation and a parallel-group model are recorded, while masking is listed as none. The registry record does not report how the random sequence was generated, whether allocation was concealed, or further details of the multicenter structure. The primary outcome uses observed cases in the ITT population. The participant counts contributing to this outcome differ across arms, and they are not the same as the overall enrollment figure. The registry record does not report the reason for these differences or the trial's original sample-size rationale.

The study's stated rationale was to assess different three-month dosing regimens intended to produce and maintain testosterone suppression, and to provide confirmatory evidence about safety. The record identifies the primary outcome and several secondary outcomes, but does not report a complete protocol or statistical analysis plan.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Observed Cases in ITT population.

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 Number of Participants With Testosterone Level <=0.5 ng/mL From Day 28 Until the End of the Study, measured over From Day 28 to 12 or 13 months.

The primary endpoint counts participants whose testosterone values remained at or below 0.5 ng/mL from Day 28 until the end of the study. The registry describes the timeframe as Day 28 to 12 or 13 months and specifies that the reported figure is the number of participants with all testosterone values meeting the threshold during that period. The analysis population is described as observed cases in the ITT population.

This is a binary outcome: each participant either met the stated sustained-value criterion or did not. The reported percentages express how often the criterion was met among the participants contributing data in each arm. The endpoint therefore reflects both the threshold and the requirement that values continue to meet it over follow-up; it is not simply a measurement taken once at the final visit. A separate secondary outcome concerns testosterone after Day 28 until the end of the study, and another concerns the value at Day 28 alone.

General statistical context: a sustained threshold outcome can summarize whether a participant maintained a specified biological measure over a defined interval. It also compresses a sequence of measurements into one participant-level result. The interpretation depends on the threshold, timing, measurement availability, and rules for handling missing measurements. The registry states the threshold and timeframe, but further details about measurement schedules and missing-value rules are not reported in the registry record.

7. Results Posted in the Registry

• Degarelix 240@40/240@60 (1,3,6,9): 79.5% (101/127) versus 78.3% (94/120) on control; risk difference 1.2 percentage points (95% CI -9.0 to 11.4), risk ratio 1.02 (0.89–1.16); unadjusted two-proportion z-test p = 0.818.
• Degarelix 240@40/240@60 (1,4,7,10): 85.3% (110/129) versus 78.3% (94/120) on control; risk difference 6.9 percentage points (95% CI -2.6 to 16.5), risk ratio 1.09 (0.97–1.23); unadjusted two-proportion z-test p = 0.155.

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.

Number of Participants With Testosterone Level <=0.5 ng/mL After the Dose at Day 28 Until the End of the Study

• 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:
  • Degarelix 240@40/240@60 (1,3,6,9): 80.2% (101/126) versus 80.7% (96/119) on control; risk difference -0.5 percentage points (95% CI -10.5 to 9.4), risk ratio 0.99 (0.88–1.12); unadjusted two-proportion z-test p = 0.919.
  • Degarelix 240@40/240@60 (1,4,7,10): 86.0% (111/129) versus 80.7% (96/119) on control; risk difference 5.4 percentage points (95% CI -3.9 to 14.7), risk ratio 1.07 (0.95–1.19); unadjusted two-proportion z-test p = 0.255.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Degarelix 240@40/240@60 (1,3,6,9) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Degarelix 240@40/240@60 (1,4,7,10) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Testosterone <=0.5 ng/mL at Day 28

• 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:
  • Degarelix 240@40/240@60 (1,3,6,9): 97.9% (143/146) versus 97.3% (142/146) on control; risk difference 0.7 percentage points (95% CI -2.8 to 4.2), risk ratio 1.01 (0.97–1.04); unadjusted two-proportion z-test p = 0.702.
  • Degarelix 240@40/240@60 (1,4,7,10): 97.9% (142/145) versus 97.3% (142/146) on control; risk difference 0.7 percentage points (95% CI -2.8 to 4.2), risk ratio 1.01 (0.97–1.04); unadjusted two-proportion z-test p = 0.709.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Degarelix 240@40/240@60 (1,3,6,9) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Degarelix 240@40/240@60 (1,4,7,10) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broadly reinforce the primary endpoint's overall pattern: the posted testosterone summaries do not show a sharply separated set of regimens. The separate Day 28 measure is near the top of its observed range across all three arms, while the later sustained measure has arm percentages in a range similar to the primary result. The recalculated comparisons for these binary endpoints also have intervals that include no difference. The secondary data therefore do not materially resolve the uncertainty in the primary comparison.

These endpoints address related but not identical questions. A measurement at Day 28 is a snapshot, whereas a criterion maintained after Day 28 or throughout follow-up concerns persistence. Similar patterns across related outcomes can be supportive context, but they are not independent confirmation in the same way that an unrelated outcome might be: the endpoints concern the same participants and the same underlying biological measure. The registry record does not report participant-level correlations or a plan for combining these outcomes.

The registered secondary list also includes liver function tests and markedly abnormal changes in vital signs and body weight. Detailed outcome results for those listed measures are not reported in the registry record, so they cannot contribute to a complete assessment of the secondary outcome pattern.

General explanation: secondary outcomes are often useful for understanding consistency, safety, or additional dimensions of a study, but their interpretation depends on whether they were prespecified, how many were tested, and whether the analysis accounted for multiple testing. The record does not report a hierarchy or multiplicity strategy. Unadjusted secondary results carry less weight because, across many analyses, some findings can appear notable by chance. They should be treated as supportive or exploratory unless the prespecified analysis plan establishes otherwise; that plan is not reported.

The secondary findings do not establish equivalence among regimens and do not correct the imprecision in the primary contrast. They add context about the same general suppression question, but the study's posted results leave open a range of possible differences. The absence of detailed results for some registered secondary measures further limits a broad synthesis.

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

• Number of Participants With Testosterone Level <=0.5 ng/mL After the Dose at Day 28 Until the End of the Study
• Number of Participants With Testosterone <=0.5 ng/mL at Day 28
• Liver Function Tests
• Number of Participants With Markedly Abnormal Change in Vital Signs and Body Weight as Compared to Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary, so the posted counts and percentages describe participants who met the sustained testosterone criterion. The outcome counts are 94 of 120, 101 of 127 and 110 of 129 in the three arms. The corresponding registry percentages are 78.3%, 79.5% and 85.3%. Counts identify how many participants met the criterion; denominators identify how many contributed to the arm-specific outcome. The registry record labels the population as observed cases in the ITT population, so the reported denominators should not be assumed to equal the full randomized group sizes.

The recalculated pairwise analysis expresses the contrast as a risk difference: the difference between the two arm-level proportions. A risk difference of zero would represent equal proportions under that summary. The recalculated intervals for both primary comparisons include zero, so values compatible with no difference are among the possibilities represented by the intervals. The unadjusted p-values are 0.818 and 0.155. The recalculations use posted summary counts and are not adjusted estimates from a full participant-level model.

The registry also reports sponsor analyses using the Mantel Haenszel method. General explanation: this method can compare proportions while accounting for strata, when strata have been defined. The stratification details and the precise implementation are not reported in the registry record, so the analysis cannot be reproduced from the information posted. The sponsor reports a three-group p-value and pairwise p-values. These are sponsor-reported tests and should be kept distinct from the simple unadjusted recalculations. The registry does not report a discrepancy between the posted sponsor results and the recalculations.

Confidence intervals describe a range of values compatible with the data and the interval method, under its assumptions. They convey uncertainty in a way that a single point estimate cannot. For the sponsor's arm-level percentages, the record reports intervals at 96.5%; for some secondary arm percentages, the reported level is 95%. The registry does not specify the interval method for those percentages. The recalculated comparisons have intervals, but the original trial's complete statistical analysis plan and interval specification are not reported in the registry record.

General explanation: for a binary outcome, intervals can be wide when there are few participants or when the underlying proportions make the estimate less stable. Here, the primary arm denominators range from 120 to 129. The displayed comparison intervals extend across no difference, showing that the data do not pin down the direction and size of a pairwise contrast with high precision. A p-value and an interval address related questions, but the interval also communicates which effect sizes remain compatible with the observed data.

The sample-size illustrations use the observed effect as a reference and show hypothetical planning sizes for smaller fractions of that effect. General explanation: power is the probability that a planned test will detect a specified effect under a particular design and assumptions. Those assumptions matter: allocation, significance level, outcome rates, analysis method, and the effect selected all influence a planning result. The illustrations are not evidence of the probability that this completed trial detected an effect. The registry record does not report the trial's original sample-size justification, original power target, interim analyses, or full prespecified testing plan.

Randomization supports comparisons between assigned groups, but the interpretation of a randomized study also depends on allocation procedures, follow-up, and analysis population. The record confirms randomization and an open-label design, but details of the sequence and allocation concealment are not reported in the registry record. The primary outcome is explicitly described as observed cases in the ITT population. The record does not explain how participants with incomplete testosterone measurements were handled, whether imputation was used, or whether a sensitivity analysis tested alternative missing-data assumptions.

Multiplicity is relevant because the registry reports a three-group analysis, multiple pairwise comparisons, and several outcomes. General explanation: when many hypotheses are tested, the chance of at least one small p-value can increase unless the analysis plan accounts for the number and structure of tests. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the tests. The posted p-values should therefore be read as reported for their individual comparisons, not as proof that a family-wide error rate was controlled.

The registered outcome list includes liver function tests and marked changes in vital signs and body weight, in addition to testosterone outcomes. Detailed results for every listed outcome are not reported in the registry record. That limits the extent to which the full planned outcome set can be assessed from this record.

11. Confidence Intervals and Precision

Precision is about how tightly the data locate an effect, rather than whether a point estimate happens to favor one arm. The registry's primary percentages are 78.3%, 79.5% and 85.3%, with sponsor-reported arm intervals of 69% to 86%, 71% to 87% and 77% to 91%, respectively. Those intervals are reported at 96.5%. They show substantial uncertainty around each arm's percentage and overlap in their ranges.

For the recalculated pairwise contrasts, both intervals include no difference. The comparison between the month 1, 3, 6 and 9 schedules has p = 0.818, while the comparison between the 40 mg/mL schedule and the month 1, 4, 7 and 10 schedule has p = 0.155. The posted results therefore do not identify a precise pairwise effect. The observed percentage for the latter schedule is higher, but the interval also allows values consistent with little or no contrast. The registry does not report the sponsor's pairwise effect estimates and intervals in the reported analyses.

General explanation: an interval is not a guarantee that the true value lies inside its endpoints. It summarizes sampling uncertainty under a statistical method and its assumptions. Overlap between arm-specific intervals is not itself a formal test of a difference; the pairwise comparison is more directly relevant to that question. Conversely, a p-value alone does not communicate the range of effect sizes compatible with the data. Considered together, the arm percentages, pairwise p-values and recalculated intervals indicate that the observed pattern is not estimated with enough precision to establish a clear distinction among these schedules.

The sample sizes contributing to the primary endpoint are modest relative to the very small contrasts between the first two posted percentages. The registry record does not report a precision target or a clinically important difference against which to judge the intervals. Statistical uncertainty can therefore be described, but the record does not establish whether a particular interval width would be acceptable for the study's intended decision.

12. Planning a Similar Trial: Sample Size

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

The planning figures are hypothetical illustrations based on the observed effect, not the trial's original design assumptions. For the binary outcomes, the figures are participants per arm. The stated 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 trial's original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for an analysis designed to have an 80% chance of detecting the selected effect, if the planning assumptions hold. The 90% power column gives the corresponding number for a 90% chance under those same assumptions. For example, when planning for 75% of the observed primary contrast between the 40 mg/mL regimen and the 60 mg/mL regimen scheduled at months 1, 4, 7 and 10, the illustration gives 894 participants per arm for 80% power and 1,196 per arm for 90% power.

Each set of figures is specific to the comparison and endpoint used to generate it. The displayed alternatives use 100%, 75% and 50% of the observed effect. As the effect to be detected becomes smaller, more participants are needed to distinguish it from random variation under the stated assumptions. Where the observed contrast is very small, the resulting illustrative sample sizes can be especially large.

These figures are planning illustrations, not observed power. They do not say how likely the completed study was to obtain a statistically significant result after the data were collected. The planning calculations also do not establish that the assumptions match the original protocol or the sponsor's analysis. For the event-total method used in time-to-event illustrations, figures would represent total events, but the outcomes discussed in these binary comparisons are expressed as participants per arm.

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 = 0.783; treatment proportion p₁ = 0.795; average p̄ = 0.789.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5767 = 1.1304.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5767 = 0.4853.
4. n = (1.1304 + 0.4853)² / (0.0119)² = 18,303.6, rounded up to 18,304 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 <- 0.783333333333333                          # control proportion
p1 <- 0.795275590551181                          # 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(116753)
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 = 18,304 (80% power), 24,503 (90% power)
 75% of observed effect: n per arm = 32,710 (80% power), 43,788 (90% power)
 50% of observed effect: n per arm = 73,975 (80% power), 99,031 (90% power)
power.prop.test: 18303.6 
Simulated power at n = 18,304 per arm: 0.800 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor reports arm-level percentages and Mantel Haenszel tests. For the primary endpoint, the sponsor reports 78.3%, 79.5% and 85.3%, with arm intervals at 96.5%. The pairwise sponsor p-values are 0.780 for the two schedules administered at months 1, 3, 6 and 9, 0.156 for the 40 mg/mL schedule versus the 60 mg/mL schedule administered at months 1, 4, 6 and 9 as represented by the arm descriptions, and 0.221 for the two 60 mg/mL schedules. The three-group test reports p = 0.302.

The recalculated comparisons are unadjusted calculations from posted counts. They give p = 0.818 for the first pair and p = 0.155 for the comparison with the month 1, 4, 7 and 10 schedule. The sponsor results and recalculations are not identical because they are different analyses; the registry record does not report a discrepancy. The sponsor's own analyses take precedence as the trial's reported analyses, while the recalculations offer a transparent, simple comparison based on the posted summary counts.

Both sets of results tell a broadly similar interpretive story: neither pairwise comparison provides a clear statistical separation, and the contrast with the highest observed percentage remains uncertain. The registry does not provide enough detail about stratification or other implementation choices to reproduce the sponsor's Mantel Haenszel tests independently. No adjustment for the number of comparisons is reported, so the reported p-values should not be treated as evidence that multiplicity was addressed.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports several analyses of the primary endpoint: a three-group Mantel Haenszel test and pairwise tests, alongside the arm-specific percentages. It also identifies multiple secondary outcomes and posts results for several testosterone measures. The full prespecified testing strategy, including any hierarchy among outcomes or comparisons, is not reported in the registry record.

General explanation: multiplicity arises when multiple statistical hypotheses are tested. If each test is treated as a separate opportunity to find a difference, the overall chance of at least one false positive can rise. A prespecified correction, testing sequence, or other strategy can address this, but the registry record does not report whether one was used. The sponsor p-values and recalculated unadjusted p-values should therefore be interpreted as individual test results, not as proof that the full family of analyses maintained a particular error rate.

The primary outcome is described as based on observed cases in the ITT population. That wording identifies the analysis population label and indicates that observed outcome data contribute, but the record does not define how the ITT population was constituted or how missing measurements were handled. It does not report imputation, a missing-data sensitivity analysis, reasons for missingness, or participant flow by analysis. Because the endpoint requires all testosterone values over follow-up to satisfy a threshold, the handling of incomplete measurement sequences could matter to the resulting count.

The trial is randomized and open label, but the record does not report random sequence generation, allocation concealment, or additional procedures intended to limit bias. It also does not report interim analyses, stopping rules, or the trial's original sample-size justification. These omissions do not show that the procedures were absent; they mean that their use cannot be assessed from the registry record.

General explanation: a registry outcome record is not a substitute for a full protocol and statistical analysis plan. Without those documents, readers cannot determine whether all prespecified outcomes and analyses are reported, whether deviations occurred, or how the testing strategy was set before results were known. This limits confidence in claims about confirmatory status beyond what the record explicitly states.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: urinary retention (2.7%), abdominal pain (1.4%), coronary artery disease (1.3%), acute myocardial infarction (1.3%), myocardial infarction (1.3%).

The safety counts distinguish serious adverse events from other adverse events. In the three groups, the numbers reported at risk for serious events are 150, 150 and 147; the numbers affected are 28, 25 and 19. For other adverse events, the numbers at risk are again 150, 150 and 147, with 117, 110 and 107 affected. These are counts of participants with events, not event totals, and the registry does not provide comparative statistical tests for these figures.

The registry lists urinary retention at 2.7% among the most frequent serious adverse-event terms, followed by abdominal pain at 1.4%, coronary artery disease at 1.3%, acute myocardial infarction at 1.3%, myocardial infarction at 1.3%, and constipation at 1.3%. These terms describe reported serious events; they do not establish that the study drug caused them. The record does not give arm-specific frequencies for these listed terms in the registry record for this analysis.

Deaths are not reported in the registry record. The safety counts should be read descriptively: the groups have different numbers at risk, and the record does not report exposure-adjusted rates, event timing, severity details beyond the serious-event distinction, or a statistical comparison. The figures alone do not support conclusions about comparative safety.

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

The posted primary results show that substantial proportions of participants in each arm met the sustained testosterone criterion from Day 28 to the end of follow-up. The observed percentages range from 78.3% to 85.3%. The highest percentage is in the 60 mg/mL maintenance schedule administered at months 1, 4, 7 and 10. The two regimens administered at months 1, 3, 6 and 9 have close observed percentages.

The pairwise comparisons do not establish a clear difference. Their recalculated intervals include no difference, and the reported p-values do not provide evidence of a well-resolved contrast. This does not show that the regimens are equivalent: the registry does not report an equivalence or non-inferiority margin, and the intervals permit uncertainty about the direction and size of the differences.

The results also do not establish that any regimen is clinically preferable. The endpoint is a biochemical measure with a defined threshold and follow-up interval. The registry record does not provide evidence connecting differences in this endpoint to patient-centered outcomes, nor does it report enough information to assess all eligibility criteria, missing data, or the full statistical plan. The record's rationale concerns testosterone suppression and safety, but that rationale should not be extended to outcomes not reported.

General explanation: a failure to detect a statistically clear difference is not proof of no difference. Likewise, a higher observed proportion in one group does not by itself demonstrate a reliable or clinically important advantage. The size and precision of the estimated contrast, the analysis plan, measurement completeness, and relevant clinical context all affect interpretation. Here, the registry results support a descriptive comparison of three schedules, while leaving substantial uncertainty about their comparative effects.

The posted safety counts give additional descriptive information, but they do not establish causation or comparative safety. Taken together, the record supports a cautious account of what was measured and observed; it does not justify claims beyond the registered outcome data and the analyses reported.

18. Why This Trial Matters Statistically

This trial illustrates why a three-arm randomized comparison requires more than comparing the largest observed percentage with the other percentages. The primary endpoint is a sustained binary outcome, and the arm estimates are accompanied by uncertainty. The recalculated pairwise analyses show that the observed differences are not precisely resolved, even though one regimen has a higher posted percentage.

It also illustrates the value of distinguishing sponsor-reported analyses from unadjusted recalculations. The sponsor reports Mantel Haenszel tests, while the recalculations compare posted counts directly. These approaches answer related but not identical statistical questions. Reporting both without treating them as interchangeable makes clear which results come from the trial's reported analysis and which are simple calculations from summary data.

Several design and reporting issues matter for biostatistical interpretation: an open-label study, an observed-cases description within the ITT population, multiple pairwise comparisons and secondary outcomes, and limited registry detail about missing data and multiplicity. These factors do not invalidate the results, but they limit how confidently the estimates can be generalized or treated as definitive.

The sample-size illustrations are another useful teaching point. Planning figures based on an observed effect can become very large when that effect is small, and they depend on assumptions that may not match the original study design. They are not a retrospective measure of the study's power. The original design rationale is not reported in the registry record.

Overall, the study provides a concrete example of how endpoint definition, analysis population, confidence intervals, and multiplicity shape the interpretation of a randomized trial. The results are most informative when read as estimates with uncertainty, rather than as a ranking of regimens based on point estimates alone.

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.

The main limitation of this registry-based account is incomplete methodological detail. The record identifies a randomized, open-label, parallel-group study, but does not report the randomization sequence method, allocation concealment, or the original sample-size justification. The full protocol and statistical analysis plan are not reported, so prespecification and analysis choices cannot be fully evaluated.

The primary outcome is based on observed cases in the ITT population, but missing-data handling is not described. This matters because the endpoint requires all values from Day 28 through the end of follow-up to meet the threshold. The record does not explain how incomplete measurement sequences were classified, whether participants with missing values were excluded, or whether sensitivity analyses were conducted.

The trial is open label. The primary endpoint is based on a laboratory measurement, but the registry record does not report laboratory procedures, measurement schedules in detail, or whether laboratory assessment was blinded. The recorded follow-up timeframe spans 12 or 13 months, and further reasons for this variation are not reported.

Multiple outcomes and comparisons are reported, while the multiplicity strategy is not. Detailed results for every registered secondary outcome are not reported in the registry record. The sponsor's Mantel Haenszel analyses cannot be fully reproduced because the stratification and implementation details are not provided. The recalculations use summary counts and do not replace participant-level or adjusted analyses.

Finally, the posted outcome denominators differ from the overall enrollment figure and vary across outcomes. The record does not explain those differences in this summary, and arm-specific participant flow is not reported. The available data therefore support a descriptive statistical reading, but not a complete audit of trial conduct, missingness, or analysis decisions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Comparative Study of Degarelix Three-month Depot in Three Different Dosing Regimens in Patients With Prostate Cancer — NCT00116753.
• Registry record last updated 2010-12-10; status last verified 2010-11.
• Results first posted 2010-12-10.
• 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

This completed phase 2 study randomized 460 patients with prostate cancer to three open-label, parallel degarelix dosing regimens. The primary outcome counted participants whose testosterone values remained at or below 0.5 ng/mL from Day 28 through 12 or 13 months, using observed cases in the ITT population.

The registry reports arm percentages of 78.3%, 79.5% and 85.3%. Recalculated pairwise comparisons do not establish clear differences, and the sponsor's reported analyses likewise do not show a clear separation among the regimens. The posted safety data are descriptive and do not include comparative tests. Important details about missing data, multiplicity, and the original sample-size rationale are not reported in the registry record.