Symptomatic Study Investigating Degarelix in Patients Suffering From Prostate Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Symptomatic Study Investigating Degarelix in Patients Suffering From Prostate Cancer (NCT00831233), a randomized phase 3 study. The primary outcome is Change From Baseline in Total International Prostate Symptom Score (IPSS) at Week 12.

2. Clinical Question

The clinical question is about the relative change in reported urinary symptom scores over the treatment period, not about prostate cancer control or survival. The registry description notes that lower urinary tract symptoms can affect normal urination and quality of life, and identifies IPSS as the primary measure used to evaluate symptom severity. It is a questionnaire-based endpoint rather than a direct measure of urine flow, prostate size, or cancer progression.

The registry record reports a randomized comparison, but does not report the reason the trial was terminated. It also does not report the trial's original sample-size justification or the detailed eligibility criteria in the information available for these results. Those omissions limit what can be inferred about the intended scope and representativeness of the comparison.

3. Trial Design

This was a phase 3, randomized, parallel-arm, open-label trial sponsored by Ferring Pharmaceuticals. The record lists an enrollment of 42 and a status of terminated. The recorded start was 2009-04 and primary completion was 2010-06. The registry record does not report why the trial was terminated, and no reason should be inferred from the status alone.

Participants were assigned to degarelix or goserelin plus bicalutamide. The treatment period described in the registry was 3 months, with urinary symptoms assessed by a patient-completed questionnaire. The primary endpoint was change from baseline in total IPSS at Week 12. The primary outcome description identifies the Full Analysis Set and Per Protocol Analysis Set and says that Last Observation Carried Forward was used. The record does not give further details about how participants entered each analysis population or how missing measurements were handled beyond that label.

The posted primary outcome summaries include 27 participants in the degarelix arm and 13 in the goserelin-plus-bicalutamide arm. Those outcome-specific counts should not be treated as a report of the number randomized to each arm, because the registry record does not make that equivalence clear. The original allocation counts and reasons for any difference between enrollment and outcome analyses are not reported in the registry record.

Open-label means masking was not used. The registry record does not report whether any other procedures were used to limit bias in outcome collection or analysis. Because the primary measure is a self-completed symptom questionnaire, knowledge of assigned treatment is relevant context when considering how the results were obtained, without establishing that any particular bias occurred.

The record lists additional outcomes involving IPSS at earlier visits, urine flow, residual volume, prostate size, testosterone, PSA, urinary symptom-related quality of life, and abnormal vital signs or body weight. Not all of those outcomes have numerical results available in the posted information. The original statistical analysis plan, trial-specific interim analysis procedures, and trial-specific sample-size assumptions are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) + Per Protocol (PP) Analysis Set, Last Observation Carried Forward (LOCF).

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 Change From Baseline in Total International Prostate Symptom Score (IPSS) at Week 12, measured over After treatment of 12 weeks compared to Baseline.

The primary endpoint is change from baseline in total International Prostate Symptom Score at Week 12, after treatment of 12 weeks compared with baseline. IPSS is a patient-completed questionnaire with 7 questions addressing incomplete emptying, frequency, intermittency, urgency, weak stream, straining, and nocturia. Each question receives a score from 0 to 5, and the total score is used to classify symptom severity: 0 to 7 is mild, 8 to 19 is moderate, and 20 to 35 is severe.

As a continuous outcome, the registry reports the mean change and standard deviation for each arm. A negative change means the recorded score at follow-up was lower than the baseline score. The measure is used to assess urinary symptom severity and monitor change after treatment begins. It captures a patient's reported experience across several urinary symptoms, rather than an objective physiological measure such as maximum urine flow or residual urine volume.

The registry record specifies that the primary endpoint was assessed at Week 12 and identifies a Full Analysis Set and Per Protocol Analysis Set with Last Observation Carried Forward. It does not report enough detail to determine how the final reported arm summaries relate to each named population or whether results for both populations were separately posted. The score is clinically relevant to the symptom question, but a change in the mean alone does not show how individual participants changed or how many moved between symptom severity categories.

7. Results Posted in the Registry

• Goserelin (3.6 mg) + Bicalutamide (50 mg): mean -7.69 versus -11.20 on control; difference 3.51 (95% CI -1.68 to 8.70), standardized effect d = 0.43; z-test p = 0.185.

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.

Change From Baseline in Prostate Size Based on Trans Rectal Ultra Sound (TRUS) at Week 12

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Goserelin (3.6 mg) + Bicalutamide (50 mg): mean -13.40 versus -22.40 on control; difference 9.00 (95% CI 0.80 to 17.20), standardized effect d = 0.66; z-test p = 0.032.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Goserelin (3.6 mg) + Bicalutamide (50 mg) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists a range of secondary outcomes, covering symptom scores at earlier visits, measures of urine flow and residual volume, prostate size, testosterone, PSA, urinary symptom-related quality of life, and abnormal vital signs or body weight. Numerical results are not reported for every listed outcome in the information available. As a result, an overall pattern across the secondary outcomes cannot be established from the registry record.

The posted numerical secondary result for prostate size at Week 12 reports mean changes of -22.4 mL for degarelix and -13.4 mL for goserelin plus bicalutamide. The unadjusted recalculation gives a mean difference of 9.0, with a 95% confidence interval from 0.797 to 17.2 and p = 0.032. The sponsor ANCOVA result for this outcome reports -7.83, with a 95% confidence interval from -17.3 to 1.64 and p = 0.102. These analyses differ, so the recalculated secondary contrast should not be taken as a definitive sponsor conclusion.

The secondary outcomes provide context around the primary symptom question, but they do not replace the primary endpoint. Measures such as prostate size, urine flow, and PSA address different aspects of health and have different scales. A result on one of them cannot be treated as confirmation of the IPSS comparison without a prespecified analysis plan and a clear account of how the outcomes relate.

Unadjusted secondary findings generally carry less weight when many outcomes or comparisons are examined, because the chance of finding an apparently unusual result can rise across repeated testing. This is a general statistical concern, not evidence that a particular finding is false. The registry record does not report a multiplicity adjustment or analysis hierarchy. Together with the lack of numerical results for most listed secondary outcomes and the difference between sponsor and recalculated results, that limits confidence in broad claims based on secondary findings.

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

• Change From Baseline in Total IPSS at Weeks 4 and 8
• Change From Baseline in Maximum Urine Flow (Qmax) at Each Visit
• Change From Baseline in Residual Volume (Vresidual) at Each Visit
• Change From Baseline in Prostate Size Based on Trans Rectal Ultra Sound (TRUS) at Week 12
• Number of Participants With Testosterone <=0.5 Nanograms/Milliliter at Each Visit
• Percentage Change From Baseline in Prostate-specific Antigen (PSA) Concentration at Each Visit
• Change From Baseline in Quality of Life (QoL) Related to Urinary Symptoms at Each Visit
• Number of Participants With Markedly Abnormal Values in Vital Signs and Body Weight

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish what the posted primary results say from what they do not say. The main reported endpoint is a continuous score, and the registry gives an arm mean and standard deviation. A mean describes the average change in that arm, while the standard deviation describes how dispersed individual changes are around that average. A mean does not imply that each participant had a change close to it; the standard deviation is useful context for that variation.

What does the unadjusted recalculation compare?

The recalculated comparison uses the two posted arm means and standard deviations to estimate a difference in mean change. It is unadjusted: it does not incorporate participant-level records, baseline covariates, or the sponsor's ANCOVA model. The posted estimate is 3.51, with a 95% confidence interval from -1.676 to 8.696. The direction follows comparator minus degarelix, so a positive value corresponds to a more negative mean change in the degarelix arm. This is a descriptive contrast derived from summary statistics, not a substitute for the sponsor's own analysis.

The recalculation also uses an unadjusted p-value of 0.185. A p-value measures how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. A p-value above a conventional threshold does not prove equality. The confidence interval is more informative about the range of effect sizes compatible with the recalculation.

Why can an ANCOVA estimate differ?

ANCOVA is a method for comparing outcomes while accounting for baseline values and potentially other covariates specified in the model. Its estimate can differ from a direct comparison of change scores because the statistical model and the information used are not the same. The registry reports two ANCOVA results for final values, but does not report enough model detail to reconstruct them or explain why two estimates appear. The recalculation should therefore be understood as a separate, unadjusted calculation, not as a correction to or replacement for the sponsor analysis. Because the record identifies a discrepancy, the sponsor's own analysis takes precedence.

The posted sponsor results include estimates, confidence intervals, and p-values. A confidence interval describes uncertainty around an estimate under the assumptions of the model. When an interval includes zero for a mean difference, it is compatible with no difference as well as with differences in either direction. The sponsor's two intervals do not have the same relation to zero, which is another reason not to reduce the record to a single yes-or-no statement. The registry does not report the context needed to determine why their estimates differ.

What do standard deviations and unequal arm sizes mean?

Standard deviations describe the spread of individual outcomes, not the uncertainty in the mean itself. The recalculation uses the arm sample sizes and standard deviations to estimate uncertainty in the difference. Unequal arm sizes affect the precision of a comparison; an arm with fewer observations generally contributes less precise information, all else being equal. These principles are general statistical explanations. They do not establish that any particular design feature caused the results seen in this trial.

Over-dispersion is a general concern when the observed variation is larger than a model assumes. If an analysis underestimates variability, its standard errors may be too small and its intervals too narrow. The posted primary outcome is analyzed as a continuous measure with reported standard deviations; there is no indication in the registry record that an over-dispersion adjustment was required or used. It would therefore be inappropriate to claim that over-dispersion affected these results.

Why are planning calculations separate from observed results?

The sample-size illustrations use the observed effect and stated planning assumptions to describe how many participants per arm might be needed for chosen power targets under a simplified model. They are not estimates of the trial's achieved power. Achieved or observed power is not a useful replacement for reading the estimate and its confidence interval, and the registry does not report an original trial design calculation. The planning values answer a hypothetical question about future study sizes under their stated assumptions, not whether this trial was adequately designed or whether its result is true.

Finally, analysis populations and missing data matter. The record names both Full Analysis Set and Per Protocol Analysis Set and says Last Observation Carried Forward. LOCF carries a participant's last available measurement forward to a later assessment under the chosen analysis procedure. This can make assumptions about the course of a participant's outcome after the last observed measurement. The record does not describe the amount or pattern of missing data, whether the two populations gave different results, or sensitivity analyses. Those unknowns limit assessment of robustness.

11. Confidence Intervals and Precision

The recalculated mean difference in primary IPSS change is 3.51, with a 95% confidence interval from -1.676 to 8.696. A confidence interval gives a range of values reasonably compatible with the observed data under the calculation's assumptions; it is not a guarantee that the true value lies in that particular interval. Here, the range includes zero and extends to either side. It therefore does not pin down whether the mean changes differ or how large a difference may be.

The width of an interval reflects both the observed variability and the amount of information available. The primary arm summaries have different participant counts, and the standard deviations show substantial spread around the means. Those features contribute to uncertainty, though the interval alone does not identify the cause of any particular imprecision. The trial's outcome-specific counts are 27 and 13, as reported for these summaries.

The sponsor reports a 95% interval from -7.51 to 1.61 for one ANCOVA estimate and a 95% interval from -11.5 to -0.291 for another. The first includes zero; the second does not. Because the registry record does not explain the distinction between these two analyses, their differing precision and relation to zero cannot be resolved from the reported information. They are sponsor-reported analyses and should be kept distinct from the unadjusted recalculation of mean change.

Confidence intervals describe statistical uncertainty, not clinical importance. The registry record does not report a threshold for a clinically important between-arm difference in IPSS, so the interval cannot be classified against such a threshold. Nor do these intervals describe the range of individual participant responses. The arm standard deviations provide information about variation, but individual outcome distributions are not reported.

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 planning figures are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts; the event-count convention applies to time-to-event outcomes, whereas this endpoint is continuous. The registry's planning 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 set as a stated fraction of the observed effect.

For each effect assumption, the 80% power column indicates the number of participants per arm that the planning calculation would require to have an 80% chance of detecting that effect under the stated assumptions, if the modeled effect and assumptions were correct. The 90% power column has the analogous interpretation for a 90% chance. These are design-planning concepts, not descriptions of what happened in the trial. The original trial-specific sample-size assumptions and justification are not reported in the registry record.

The rows consider planning for 100%, 75%, and 50% of the observed effect. A smaller target effect requires more participants because a smaller difference is harder to distinguish from random variation. This relationship is general; the calculated figures remain conditional on the specified planning assumptions and the observed estimate used as their starting point.

These figures are not observed power. They do not show the probability that the trial's result is correct, nor do they repair uncertainty in the observed estimate. The observed estimate itself may be imprecise, and planning calculations based on it can therefore be uncertain too. The proper reading is as an illustration of sample sizes under hypothetical future-study assumptions, not a claim about the trial's adequacy or a recommendation for a future study.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 3.510; pooled standard deviation σ = 8.081.
2. n = 2 × (1.96 + 0.842)² × 8.081² / 3.510² = 83.2, rounded up to 84 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
delta <- 3.51                      # observed difference in means
sigma <- 8.08144691317875                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(831233)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 84 (80% power), 112 (90% power)
 75% of observed effect: n per arm = 148 (80% power), 199 (90% power)
 50% of observed effect: n per arm = 333 (80% power), 446 (90% power)
power.t.test: 84.2 
Simulated power at n = 84 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 reports two sponsor ANCOVA analyses comparing final values. One reports a mean difference of -2.95, with a 95% confidence interval from -7.51 to 1.61 and p = 0.197. The other reports a mean difference of -5.88, with a 95% confidence interval from -11.5 to -0.291 and p = 0.040. Both are labeled ANCOVA and mean difference in final values, but the registry record does not explain how the analyses differ or why both are reported.

The unadjusted recalculation instead compares the posted mean changes from baseline and gives an estimate of 3.51, a 95% confidence interval from -1.676 to 8.696, and p = 0.185. These are not identical estimands or methods: the recalculation uses summary changes, whereas the sponsor's estimates come from ANCOVA of final values. The registry record does not provide the model specifications or participant-level data needed to reconcile them.

Because the posted sponsor analysis and the recalculation do not agree, the sponsor's own analysis takes precedence. The recalculation remains useful as a transparent comparison from the arm summaries, but it should not be represented as the trial's official adjusted result. The two sponsor estimates should also be reported with their distinction unresolved rather than selecting one without support from the record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when analyses test more than one outcome, comparison, time point, or population. Without a plan to account for those repeated opportunities, nominal p-values can overstate how strong the total evidence is. The registry record lists multiple secondary outcomes and reports multiple sponsor analyses for the primary outcome, but it does not report a multiplicity strategy, testing hierarchy, or which outcomes were designated confirmatory beyond identifying the primary endpoint.

That omission matters most when interpreting isolated p-values, particularly among secondary analyses. It does not mean the reported values are invalid; it means the registry does not establish whether their interpretation was adjusted for the full set of analyses. The trial's statistical analysis plan and any prespecified procedures for controlling multiplicity are not reported in the registry record.

The primary endpoint description names both the Full Analysis Set and Per Protocol Analysis Set and specifies Last Observation Carried Forward. It does not provide separate result details for those populations or explain whether the reported summary represents both. The exact definitions of the populations, exclusions, and handling of deviations are not reported in the registry record. Therefore, the robustness of the result across analysis populations cannot be assessed from the posted information.

LOCF uses a participant's last recorded outcome as the value for a later time point when the later outcome is unavailable. As a general method, this can impose an assumption that the outcome remains at its last observed level; whether that assumption is appropriate depends on why data are missing and how outcomes evolve. The registry record does not report how many outcomes were missing, why they were missing, the pattern of missingness, or whether alternative missing-data analyses were performed. It is not possible to judge the impact of missing data from the LOCF label alone.

The record also does not report interim analyses, stopping rules, or the original sample-size rationale. Those features should not be inferred from the terminated status. Without this information, readers cannot determine whether particular analysis choices or stopping decisions were prespecified. These are reporting limitations, not proof that the trial's conduct or analysis was inappropriate.

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: hepatic failure (7.7%), prostate cancer (7.7%), renal failure (7.7%), prostatic obstruction (7.7%).

The serious adverse event figures report 0 affected participants among 27 at risk in the degarelix arm and 1 among 13 at risk in the goserelin-plus-bicalutamide arm. These are counts of participants with a serious adverse event, not rates of all adverse experiences. The registry record also lists hepatic failure, prostate cancer, renal failure, and prostatic obstruction as top serious-event terms, each at 7.7%. The record does not provide the participant counts corresponding to each listed term in the information.

For other adverse events, the posted figures are 14 of 27 in the degarelix arm and 7 of 13 in the comparator arm. These figures describe participants affected, but the record does not provide further detail in this summary about event severity, duration, or attribution. The number of deaths is not reported in the registry record.

These small outcome-specific groups do not support a precise comparative safety estimate. Counts can be sensitive to a small number of events, and the registry record does not report a formal between-arm safety comparison. The figures should be read as descriptive safety reporting, not as proof of a difference or of equivalence between the regimens.

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

The posted data describe average change in a patient-reported urinary symptom score during a 12-week treatment period. Both primary arm means indicate a lower IPSS at follow-up than baseline. The simple unadjusted comparison is imprecise, with a confidence interval that includes zero. The sponsor's own analyses give two ANCOVA estimates that do not tell the same statistical story, and the registry record does not explain the difference between them. Those features argue for a restrained interpretation.

The numbers do not establish that the two regimens have identical effects, nor do they establish a reliable advantage for either regimen. A non-significant comparison is not evidence of equivalence unless the study was designed and analyzed to support an equivalence conclusion with an appropriate margin. Although the sponsor analyses are labeled non-inferiority or equivalence, the relevant margin and the analysis distinctions are not reported in the registry information available. The posted values alone do not allow a full assessment of an equivalence claim.

Likewise, a p-value below a conventional threshold in one reported analysis does not by itself establish a clinically meaningful difference. The confidence interval, the analysis method, the existence of two sponsor estimates, and the lack of a reported multiplicity plan all matter. The record does not report a threshold for a clinically important IPSS difference between arms, so statistical estimates cannot be translated into a claim about clinical importance.

The endpoint is symptom-focused. It does not directly answer whether cancer progression changed, whether participants lived longer, or whether effects persisted beyond the reported treatment period. The registry lists other outcomes, but the available numerical results are incomplete. The trial's terminated status is recorded, but its reason is not reported; termination should not be treated as evidence for or against a particular result.

The most defensible reading is therefore specific: the posted means show decreases in IPSS in both arms, while the comparative estimate remains uncertain and sponsor analyses require clarification. These are trial results, not individual treatment guidance. They cannot determine what an individual patient should receive or predict an individual's response.

18. Why This Trial Matters Statistically

This trial raises several important statistical issues for clinical research. First, its primary outcome is patient-reported and continuous, so a mean change is an efficient summary but can conceal substantial variation among participants. The standard deviations and confidence interval help show why an average alone is insufficient to characterize the evidence.

Second, the record makes it possible to distinguish an unadjusted reconstruction from the sponsor's adjusted analysis. The recalculation is based on arm-level change summaries, while the sponsor reports ANCOVA comparisons of final values. Those methods need not produce the same estimate. Explicitly separating them prevents an accessible calculation from being mistaken for the trial's official result. Here the difference is consequential because the posted sponsor analyses themselves include two estimates that are not explained by the record.

Third, sample size and precision matter in interpreting the comparison. Outcome-specific participant counts are limited and unequal, and the interval around the unadjusted estimate covers a broad range. A lack of clear statistical separation should not be converted into proof of equality. Conversely, a nominally significant result among several analyses should not be treated as decisive without knowing the analysis plan and multiplicity handling.

Finally, the record demonstrates why registry results need interpretive context: a terminated status without a stated reason, named analysis populations without separate results, LOCF without missingness details, and multiple sponsor estimates all leave questions unanswered. These are not grounds to dismiss the results, but they define the boundaries of what can be concluded. Good statistical interpretation reports both the observed estimates and the uncertainties that remain.

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.

Several limitations specific to this trial constrain interpretation. The record lists the study as terminated but does not report the reason. It does not report the original sample-size justification, so the adequacy of the planned enrollment cannot be assessed from the registry information. The sample-size illustrations are based on the observed effect and should not be confused with original design calculations.

The primary outcome summaries are based on different participant counts in the two arms, and the record does not explain how those counts relate to enrollment, randomization, or the named Full Analysis Set and Per Protocol Analysis Set. It also does not give separate outcomes for the two populations. Consequently, the impact of exclusions or differences between analysis populations cannot be evaluated.

Missing-data reporting is limited to the LOCF label. The amount and pattern of missing outcomes, reasons for missingness, and sensitivity analyses are not reported in the registry record. The record also does not provide the detailed ANCOVA specification or explain why two sponsor analyses of final values are reported. This prevents a direct reconciliation with the unadjusted recalculation.

The trial was open-label, and the primary endpoint was completed by participants as a symptom questionnaire. This is relevant context for a subjective outcome, although the record does not show that reporting bias occurred. The registry does not report a multiplicity procedure despite listing several secondary outcomes and multiple analyses. Numerical results are also unavailable for most listed secondary measures in the reported information.

Finally, the short described treatment period and the symptom-focused endpoint restrict the scope of the results. The record does not establish longer-term effects, cancer outcomes, or a clinically important difference threshold for IPSS. These limitations counsel against broad conclusions beyond the reported symptom-score summaries.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Symptomatic Study Investigating Degarelix in Patients Suffering From Prostate Cancer — NCT00831233.
• Registry record last updated 2013-11-11; status last verified 2013-10.
• Results first posted 2011-08-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a randomized, parallel-arm, open-label phase 3 trial comparing degarelix with goserelin plus bicalutamide in patients with lower urinary tract symptoms secondary to locally advanced prostate cancer. Enrollment is listed as 42, and the trial status is terminated. The treatment period was 12 weeks, and the primary endpoint was change from baseline in total IPSS at Week 12.

The primary arm summaries report mean changes of -11.2 and -7.69. An unadjusted recalculation estimates a mean difference of 3.51, with a 95% confidence interval from -1.676 to 8.696 and p = 0.185. The sponsor reports two ANCOVA analyses of final values, with different estimates and p-values; the registry record does not explain the distinction. Because of this discrepancy, the sponsor's analysis takes precedence over the recalculation.

The record names the Full Analysis Set and Per Protocol Analysis Set, specifies LOCF, and lists multiple secondary outcomes. Important details—including the termination reason, original sample-size assumptions, missing-data patterns, analysis specifications, and multiplicity procedures—are not reported in the registry record.