Maintaining Suppression of Testosterone With Transdermal Estradiol Gel: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Maintaining Suppression of Testosterone With Transdermal Estradiol Gel (NCT02349386), a randomized phase 2 study. The primary outcome is Maintenance of Testosterone Suppression at Week 12.

2. Clinical Question

The study was a dose-finding evaluation of three BHR-200 doses against placebo. The clinical question is therefore not only whether the posted outcome differed by treatment group, but also how the observed counts should be interpreted in light of the endpoint definition and the limited reporting. The registry gives counts for each arm, but does not report a statistical comparison or an uncertainty interval for those results.

3. Trial Design

This was a Phase 2, randomized, quadruple-masked, parallel-group, placebo-controlled study. The registry lists an enrollment of 34 and identifies the condition as cancer of the prostate. It describes the study objective as evaluating the safety and efficacy of three doses of BHR-200 for maintaining testosterone suppression in men with advanced androgen-sensitive prostate cancer.

Participants were assigned to low-, mid-, or high-dose BHR-200, or to placebo. The active gel was 0.36% transdermal 17β-estradiol. The low-dose regimen was 3 mg estradiol per 1 mL, the mid-dose regimen was 6 mg per 2 mL, and the high-dose regimen was 9 mg per 3 mL. Each was applied daily to the skin for up to 52 weeks. The placebo regimen used 1, 2, or 3 mL of gel containing 0 mg estradiol, also applied daily for up to 52 weeks.

The primary outcome was assessed at Week 12. A secondary outcome concerned maintenance of testosterone suppression at Week 24, and another concerned patients reporting thromboembolic adverse events. The registry lists 8 outcome measures and 2 secondary outcomes. It records a study start of 2015-07, primary completion on 2017-06-14, and a terminated status. The reason for termination is not reported in the registry record.

The registry does not report how randomization was generated, how treatment assignments were concealed, or how masking was implemented. It also does not report the planned allocation ratio, the intended number of participants in each arm, or why the study was terminated. The posted design information identifies the broad structure of the trial but does not supply enough detail to assess these operational features.

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.

24-Week Double-Blind Main Study

Reasons for not completing this period:

28-Week Double-Blind Optional Extension

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intent-to-treat (ITT) population contains all patients who are randomized into the study. All efficacy parameters were analyzed using the ITT population. In the case of a patient who was randomized but did not take the study drug, the analysis was done for this patient using the randomized treatment.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Safety Population

6. Primary Endpoint

The registry lists the primary outcome as Maintenance of Testosterone Suppression at Week 12, measured over Week 12.

The primary outcome is titled maintenance of testosterone suppression at Week 12, and its unit is participants. The endpoint description frames the primary efficacy endpoint as the percentage of patients failing to maintain castrate testosterone levels, defined as testosterone below 50 ng/dL. It defines suppression as the absence of any testosterone measurement over 50 ng/dL during Weeks 4 to 12. Thus, the assessment depends on whether any measurement crossed the stated threshold during that interval, rather than only on a single reading at Week 12.

A threshold-based endpoint turns repeated laboratory measurements into a binary classification: a participant either meets the stated suppression definition or does not. Counts can be useful for describing how many participants in each arm met the recorded outcome, but they do not show how close individual measurements were to the threshold, how measurements changed over time, or how often measurements were taken.

The registry reports participant counts by arm for the primary measure. It does not provide an uncertainty interval or a statistical comparison for those counts. The endpoint description refers to a percentage failing to maintain suppression, while the posted measure is reported as counts; percentages should not be inferred from the counts when they are not reported. The clinical interpretation also depends on the endpoint’s direction: the description focuses on failure, while the outcome title refers to maintenance. The record does not provide further clarification about that presentation.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Statistical methods help distinguish a descriptive result from an estimate of a treatment contrast. The registry presents primary-outcome counts by arm, but reports no analyses for the outcome. No test, effect estimate, confidence interval, or adjustment is reported in the registry record. The arm-specific values can be described as posted, but they should not be presented as though a formal comparison had been conducted.

What does a binary endpoint represent?

As a general statistical concept, a binary endpoint places each participant into one of two outcome categories according to a defined rule. In this study, the stated suppression rule is based on whether any testosterone measurement exceeded 50 ng/dL during Weeks 4 to 12. Such a rule makes the clinical measurement easier to summarize as a count, but it discards detail about the actual measurement values and their trajectory. Two participants in the same category could have had very different patterns of testosterone measurements.

The count is useful for describing the recorded outcome within an arm. To compare arms statistically, an analysis would also need to define the contrast of interest and account for the uncertainty that arises from observing only a limited number of participants. The registry record does not report such a contrast or its uncertainty. It would therefore be inappropriate to derive and report a new comparative estimate from the counts in this explanatory text.

Why does uncertainty matter?

In general, a confidence interval describes a range of values compatible with the observed data under a specified model and method. Its width reflects precision: a wider interval indicates less precision, while a narrower interval indicates more precision. The registry does not report confidence intervals for the primary outcome. As a result, readers cannot use the posted results to assess the precision of a treatment comparison from an interval estimate.

A p-value, in general, summarizes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the model assumptions were true. It is not an estimate of effect size and does not measure the probability that a treatment works. No p-value or statistical test is reported for the primary outcome in the registry record. The absence of a reported test means that the displayed counts should not be described as statistically significant or non-significant.

What does the sample-size material mean?

The planning illustrations use the observed effect as a starting point and consider detecting a stated fraction of that effect. Their stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For non-time-to-event outcomes, the planning quantity is participants per arm. These are planning illustrations, not a report of the study’s original sample-size design and not observed power. The registry record does not report the trial’s own sample-size justification or statistical plan.

In general, a sample-size calculation describes how many participants may be needed to detect a specified effect under stated assumptions. Its result depends on the target effect, the variability or event frequency, the analysis method, and the chosen error rates. A calculation based on an observed effect can be especially sensitive to that estimate; it does not establish that the completed study had a particular probability of detecting an effect. No specific planning result is described because no sample-size values are reported in the registry record.

How should masking and allocation be interpreted?

The registry identifies the study as randomized, quadruple-masked, and parallel-group. In general, randomization is intended to reduce systematic differences between treatment groups, while masking is intended to limit the influence of treatment knowledge on participants, clinicians, or outcome assessment. The record does not specify who was included in the masking description, how randomization was generated, or how allocation concealment was handled. The labels alone do not answer those implementation questions.

A parallel-group design assigns participants to a study group and compares outcomes across groups. The listed groups were three BHR-200 dose regimens and placebo. The registry’s description identifies the study as dose-finding, but does not report a dose-response model or a statistical procedure for evaluating trends across doses. No particular trend analysis should be inferred from the presence of multiple dose groups.

What can be said about the analysis population?

The registry says efficacy parameters were analyzed using the intent-to-treat population and describes that population as all patients randomized into the study. It also states that a randomized patient who did not take study drug was analyzed according to randomized treatment. In general, an intent-to-treat approach seeks to preserve the comparison created by randomization. However, the available description is incomplete and does not explain how missing Week 12 measurements, withdrawals, or other post-randomization circumstances were handled.

The registry lists 0 analyses. This does not mean that no statistical work was performed outside the posted record; it means that inferential results are not available in the registry information. The analysis plan, outcome-level methods, multiplicity procedure, and missing-data assumptions are not reported in the registry record. Consequently, method-specific conclusions about robustness, model fit, or adjusted comparisons cannot be made.

10. Exact Estimates for Each Arm

No two-arm comparison is shown for this trial, but each arm's result can still be summarized with exact interval estimates computed from the posted counts. The Clopper-Pearson interval is exact and conservative; the Wilson interval is a common closer-to-nominal alternative; the Bayesian credible interval uses a uniform Beta(1, 1) prior. For small groups the three can differ noticeably.

R code and output

arm    <- c("BHR-200 Low Dose", "BHR-200 Mid Dose", "BHR-200 High Dose", "Placebo")
n      <- c(8, 8, 8, 7)
events <- c(3, 3, 5, 2)
for (i in seq_along(n)) {
  ci <- binom.test(events[i], n[i])$conf.int          # Clopper-Pearson exact interval
  cr <- qbeta(c(0.025, 0.975), 1 + events[i], 1 + n[i] - events[i])   # Bayesian, uniform Beta(1,1) prior
  wi <- (function(x, n) { p <- x / n; z <- qnorm(0.975); d <- 1 + z^2 / n
    c((p + z^2 / (2 * n) - z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d, (p + z^2 / (2 * n) + z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d) })(events[i], n[i])
  cat(sprintf("ARM|%s|%d|%d|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f\n", arm[i], n[i], events[i], 100 * events[i] / n[i],
              100 * ci[1], 100 * ci[2], 100 * wi[1], 100 * wi[2], 100 * cr[1], 100 * cr[2]))
}

ARM  BHR-200 Low Dose  8  3  37.5  8.5  75.5  13.7  69.4  13.7  70.1
ARM  BHR-200 Mid Dose  8  3  37.5  8.5  75.5  13.7  69.4  13.7  70.1
ARM  BHR-200 High Dose  8  5  62.5  24.5  91.5  30.6  86.3  29.9  86.3
ARM  Placebo  7  2  28.6  3.7  71.0  8.2  64.1  8.5  65.1

11. Multiplicity, Missing Data and Analysis Populations

The registry lists 8 outcome measures, including the primary outcome at Week 12 and two secondary outcomes: maintenance of testosterone suppression at Week 24 and the number of patients reporting thromboembolic adverse events. When a study assesses multiple outcomes or multiple treatment comparisons, the chance of at least one apparently unusual result can increase. As a general statistical principle, a prespecified multiplicity approach can address that issue. The registry record does not report whether any adjustment was planned or used, nor does it give a hierarchy for interpreting outcomes.

The record lists 0 analyses. It therefore does not provide inferential results for the primary or secondary outcomes, including adjusted estimates or p-values. The statistical plan and any interim-analysis procedures are not reported in the registry record. No assumptions about those procedures can be made from the posted outcome descriptions.

The efficacy population is described as intent-to-treat and includes all randomized patients. The registry also states that a randomized patient who did not take study drug was analyzed using randomized treatment. This describes the stated population principle, but not the handling of missing outcome measurements. The record does not report how participants without a Week 12 measurement were classified, whether imputation was used, or how withdrawals and incomplete follow-up affected the analysis. It also does not provide a participant-flow account that would explain the primary-outcome arm sizes.

These omissions matter because missing data and multiple outcomes can affect both the estimates and the interpretation of uncertainty. The reported counts remain descriptive, but the registry information is insufficient to evaluate how complete the endpoint data were or how multiplicity was addressed.

12. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: small intestinal obstruction (11.1%), lymphoid tissue operation (11.1%).

The registry’s serious-adverse-event figures list participants at risk and participants affected separately for each arm. For the low-dose arm, 9 were at risk and 0 were affected; for the mid-dose arm, 8 were at risk and 0 were affected; for the high-dose arm, 9 were at risk and 2 were affected; and for placebo, 8 were at risk and 0 were affected. The record lists 0 deaths in each arm.

These are descriptive safety counts, not estimates of comparative risk. The registry does not report inferential comparisons or uncertainty intervals for serious adverse events. The number at risk in the safety results is not the same in every arm as the arm size listed for the primary outcome. The record does not explain the difference, so the denominators should be read in the context of the specific safety results rather than substituted for the primary-outcome arm sizes.

The registry lists small intestinal obstruction and lymphoid tissue operation among the top serious adverse event terms, each with 11.1%. The available information does not identify an arm for these terms or provide enough context to interpret their relationship to the arm-level serious-event counts. These terms and percentages should not be treated as evidence of a treatment-related cause. The secondary outcome concerning thromboembolic adverse events is listed, but its results are not reported in the registry record.

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

The results establish what the registry reports: arm-specific counts for the primary measure, safety counts by arm, and a terminated study status. They do not establish a comparative treatment effect. The primary measure is described in terms of failure to maintain castrate testosterone levels, with suppression defined by the absence of any measurement over 50 ng/dL during Weeks 4 to 12. The registry’s outcome title instead refers to maintenance, so the reported counts should be interpreted with attention to that wording rather than assigned a direction that the record does not clarify.

The posted primary results do not include percentages, confidence intervals, p-values, or adjusted analyses. Therefore, the counts cannot show how precise a between-group difference would be, or whether a formal comparison would distinguish an effect from random variation. The counts also do not describe individual testosterone trajectories, the frequency of measurements, or changes after the primary assessment.

The safety information is similarly descriptive. It reports serious adverse events and deaths by arm, and lists selected serious-event terms, but it does not provide comparative safety estimates or a reported result for thromboembolic adverse events. The figures should not be used to infer causality or to rank treatment groups.

More broadly, the registry record does not report the original statistical plan, sample-size justification, missing-data methods, multiplicity handling, or reason for termination. Those gaps constrain evaluation of both the analysis and the completeness of follow-up. The study’s randomized and masked design is relevant context, but design labels alone do not resolve the missing reporting details.

In general, a registry result is one component of an evidence assessment, not a substitute for a complete statistical report. Here, the posted data support a careful description of observed counts, but not a conclusion about efficacy, comparative safety, or the clinical importance of any difference.

14. Why This Trial Matters Statistically

This trial raises several important statistical issues in a compact dose-finding design. It uses a threshold-based testosterone endpoint, compares three active doses with placebo, and reports a binary count at a prespecified time point. Those features make clear definitions and transparent reporting essential: readers need to know how repeated measurements produce a participant-level classification and whether the reported count represents maintenance or failure, particularly because the title and endpoint description emphasize different directions.

The study also illustrates why counts should be accompanied by measures of uncertainty when a comparative question is being asked. A count alone describes the recorded outcomes, but does not quantify the precision of a treatment contrast. Without an inferential analysis or confidence interval in the registry record, the observed arm values cannot support a formal claim about differences between doses and placebo.

Multiplicity is another relevant consideration. The registry lists multiple outcome measures and more than one secondary outcome, yet does not report a statistical plan or any adjustment for multiple comparisons. In general, considering several outcomes and treatment contrasts can complicate interpretation unless the analysis strategy is clearly stated in advance and reported with the results.

Finally, the registry’s intent-to-treat description gives useful context, but does not explain the handling of missing measurements or the difference between arm sizes reported for the primary outcome and safety results. These details matter when evaluating a trial’s analysis population and the reliability of its estimates. The record’s terminated status, without a reported reason, is also important context but does not itself explain the observed results.

The trial therefore matters statistically as an example of why design labels and raw outcome counts are not enough for comparative interpretation. Clear endpoint direction, analysis methods, participant flow, missing-data handling, and uncertainty estimates are needed to understand what a randomized study’s results can support.

15. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves important aspects of the primary endpoint unclear. Its title describes maintenance of testosterone suppression, while the endpoint description calls the primary efficacy endpoint the percentage failing to maintain castrate levels. The record defines suppression using the absence of any testosterone measurement over 50 ng/dL during Weeks 4 to 12, but does not further reconcile the direction of the title, definition, and posted counts.

Only counts are reported for the primary measure. No percentage, effect estimate, confidence interval, or inferential comparison is posted. Although the stated analysis population is intent-to-treat, the record does not explain how missing Week 12 measurements, withdrawals, or incomplete follow-up were handled. Nor does it provide participant flow or explain why the primary-outcome and safety results have different arm-specific risk counts.

The registry describes a randomized, quadruple-masked design but does not report details of sequence generation, allocation concealment, or implementation of masking. The statistical plan, sample-size justification, multiplicity handling, and any interim analyses are not reported in the registry record. The reason for the terminated status is also not reported.

Safety results are limited to the reported event counts and selected terms. The registry does not provide inferential safety comparisons or a posted result for the secondary outcome concerning thromboembolic adverse events. These limitations mean the available record supports description of selected outcomes, but not a full assessment of the analysis, missingness, comparative precision, or reasons the study ended.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Maintaining Suppression of Testosterone With Transdermal Estradiol Gel — NCT02349386.
• Registry record last updated 2022-03-31; status last verified 2018-04.
• Results first posted 2022-03-31.
• 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.

19. Record Summary

The registry describes a Phase 2 randomized, quadruple-masked, parallel-group, placebo-controlled dose-finding study of BHR-200 transdermal estradiol gel in men with advanced androgen-sensitive prostate cancer. The active regimens were low, mid, and high dose, with placebo as comparator. The primary outcome was maintenance of testosterone suppression at Week 12, defined in the outcome description by the absence of any measurement over 50 ng/dL during Weeks 4 to 12.

The primary results are reported as participant counts by arm, and safety results include serious adverse event counts and deaths. The registry lists 8 outcome measures and 2 secondary outcomes. It records an enrollment of 34 and a terminated status. No inferential analyses are reported. The registry record does not report the reason for termination, the statistical plan, missing-data methods, multiplicity handling, or confidence intervals for the primary outcome.