Oral Testosterone for the Treatment of Hypogonadism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Oral Testosterone for the Treatment of Hypogonadism (NCT01717768), a randomized phase 2 study. The primary outcome is Percentage of Subjects Achieving a 24 Hour Average Total Serum Testosterone Concentration (Cavg,0-24h) in the Range of 300 to 1050 ng/dL After 15 Days of Treatment With TSX-002.

2. Clinical Question

3. Trial Design

The registry identifies this as a Phase 2 study of oral testosterone in participants with hypogonadism. It reports randomized allocation, a parallel model, and masking of none. The official title describes the study as double-blind, so the title and the registry's masking field do not agree. The record does not explain that difference. Enrollment was 130, and the study status is completed.

The study had multiple parts rather than a single simple comparison. Part 1 included 120 mg BID and 240 mg BID regimens, each described as oral treatment for 15 days. Part 2 was a single-cohort, open-label, nonrandomized 120 mg BID regimen for 15 days. Part 3 used an open-label, randomized, three-way crossover design to assess single-dose exposure with a meal; the listed sequences were A-B-C, B-C-A, and C-A-B. Part 4 listed several dose and frequency regimens, including BID, TID, and once-daily treatment. Some Part 4 descriptions specify sequential schedules, while the posted endpoint groups name the individual treatment regimens.

The primary endpoint results are reported for Part 1, Part 2, and Part 4. The brief study description says related outcome measures were to be reported for those parts, and identifies Part 3 as a meal-effect pharmacokinetic assessment. Part 3 does not appear among the primary endpoint groups. The registry record does not report how participants were assigned across all parts, whether every regimen was intended for direct comparison, or the original statistical 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.

Only the first 6 of 12 groups are shown.

Part 1 (Duration of 15 Days)

Reasons for not completing this period:

Part 2 (Duration of 15 Days)

Part 3 - Treatment 1 (Duration of 1 Day)

Part 3 - Treatment 2 (Duration of 1 Day)

Analysis population for the primary outcome, as defined in the registry: All efficacy analyses were conducted based on the modified intent-to-treat (MITT) analysis population, comprised of all randomized subjects who receive at least 1 dose of study drug and have at least 1 post-baseline measurement of total serum testosterone.

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.

Only the first 6 of 11 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects Achieving a 24 Hour Average Total Serum Testosterone Concentration (Cavg,0-24h) in the Range of 300 to 1050 ng/dL After 15 Days of Treatment With TSX-002, measured over 15 days.

The primary endpoint is the percentage of participants whose 24-hour average total serum testosterone concentration, described as Cavg,0-24h, was from 300 to 1050 ng/dL after 15 days of treatment with TSX-002. In plain terms, it counts participants whose measured concentration summary fell inside the registry's specified range. The reported values are percentages of participants, not average testosterone concentrations.

The endpoint is based on serial blood sampling over a 24-hour period after the treatment period. The registry gives different sampling schedules for Parts 1, 2, and 4. This approach is used to characterize concentrations across the dosing interval, rather than relying on a single blood measurement. As a general statistical point, converting a continuous measurement into an in-range versus out-of-range outcome makes the result easier to read as a proportion, but it discards information about how far an individual value lies from either boundary.

The endpoint addresses whether participants met the stated concentration target at the specified assessment. It does not directly report symptom relief, quality of life, or longer-term clinical outcomes. Those outcomes are not reported in the registry record as primary results. The record also does not explain why these particular concentration boundaries were selected.

7. Results Posted in the Registry

• Part 1: 240 mg BID: 29.4% (5/17) versus 58.8% (10/17) on control; risk difference -29.4 percentage points (95% CI -61.3 to 2.5), risk ratio 0.50 (0.22–1.15); unadjusted two-proportion z-test p = 0.084.
• Part 2: 120 mg BID: 35.3% (6/17) versus 58.8% (10/17) on control; risk difference -23.5 percentage points (95% CI -56.1 to 9.1), risk ratio 0.60 (0.28–1.28); unadjusted two-proportion z-test p = 0.169.
• Part 4 Cohort 1: 60 mg BID: 41.2% (7/17) versus 58.8% (10/17) on control; risk difference -17.6 percentage points (95% CI -50.7 to 15.4), risk ratio 0.70 (0.35–1.40); unadjusted two-proportion z-test p = 0.303.
• Part 4 Cohort 1: 60 mg TID: 52.9% (9/17) versus 58.8% (10/17) on control; risk difference -5.9 percentage points (95% CI -39.2 to 27.4), risk ratio 0.90 (0.49–1.64); unadjusted two-proportion z-test p = 0.730.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant either met the stated concentration range or did not. A group percentage is the proportion meeting that criterion, expressed in the registry as a percentage. The risk difference compares two such proportions by subtracting the reference proportion from the comparison proportion. A negative risk difference means the comparison group had a lower observed proportion than the reference group. These are general interpretations of the statistical measures.

What does the confidence interval describe?

A confidence interval gives a range of values that are reasonably compatible with the observed data under the method used to construct it. It reflects sampling uncertainty, not the range of individual participants' concentrations. For example, the Part 1: 240 mg BID risk difference is -0.294, with an interval from -0.613 to 0.025. Because that interval includes zero, the posted estimate is compatible with no difference as well as with a lower percentage in the comparison group. An interval that excludes zero, as reported for the 90 mg BID and Part 4 120 mg BID comparisons, indicates that the corresponding interval estimate does not include a zero risk difference. It does not resolve limitations in study design, analysis choices, or precision.

Why are risk ratios and odds ratios different?

A risk ratio compares the two proportions as a ratio, while an odds ratio compares the odds of meeting the endpoint. They are distinct scales for describing the same binary outcome, so their numerical values need not match. The registry's pairwise results include risk ratios and odds ratios as well as risk differences. These measures can be useful for different reporting purposes, but their interpretation depends on the chosen scale. The risk difference is especially direct in this setting because it describes the difference in the percentage meeting the criterion. No adjustment for other variables is reported for these derived comparisons.

What does an unadjusted p-value mean?

A p-value summarizes how unusual results at least as extreme as the observed result would be under a statistical model in which there is no difference between the groups. It is not the probability that the no-difference explanation is true, nor a measure of the size or clinical importance of an observed difference. The listed p-values are unadjusted. The registry record does not report whether the trial's own analysis used multiplicity adjustment, or how the multiple dose and schedule comparisons were handled. Accordingly, p-values near conventional thresholds should be read alongside the estimates, intervals, group sizes, and design context rather than as stand-alone conclusions.

What is the role of the analysis population?

The registry says efficacy analyses used a modified intent-to-treat population, defined as randomized participants who received at least 1 dose and had at least 1 post-baseline total serum testosterone measurement. This definition excludes randomized participants who did not meet either condition. As a general matter, an analysis population definition affects which participants contribute to an estimate and may affect how results relate to the originally randomized groups. The number included in each endpoint analysis and the handling of missing measurements are not reported in the registry record in the details available for these results.

What can the posted calculations add?

The pairwise risk differences and associated intervals and p-values are simple, unadjusted re-calculations from posted group summaries. They help put the group percentages into a contrast against the reference group, but they are not a substitute for the sponsor's prespecified analysis. No discrepancy is flagged between these calculations and a sponsor result in the registry record. The original statistical methods, including the exact interval construction and any covariate adjustment, are not reported in the registry record. The re-calculations therefore support descriptive interpretation, not reconstruction of an undocumented trial analysis.

10. Confidence Intervals and Precision

The primary endpoint groups are small: the reported group counts are 17 in most listed groups and 16 in several Part 4 groups. With limited observations, each participant's endpoint status can have a noticeable influence on the group percentage. This is one reason to read the estimated percentages together with their confidence intervals rather than treating the percentages as precise population values.

The risk-difference intervals are broad for many comparisons. For example, the interval for Part 1: 240 mg BID extends from -0.613 to 0.025, and that for Part 2: 120 mg BID extends from -0.561 to 0.091. These intervals include zero and allow for a range of possible differences. The interval for Part 4 Cohort 1: 60 mg TID also spans zero, from -0.392 to 0.274. Thus, the observed group values alone do not tightly determine the underlying difference.

Two reported comparisons have intervals that exclude zero: Part 4 Cohort 2: 90 mg BID and 90 mg TID, each with an interval from -0.703 to -0.099; and Part 4 Cohort 4: 120 mg BID, with an interval from -0.654 to -0.022. Those intervals still cover a broad range of negative differences. The reported interval for the 120 mg BID comparison on the risk-difference scale includes only negative values, while the posted risk-ratio interval extends to 1.085. Different measures and interval methods can yield different interval behavior; the registry record does not report enough methodological detail to reconcile that feature.

Confidence intervals address sampling variability under their calculation method. They do not account automatically for selection, missing data, differences in study structure, or multiple comparisons. Those considerations matter because the groups are small and the record does not fully describe the analysis plan or missing-data handling. Precision is therefore limited both by the width of the intervals and by incomplete information about how the comparisons were designed and analyzed.

11. 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 figures are planning illustrations based on the observed effect, not a report of the trial's original design assumptions. For these binary endpoint comparisons, the figures are participants per arm, not total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the assumed effect under those assumptions, if that effect and model were correct. The 90% power column uses a higher target chance of detecting the same assumed effect, and therefore generally calls for more participants per arm. These are hypothetical design calculations, not evidence about the power achieved by the completed trial. This is not observed power.

Rows labeled planning for 100%, 75%, or 50% of the observed effect show how the planning requirement changes when the assumed effect is reduced from the observed estimate. Smaller effects need more participants to distinguish them from random variation with the same target power. This is particularly relevant because the observed effects come from small groups and may be unstable; a planning estimate based on an observed effect should not be treated as a reliable prediction of a future result.

The registry record does not report the trial's own sample-size justification or original power assumptions. The figures are per arm for the displayed binary comparisons; they should not be confused with the trial enrollment of 130 or interpreted as retrospective proof that a particular comparison was adequately powered.

12. 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 = 0.588; treatment proportion p₁ = 0.294; average p̄ = 0.441.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7022 = 1.3763.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6707 = 0.5645.
4. n = (1.3763 + 0.5645)² / (-0.2941)² = 43.5, rounded up to 44 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 <- 0.588235294117647                          # control proportion
p1 <- 0.294117647058824                          # 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(1717768)
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 = 44 (80% power), 58 (90% power)
 75% of observed effect: n per arm = 80 (80% power), 106 (90% power)
 50% of observed effect: n per arm = 181 (80% power), 241 (90% power)
power.prop.test: 43.5 
Simulated power at n = 44 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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists several dose and frequency groups and multiple pairwise comparisons against Part 1: 120 mg BID. When many comparisons are examined, the chance of at least one apparently notable result arising by chance can increase. As a general statistical principle, multiplicity procedures can control that risk, but the record does not report whether any such procedure was prespecified or applied. The p-values attached to the comparisons are identified as unadjusted, so they do not account for the number of contrasts.

The record reports the primary endpoint and describes secondary outcomes concerning Cmax thresholds after treatment. It indicates one posted secondary outcome measure, while the description refers to several threshold categories. Secondary outcome results and analysis details are not reported in the registry record in the information summarized for these results. The registry also reports zero analysis entries. The original statistical analysis plan, including endpoint hierarchies, subgroup analyses, covariate adjustment, and handling of repeated or multiple assessments, is not reported in the registry record.

The stated efficacy population is modified intent-to-treat: randomized participants who received at least 1 dose and had at least 1 post-baseline total serum testosterone measurement. The registry does not report, for each endpoint group, the number excluded from this population or the reasons for exclusion. It also does not report how missing endpoint measurements were handled, whether values were imputed, or whether sensitivity analyses were conducted.

These omissions affect interpretation. A modified intent-to-treat definition can differ from an analysis of every randomized participant, and missing outcomes can alter the observed percentage if their absence is related to treatment or endpoint status. This is a general concern, not evidence that missingness changed these results. Without the missing-data methods, analysis population counts, and multiplicity plan, readers cannot determine how robust the reported comparisons are to those choices. The posted group summaries remain interpretable as reported, but they do not answer those methodological questions.

14. 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 non-serious adverse event terms

The registry's serious adverse event figures report zero affected participants in every listed group. The numbers at risk range from 4 to 17 across the groups, reflecting the different group sizes recorded for safety. A zero count means no serious adverse events were reported among the participants represented in that group; it does not establish that the risk is absent. With small groups, the figures provide limited precision about uncommon events.

The record also lists participants with other, non-serious adverse events by group, but those counts are not the same as the serious adverse event figures. The safety summary does not provide serious adverse event terms, and the listed deaths field is not populated with a number. These details are not reported in the registry record. The registry's safety counts should be read as descriptive counts over the reported study groups, not as a complete assessment of longer-term safety or a comparison designed to detect rare events.

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

The results describe the percentage of participants in each reported regimen group who met the registry's concentration criterion after 15 days. The observed percentages differ across groups, with Part 1: 120 mg BID at 59.0% and the reported Part 4 Cohort 2: 90 mg BID group at 19.0%. The unadjusted comparisons put those group percentages in relation to the Part 1 reference group, with estimates and confidence intervals that convey sampling uncertainty.

These results do not, on their own, establish which regimen is preferable or whether treatment changes symptoms. The endpoint is a laboratory concentration target, not a direct measure of how participants felt or functioned. The posted results do not report symptom outcomes or longer-term clinical outcomes. The registry record also includes groups from different study parts and designs, including an explicitly nonrandomized open-label cohort. Those differences limit how confidently all listed percentages can be interpreted as directly comparable treatment effects.

Some intervals include no difference, and others exclude zero on the risk-difference scale. Even where an interval excludes zero, the estimate remains subject to small group sizes, unadjusted multiple comparisons, and incomplete reporting of analysis methods. Statistical evidence about this endpoint should not be mistaken for a complete account of the study or a guarantee about individual outcomes.

In general, an in-range concentration result can describe whether a measured value met the study's target at the assessment time. It does not by itself show the duration of that result beyond the measured period, nor does it establish benefits or harms beyond outcomes actually reported. The record's 15-day endpoint and posted group summaries support a narrow statistical reading: observed proportions differed, and the precision and design context should shape interpretation.

16. Why This Trial Matters Statistically

This trial illustrates why dose-ranging results need to be read as estimates with uncertainty rather than as a simple ranking of percentages. The groups differ in dose and administration frequency, and the reported proportions vary. But the group sizes are small, confidence intervals are often broad, and not every group arises from the same design structure. The registry's single reference group is useful for organizing contrasts, yet it does not make every contrast equivalent to a randomized head-to-head comparison.

The binary endpoint also demonstrates a common tradeoff in clinical statistics. An in-range percentage is easy to interpret, but turning a continuous concentration profile into a threshold outcome removes information about the values within and outside the range. A participant just outside a boundary and one far outside it are both counted as not meeting the criterion. The posted endpoint therefore answers a specific question, not every question about the concentration profile or clinical response.

Finally, the record highlights the importance of transparent statistical reporting. The population definition is stated, but the original sample-size rationale, detailed analysis plan, multiplicity handling, and missing-data methods are not reported in the registry record. Those items help readers understand how estimates were selected and how much weight to place on multiple comparisons. The observed results are informative as descriptive data, while their interpretation remains bounded by the precision and reporting available.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record presents a complex study with multiple parts, several dose schedules, and different design descriptions. It reports randomized allocation overall, but also identifies Part 2 as a single-cohort, open-label, nonrandomized part and Part 3 as an open-label crossover assessment. The record does not specify how the primary endpoint groups relate to randomization across all parts. Consequently, the pairwise contrasts should not automatically be treated as randomized causal comparisons.

The registry's masking field is none, while the official title calls the study double-blind. The record does not explain this inconsistency or indicate whether masking differed across parts. The posted endpoint group sizes are small, and several confidence intervals are wide. Such estimates may be sensitive to a small number of participants meeting or not meeting the threshold.

Statistical reporting is incomplete for evaluating robustness. The original analysis plan, sample-size justification, multiplicity procedures, missing-data methods, and analysis counts by group are not reported in the registry record. The available pairwise comparisons are unadjusted calculations from group summaries. The record also does not provide the primary endpoint results for Part 3, whose stated focus was meal-related pharmacokinetic exposure, or detailed secondary outcome results.

Lastly, the primary outcome is a short-term concentration threshold after 15 days. The registry does not report symptom-based or longer-term primary results in the information. These limitations do not negate the posted measurements; they define the scope of conclusions that can be drawn from them.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Oral Testosterone for the Treatment of Hypogonadism — NCT01717768.
• Registry record last updated 2015-12-15; status last verified 2015-12.
• Results first posted 2015-12-15.
• 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.

21. Record Summary

NCT01717768 is a completed Phase 2 study of oral TSX-002 in participants with hypogonadism, with registry enrollment of 130. Its primary endpoint was the percentage achieving a 24-hour average total serum testosterone concentration from 300 to 1050 ng/dL after 15 days of treatment. The posted group percentages vary across the reported regimens, and the unadjusted risk-difference comparisons against Part 1: 120 mg BID have varying estimates and precision.

The registry describes multiple study parts, including a nonrandomized open-label cohort and a randomized crossover meal assessment. Small group sizes, wide intervals, and unreported details about multiplicity, missing data, and the original statistical plan constrain interpretation. The results characterize the posted concentration endpoint and do not alone establish effects on symptoms or longer-term outcomes.