Safety and Efficacy of Intranasal TBS-1 Treatment of Male Hypogonadism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Intranasal TBS-1 Treatment of Male Hypogonadism (NCT01446042), a randomized phase 3 study. The primary outcome is Serum Testosterone Cavg.

2. Clinical Question

3. Trial Design

NCT01446042 is recorded as a Phase 3, randomized, parallel study with no masking. It was completed, with enrollment of 306. The registry lists the study start as 2011-09 and primary completion as 2012-12. The official title describes a 90-day dose-ranging study, potential dose titration, and sequential safety extension periods of 90 and 180 days. These title details describe the planned study structure; they do not establish which participants entered or completed each period.

Three treatment arms appear in the posted primary outcome results: TBS-1 - b.i.d., TBS-1 - b.i.d./t.i.d., and TBS-1 - t.i.d. The arm descriptions give 5.5 mg per nostril of 4.5% TBS-1 for the b.i.d. and t.i.d. regimens. The registry lists testosterone as the drug intervention. It does not list a placebo or untreated control arm. The b.i.d. regimen is the reference for the posted comparisons.

The primary outcome is Serum Testosterone Cavg, assessed at 90 days. It is defined as the percentage of patients whose average serum total testosterone concentration was within 300 to 1050 ng/dL. The population stated for this endpoint is the Per-Protocol Population. The registry records two outcome measures and one posted secondary outcome. The duration and conduct of any safety extension for individual arms, the method used to assign participants, and the handling of participants who changed dose 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: Per-Protocol 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 Serum Testosterone Cavg, measured over 90 days.

Serum Testosterone Cavg refers to the average serum total testosterone concentration. The primary endpoint counts participants whose Cavg was within the stated normal range, 300 to 1050 ng/dL, at 90 days. Although the registry describes the outcome as a percentage, the posted results also give the number of participants meeting the criterion and the number in each arm. The endpoint population is the Per-Protocol Population.

This endpoint turns a continuous measurement into a binary outcome: each participant either met the specified range criterion or did not. A threshold-based endpoint can make the treatment-group results easy to describe as counts and proportions. It also answers a narrower question than a comparison of the full distribution of testosterone concentrations would answer. Participants with values near either boundary are classified according to whether their average concentration falls within the stated range; the registry outcome does not report how far a value was from a boundary.

The registry describes the study purpose as evaluating efficacy based on the pharmacokinetic profile of testosterone and safety. Cavg is relevant to that stated purpose because it summarizes average concentration over the assessment period rather than representing a single maximum concentration. The separately listed secondary outcome concerns participants with a certain serum total testosterone maximum concentration on Day 90. That is distinct from the primary Cavg criterion. The registry record does not report further endpoint calculation details or the timing of samples used to derive Cavg.

7. Results Posted in the Registry

• TBS-1 - b.i.d./t.i.d.: 63.2% (43/68) versus 74.5% (76/102) on control; risk difference -11.3 percentage points (95% CI -25.5 to 3.0), risk ratio 0.85 (0.69–1.05); unadjusted two-proportion z-test p = 0.116.
• TBS-1 - t.i.d.: 91.0% (61/67) versus 74.5% (76/102) on control; risk difference 16.5 percentage points (95% CI 5.7 to 27.4), risk ratio 1.22 (1.07–1.40); unadjusted two-proportion z-test p = 0.007.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is counted as meeting or not meeting the Cavg range criterion. For this kind of endpoint, group results can be expressed as event counts and proportions. The comparison reported for each non-reference arm is a risk difference, which describes the difference between the arms’ proportions meeting the endpoint. A positive estimate indicates a higher proportion in the comparison arm; a negative estimate indicates a lower proportion. The posted comparison estimates have intervals and unadjusted p-values.

What does an interval convey?

In general, a confidence interval describes a range of values compatible with the observed data under the statistical model used. It communicates uncertainty about the effect estimate, not a guarantee that the true effect lies within the interval. For a risk difference, the null value is no difference. An interval that includes that value does not rule out no difference at the interval’s stated confidence level; an interval that excludes it is inconsistent with no difference at that level under the model. The registry record does not state the confidence level or provide enough detail to assess the interval method.

How should the p-values be read?

A p-value measures how unusual data at least as inconsistent with the null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an effect. The posted p-values are explicitly unadjusted. The result for t.i.d. versus b.i.d. has p = 0.007, while the result for b.i.d./t.i.d. versus b.i.d. has p = 0.116. Their interpretation depends on the underlying analysis assumptions, the endpoint definition, and whether multiple comparisons were planned or adjusted.

What can be inferred from the arm counts?

The posted endpoint counts are 76 of 102 in the b.i.d. arm, 43 of 68 in the b.i.d./t.i.d. arm, and 61 of 67 in the t.i.d. arm. The counts identify how many participants met the endpoint in each arm, but do not, by themselves, give the uncertainty in a between-arm difference. The risk-difference comparisons add an estimate and interval for each comparison with the reference arm. Because the groups are not the same size, raw counts should not be compared as though they were proportions.

Randomization is intended, in general, to support fair comparison of treatment groups by reducing systematic differences at assignment. The registry identifies the study as randomized but does not report the allocation sequence, allocation concealment, or detailed randomization procedures. Masking is listed as none. In general, an open-label design can leave outcome assessment or participant behavior more vulnerable to expectations, although this endpoint is based on a laboratory concentration and the registry does not report who knew treatment assignment or how measurements were handled.

Which analysis details are absent?

The endpoint population is the Per-Protocol Population. The registry record does not report the per-protocol eligibility rules, the analysis model, covariate adjustment, missing-data approach, or the original statistical analysis plan. It also does not report whether the risk-difference method accounted for any features of the design beyond the posted comparison. No interim analyses or multiplicity adjustment are reported in the registry record. The registry lists zero analyses, so the posted counts and comparisons do not constitute a detailed account of all analyses that may have been conducted.

The endpoint is a thresholded summary of a continuous measure. In general, a binary endpoint can be straightforward to interpret, but reduces information about how measured values vary within or beyond the normal range. The registry’s separately listed secondary outcome concerns a maximum concentration and does not substitute for the primary average-concentration endpoint. No additional subgroup analyses are posted. Any interpretation should therefore remain tied to the stated 90-day Cavg criterion and the analysis population identified in the record.

10. Confidence Intervals and Precision

The comparison intervals help convey how precisely the risk differences are estimated. For b.i.d./t.i.d. versus b.i.d., the interval spans both a negative difference and no difference, so the result is compatible with more than one direction of effect. The unadjusted p-value is 0.116. For t.i.d. versus b.i.d., the interval lies on the positive side of no difference, and the unadjusted p-value is 0.007. These features indicate different levels of statistical evidence for the two posted comparisons, but neither interval alone establishes clinical importance.

In general, interval width reflects both the observed data and the method used to estimate uncertainty. The number of participants and the frequency of the binary outcome affect precision. The arm sizes for the primary outcome are 102, 68, and 67, respectively. The registry does not report the confidence level or enough methodological detail to independently evaluate the interval construction. No precision statement should be extended to outcomes or time periods not represented by these endpoint comparisons.

The intervals concern differences in proportions meeting the specified Cavg range, not differences in average testosterone concentration itself. They also do not quantify uncertainty about serious adverse events. The outcome is identified as per-protocol, and any uncertainty related to excluded participants or missing measurements is not captured by the reported comparison unless those factors were handled in the analysis; the relevant methods are not reported in the registry record. Thus, the intervals express statistical precision within the posted analysis, while unanswered design and analysis questions remain outside their scope.

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 planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect, rather than the original trial’s own design calculations. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses a stated fraction of the observed effect to define the effect to detect. The original sample-size justification and design assumptions are not reported in the registry record.

For the b.i.d./t.i.d. comparison, planning for 100% of the observed effect gives 264 participants per arm for 80% power and 353 participants per arm for 90% power. Planning for 75% gives 458 participants per arm for 80% power and 612 participants per arm for 90% power. Planning for 50% gives 1,002 participants per arm for 80% power and 1,341 participants per arm for 90% power.

For the t.i.d. comparison, planning for 100% of the observed effect gives 81 participants per arm for 80% power and 108 participants per arm for 90% power. Planning for 75% gives 158 participants per arm for 80% power and 211 participants per arm for 90% power. Planning for 50% gives 385 participants per arm for 80% power and 515 participants per arm for 90% power.

In general, 80% power means an 80% chance of detecting the specified effect under the planning assumptions if that effect is real; 90% power means a higher chance under the same conditions. Smaller effects need more participants to detect with the same power. These figures are planning illustrations, not observed power, and do not show the probability that the trial’s findings are correct.

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 = 0.745; treatment proportion p₁ = 0.632; average p̄ = 0.689.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6548 = 1.2834.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6499 = 0.5470.
4. n = (1.2834 + 0.5470)² / (-0.1127)² = 263.6, rounded up to 264 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 <- 0.745098039215686                          # control proportion
p1 <- 0.632352941176471                          # 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(1446042)
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 = 264 (80% power), 353 (90% power)
 75% of observed effect: n per arm = 458 (80% power), 612 (90% power)
 50% of observed effect: n per arm = 1,002 (80% power), 1,341 (90% power)
power.prop.test: 263.6 
Simulated power at n = 264 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 one secondary outcome: patients with a certain serum total testosterone maximum concentration on Day 90. It also records two outcome measures and zero analyses. The primary endpoint and comparisons are posted, but the registry does not specify how many hypotheses were included in the original analysis plan or which comparisons were designated as primary, secondary, or exploratory.

The p-values for the two comparisons are unadjusted. No correction for testing multiple comparisons is reported in the registry record. When several hypotheses are tested, the chance of obtaining at least one apparently unusual result can increase; multiplicity procedures are used in some analyses to address that issue. Without a stated analysis plan or adjustment method, the p-values should be read as unadjusted evidence for their individual comparisons, not as results adjusted across all possible outcomes or comparisons.

The primary endpoint is reported for the Per-Protocol Population. The registry record does not report the criteria used to define that population, participant disposition by analysis population, or whether participants with missing measurements were excluded, imputed, or handled in another way. Missing-data methods can affect both the estimated endpoint proportions and their uncertainty, particularly when missingness differs across groups or relates to the outcome. The posted arm counts do not explain why participants are not included in the endpoint denominators.

Details of the statistical analysis plan, any interim analyses, and sensitivity analyses are not reported in the registry record. Their absence from the record should not be taken as proof that these analyses or procedures did not occur. It means the posted information does not allow readers to assess prespecification, the handling of missing data, or the robustness of the findings to alternative analysis choices.

14. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: internal injury (1.3%), road traffic accident (1.3%), abdominal mass (1.3%), acute coronary syndrome (1.2%), fall (0.7%).

The safety results report participants at risk, participants affected by serious adverse events, participants affected by other adverse events, and deaths for each safety group. For TBS-1 - b.i.d., 142 participants were at risk for the serious-event count and 2 were affected; 65 participants were affected by other adverse events, and 0 deaths were reported. For TBS-1 - b.i.d./t.i.d., the corresponding counts were 86 at risk, 1 with a serious adverse event, 40 with other adverse events, and 0 deaths. For TBS-1 - t.i.d., 78 were at risk, 2 had a serious adverse event, 46 had other adverse events, and 1 death was reported.

These figures are counts, not comparative estimates of risk, and the safety-group denominators differ from the primary endpoint denominators. The registry also lists serious-event terms with percentages, including Internal injury, Road traffic accident, and Abdominal mass at 1.3% each; Acute Coronary Syndrome at 1.2%; and Fall and Hip Fracture at 0.7% each. The record does not establish that an event was caused by treatment. Event relatedness, exposure time, and the safety analysis methods are not reported in the registry record. The counts should be read as descriptive safety reporting, not as a basis for comparing regimens without further context.

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

The posted data describe how often participants in each TBS-1 regimen met a defined laboratory concentration criterion at 90 days. The t.i.d. group had a positive risk-difference comparison with the b.i.d. reference group, with an interval excluding no difference and an unadjusted p-value of 0.007. The b.i.d./t.i.d. comparison had an interval including no difference and an unadjusted p-value of 0.116. These are statistical results for the primary endpoint as recorded, not conclusions about every measure of treatment response or safety.

The endpoint classifies average serum total testosterone concentration against the stated range of 300 to 1050 ng/dL. It does not report the distribution of Cavg values, the magnitude of changes from baseline, or whether participants were close to the range boundaries. The results do not by themselves show how long concentrations remained within the range, what occurred during the sequential safety extensions, or how maximum concentration outcomes compared across all arms.

The trial was randomized, but masking was listed as none, and the endpoint is reported for a per-protocol population. The registry does not report the analysis plan, missing-data procedures, or multiplicity adjustment. These limitations affect how comprehensively the posted comparisons can be interpreted. A result with an unadjusted p-value below 0.05 is not proof of a clinically important effect, and a result with a larger p-value does not prove no difference.

Safety counts include serious adverse events and deaths, but the registry does not report attribution or provide a detailed comparative safety analysis. Overall, the record supports a focused reading of the 90-day threshold-based endpoint and descriptive safety counts. Broader conclusions about clinical benefit, long-term outcomes, comparative safety, or the robustness of findings require information not reported in the registry record.

16. Why This Trial Matters Statistically

This study illustrates how a continuous biological measurement can be converted into a binary endpoint. Defining success as Cavg within 300 to 1050 ng/dL yields a direct count of participants meeting a prespecified-looking clinical range, but the registry does not say how the range was selected or whether it was prespecified in the analysis plan. Dichotomizing a measurement can simplify communication while discarding information about how values are distributed within each arm.

The three-arm design also creates more than one comparison with the reference regimen. The posted evidence differs by comparison: the t.i.d. comparison has an interval excluding no difference, whereas the b.i.d./t.i.d. comparison has an interval spanning no difference. This contrast shows why effect estimates and intervals matter alongside p-values. The registry does not report a multiplicity strategy, so the evidence cannot be interpreted as adjusted across all possible comparisons.

Enrollment and endpoint analysis sizes are not identical descriptions of the trial population: the registry records enrollment of 306, while the posted primary endpoint has arm denominators of 102, 68, and 67. The record does not explain participant flow or the relationship between enrollment and the per-protocol endpoint population. That distinction is important when evaluating how broadly the analysis represents the randomized study population.

Finally, the safety summaries use their own at-risk counts, which differ from the primary outcome denominators. Keeping endpoint populations and safety populations distinct prevents accidental comparison of unlike denominators. The record is a useful example of why statistical interpretation needs to consider endpoint definition, analysis population, uncertainty, multiplicity, and the completeness of registry reporting together.

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.

The posted primary results are limited to the 90-day Cavg threshold outcome in the Per-Protocol Population. The registry record does not report the per-protocol criteria, participant flow, or how the endpoint denominators relate to all 306 enrolled participants. It also does not report baseline endpoint values, changes from baseline, or the distribution of measured concentrations, so the primary results cannot describe those aspects of the data.

The study was unmasked. The registry does not describe who knew treatment assignments during outcome collection or whether laboratory assessment procedures were blinded. It also does not report allocation concealment or the method used to generate the randomization sequence. The statistical analysis plan, model details, missing-data handling, and multiplicity approach are not reported in the registry record. The comparisons are unadjusted, and the record does not establish whether they were prespecified.

The registry title describes potential dose titration and sequential safety extension periods of 90 and 180 days, but the posted primary endpoint is at 90 days. The record does not provide extension-period outcome results or participant-level exposure details. Safety summaries are counts with different at-risk denominators, and event attribution and exposure time are not reported. The record also does not report the original sample-size justification; the displayed planning calculations are illustrations based on the observed effects rather than the trial’s own design assumptions.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Efficacy of Intranasal TBS-1 Treatment of Male Hypogonadism — NCT01446042.
• Registry record last updated 2018-06-13; status last verified 2018-03.
• Results first posted 2018-06-13.
• 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

NCT01446042 is a completed, randomized, open-label, parallel Phase 3 study of intranasal TBS-1 in men with male hypogonadism. Enrollment was 306. The registry lists the start as 2011-09 and primary completion as 2012-12. The official title describes a 90-day dose-ranging study with potential dose titration and sequential safety extension periods of 90 and 180 days.

The primary endpoint was the proportion of the Per-Protocol Population with serum testosterone Cavg within 300 to 1050 ng/dL at 90 days. The posted results compare TBS-1 - b.i.d./t.i.d. and TBS-1 - t.i.d. with TBS-1 - b.i.d. The t.i.d. comparison has an unadjusted p-value of 0.007; the b.i.d./t.i.d. comparison has an unadjusted p-value of 0.116. The record includes safety counts and one secondary outcome, but does not report the original analysis plan, missing-data methods, or multiplicity approach.