90 mg Fluoxetine Hydrochloride Capsules Under Non-Fasting Conditions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for 90 mg Fluoxetine Hydrochloride Capsules Under Non-Fasting Conditions (NCT01247285), a randomized phase 1 study. The primary outcome is Cmax of Fluoxetine..

2. Clinical Question

3. Trial Design

This was a Phase 1, randomized, unmasked crossover study recorded as completed. It enrolled 26 participants and compared the test and reference products in healthy adults. Both products were 90 mg capsules administered as a single oral dose under non-fasting conditions. The study start was recorded as 2001-05, and primary completion as 2001-07.

The crossover structure is important when interpreting the comparison. Participants in this design receive both treatments, so measurements from the same person can be related. That within-person relationship can improve precision when the analysis accounts for it. The registry lists 26 participants in each treatment group, but does not report the treatment sequence, washout duration, or other operational details needed to reconstruct the crossover analysis. It also does not report whether every randomized participant completed both periods.

Masking was listed as none. The registry record does not explain how the randomization sequence was generated or concealed, nor does it describe blinding of laboratory personnel or analysts. The primary endpoint population is described as participants who completed the study and had their samples analyzed. Further details about the protocol, exclusion rules, and analysis population are not reported in the registry record.

The study focus was relative bioavailability: comparison of the rate and extent of absorption of the Teva test capsule with the PROZAC WEEKLY® reference capsule. This is distinct from a clinical-outcome trial intended to compare changes in symptoms or health events. The registry reports pharmacokinetic outcomes measured from blood samples collected over a 25 day period.

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.

First Intervention

Washout of 28 Days

Second Intervention

Analysis population for the primary outcome, as defined in the registry: All participants that completed the study had their samples analyzed.

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 Cmax of Fluoxetine., measured over Blood samples collected over a 25 day period..

The primary endpoint, Cmax of fluoxetine, is the maximum observed concentration of the drug in plasma after administration. It is a continuous pharmacokinetic measure reported in ng/mL. In this study, it was measured from blood samples collected over a 25 day period. The registry describes bioequivalence as being based on this endpoint, while the study's stated purpose was to compare relative bioavailability.

Cmax is used to characterize the peak concentration reached after a dose. In general, a peak measure can contribute information about the rate and extent of absorption, but it does not by itself describe every feature of a concentration-time profile. It is interpreted alongside other pharmacokinetic measures, such as total exposure over time. This study also lists norfluoxetine outcomes, but they are secondary endpoints and concern a metabolite rather than the primary fluoxetine measure.

The posted arm summaries give a mean and standard deviation for each product. The sponsor analysis reports the test-to-reference geometric mean ratio as a percentage with a 90% confidence interval. The registry record does not give the detailed analysis method or the acceptance limits used to judge bioequivalence. Consequently, the endpoint's purpose is clear, but the decision rule and its application cannot be independently reconstructed from the registry record.

7. Results Posted in the Registry

• Fluoxetine Hydrochloride (Test): mean 75.32 versus 69.86 on control; difference 5.46 (95% CI -2.59 to 13.51), standardized effect d = 0.37; z-test p = 0.183.

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.

Cmax of Norfluoxetine.

• 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:
  • Fluoxetine Hydrochloride (Test): mean 35.11 versus 33.47 on control; difference 1.64 (95% CI -5.35 to 8.63), standardized effect d = 0.13; z-test p = 0.645.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fluoxetine Hydrochloride (Test) and the control. The interval gives the range of effects that remain compatible with the data.

AUC0-t of Norfluoxetine.

• 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:
  • Fluoxetine Hydrochloride (Test): mean 114,575 versus 10,849 on control; difference 103,726 (95% CI 101,974 to 105,478), standardized effect d = 32.18; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Fluoxetine Hydrochloride (Test) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

AUC0-inf of Norfluoxetine.

• 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:
  • Fluoxetine Hydrochloride (Test): mean 13,506 versus 13,365 on control; difference 140.71 (95% CI -3,015 to 3,296), standardized effect d = 0.02; z-test p = 0.930.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fluoxetine Hydrochloride (Test) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary norfluoxetine measures: peak concentration and two measures of exposure over time. The sponsor's reported geometric-mean ratio intervals for these outcomes all include 100. Taken together, the secondary analyses do not show a consistent pattern of ratios clearly separated from the equal-ratio value. This broad pattern is compatible with the primary result's interval also spanning 100, but it does not independently resolve the primary endpoint's uncertainty.

The secondary endpoints provide additional pharmacokinetic context because they concern the metabolite and different features of concentration over time. Their relationship to the primary result is supportive context, not a replacement for the primary endpoint. The registry record does not report whether the secondary measures were confirmatory, exploratory, or linked to a prespecified hierarchy. Detailed analysis methods for these estimates are also not reported.

Unadjusted secondary results deserve less weight when several outcomes are examined. In general, the more comparisons considered, the more opportunity there is for chance findings to appear. A multiplicity adjustment or a prespecified testing hierarchy can address that concern, but neither is described in the registry record. The absence of a reported adjustment does not prove that none was used; it means its use cannot be established from this record. The secondary results should therefore be interpreted cautiously and as a pattern of supportive measurements, rather than as separate definitive tests.

The registry also reports six outcome measures and six analyses overall, while three secondary outcomes are listed in the posted record. It does not explain how the full set of measures and analyses relates to the listed secondary outcomes. No additional claims about unlisted outcomes or results can be made from the registry record.

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

• Cmax of Norfluoxetine.
• AUC0-t of Norfluoxetine.
• AUC0-inf of Norfluoxetine.

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean and standard deviation describe?

The primary outcome is continuous, so the registry reports a mean concentration and a standard deviation for each treatment group. A mean describes the group average. A standard deviation describes how spread out individual measurements are around that average. It is not the uncertainty interval for the mean, and it does not indicate how precisely the treatment contrast has been estimated. The posted group summaries are useful for describing the observed concentrations, but they do not show the individual paired observations from a crossover study.

What does the recalculated mean difference represent?

The recalculated estimate subtracts the reference mean from the test mean, yielding a mean difference of 5.46 ng/mL. Its interval, -2.585 to 13.51, describes a range of values compatible with this unadjusted summary-based comparison under its calculation assumptions. Because the interval crosses zero, the data do not sharply distinguish a positive difference from no difference on this scale. The unadjusted p-value is 0.183. A p-value describes how unusual data at least this discrepant would be under a specified null model; it is not the probability that the null hypothesis is true, and it does not measure the importance of an effect.

This recalculation should not be confused with a paired crossover analysis. In a crossover trial, each participant's measurement under one product can be compared with that same participant's measurement under the other. The variability of those paired differences depends on the within-person correlation. Posted group means and standard deviations do not reveal that correlation. The registry record does not report the method behind the sponsor analysis, so the sponsor's calculation cannot be independently reconstructed from these summaries alone.

Why is the sponsor result expressed as a ratio?

The sponsor reports the ratio of the test-to-reference geometric means multiplied by 100. A ratio compares the scale of the two geometric means; 100 represents equality on this ratio scale. The posted primary estimate is 107.81, and its 90% confidence interval is 97.37 to 119.38. This presentation is distinct from a difference in arithmetic means. Pharmacokinetic measurements are often analyzed on a transformed scale, but the registry record does not specify whether or how a transformation was used, nor does it describe the model. Those details are not reported in the registry record.

A confidence interval combines an estimate with its sampling uncertainty. A narrower interval indicates greater precision on the relevant scale; a wider interval indicates more uncertainty. Whether an interval supports a formal bioequivalence conclusion depends on the prespecified acceptance range and the analysis plan. Neither is reported in the registry record. An interval containing 100 is not, by itself, proof of equivalence, just as an interval containing zero for a difference is not proof that the treatments are identical.

Why does over-dispersion matter in general?

In general, over-dispersion means that observed variability is greater than a statistical model assumes. If a model understates variability, standard errors may be too small and confidence intervals too narrow. If it accounts for more variability than the data contain, estimates may be less precise than necessary. This is a general statistical consideration; the registry record does not report an over-dispersion assessment or indicate that such a model was used in this trial.

What is the role of the crossover design?

Randomization determines treatment assignment or sequence by chance, helping to reduce systematic allocation differences. In a crossover study, the same participants receive each treatment, which permits comparison within individuals. Such a design requires attention to sequence, period, and potential carryover effects. The registry record identifies randomization and a crossover model, but does not report sequence details, period-specific analyses, washout information, or carryover assessment. These omissions prevent a full appraisal of whether and how those design features were incorporated into the sponsor's analysis.

The study was unmasked. Lack of masking can matter for outcomes influenced by expectations or judgment. Plasma concentrations are laboratory measurements, but the registry does not state whether laboratory staff or analysts were masked. No conclusion about those safeguards can be drawn from the registry record.

11. Confidence Intervals and Precision

The primary sponsor estimate is a test-to-reference geometric mean ratio of 107.81, with a 90% confidence interval from 97.37 to 119.38. The interval contains 100, the ratio value corresponding to equal geometric means. It also extends both below and above 100, so the estimate does not pinpoint the direction or size of a difference with high precision. The registry record does not report the acceptable ratio range for a bioequivalence decision, which is essential context for judging the interval against a formal criterion.

The recalculated difference in posted means is 5.46 ng/mL, with an interval from -2.585 to 13.51. This interval includes zero and allows for values on either side of zero. Its interpretation is limited by the summary-based, unadjusted calculation and by the absence of within-person covariance information for the crossover comparison. It should not be treated as a replacement for the sponsor's reported analysis.

Confidence intervals are not guarantees that the true value lies inside the displayed limits. In general, they reflect the uncertainty that would arise from repeated sampling under the method's assumptions. Precision depends on the observed variability, sample size, design, and analysis. The registry record reports 26 participants in each treatment group, but the exact sponsor model and its assumptions are not reported. The interval therefore conveys uncertainty as posted, while incomplete method details limit independent assessment of that uncertainty.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect, not the original trial's design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

For the primary comparison, planning for 100% of the observed effect gives 116 participants per arm for 80% power and 155 participants per arm for 90% power. Planning for 75% of the observed effect gives 206 participants per arm for 80% power and 275 participants per arm for 90% power. Planning for 50% of the observed effect gives 462 participants per arm for 80% power and 618 participants per arm for 90% power. The other outcomes have their own illustrations based on their respective observed estimates.

In plain terms, an 80% power target means that, if the assumed effect and model were correct, a study of that planned size would have an 80% chance of meeting the specified statistical significance criterion. A 90% target uses a higher chance under those assumptions and generally requires more participants. Smaller effects are harder to distinguish from background variability, so planning for a smaller effect requires more participants. These are planning illustrations, not observed power; they do not describe the chance that this completed study found a real effect.

The figures are sensitive to the observed effect used as their starting point. In a small study, that estimate may be uncertain, and an unusually large or small observed estimate can produce an unstable planning illustration. The values should therefore be read as conditional scenarios under the stated assumptions, not as a recommended sample size or as evidence about the quality of the original trial design.

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 = 5.460; pooled standard deviation σ = 14.800.
2. n = 2 × (1.96 + 0.842)² × 14.800² / 5.460² = 115.3, rounded up to 116 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 <- 5.45999999999999                      # observed difference in means
sigma <- 14.800337833982                     # 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(1247285)
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 = 116 (80% power), 155 (90% power)
 75% of observed effect: n per arm = 206 (80% power), 275 (90% power)
 50% of observed effect: n per arm = 462 (80% power), 618 (90% power)
power.t.test: 116.3 
Simulated power at n = 116 per arm: 0.796 (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 sponsor's posted primary result is a geometric-mean ratio rather than a difference in arithmetic means: 107.81, with a 90% confidence interval from 97.37 to 119.38. The registry labels the analysis as a ratio of the test-to-reference geometric mean multiplied by 100. It does not identify the method used to calculate the ratio or interval, and it does not report a p-value for this analysis.

The unadjusted recalculation from the posted means gives a difference of 5.46 ng/mL, with an interval from -2.585 to 13.51 and an unadjusted p-value of 0.183. This calculation does not replicate the sponsor analysis: it uses arithmetic means and a difference scale, and it does not incorporate the paired structure using individual participant data. The two estimates answer related but distinct statistical questions.

No discrepancy is flagged between the posted results and the recalculation. The sponsor result is the registry's own analysis for the stated relative-bioavailability question; the recalculation is an additional descriptive comparison, not a substitute for it. Because the method, acceptance limits, and detailed analysis plan are not reported in the registry record, the sponsor result cannot be fully audited or judged against a formal bioequivalence rule from this entry alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and six analyses overall, including the primary Cmax measure and three posted secondary norfluoxetine measures. It does not report a multiplicity strategy, such as an adjustment across outcomes or a hierarchy that would determine which tests were confirmatory. It also does not state whether the secondary analyses were planned before the data were examined. Without that information, unadjusted secondary p-values and intervals should be treated as exploratory evidence rather than as a collection of independently conclusive tests.

Missing-data handling is not described in the registry record. The primary outcome population is defined as all participants who completed the study and had their samples analyzed. This indicates a completer-based analysis description, but does not explain how many participants were randomized, whether any participants withdrew, or how missing samples or incomplete treatment periods were handled. Although enrollment was 26 and each product has 26 participants listed, the record does not provide a participant flow account or establish that every enrolled participant completed both periods.

The record does not report an intention-to-treat analysis, a per-protocol definition, or sensitivity analyses for missing data. It also does not describe protocol deviations, exclusions, or reasons for excluding observations. These details matter because the analyzed population can affect the interpretation of a treatment comparison, particularly when completion or measurement availability is selective.

The crossover design additionally raises questions about sequence, period, and carryover handling. The registry identifies the design but does not report a model or analyses addressing these features. It is therefore not possible to determine from the registry record whether the sponsor's analysis accounted for them, how missing measurements affected paired comparisons, or whether alternate analysis choices were tested.

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 non-serious adverse event terms

The posted serious adverse event figures list 26 participants at risk in each treatment group and zero serious adverse events in each group. No serious adverse event terms are listed. These counts describe what was recorded for the study; they do not establish that the products have no serious risks, especially in a study with a small healthy-volunteer population.

Other adverse events are listed for 11 participants in each group, with 26 at risk in each. The registry record does not provide further detail about the type, timing, severity, or relationship of those events to treatment in the material. Death counts are not reported in the registry record. The adverse event figures should be read as descriptive counts, not as a powered comparison of safety between products.

Because the study used a crossover design, the same participants may contribute observations under both products. The registry does not explain how adverse events were attributed or analyzed across treatment periods. Equal counts in the two groups do not, by themselves, establish equal safety profiles or rule out differences in event types or timing.

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

The results describe pharmacokinetic measurements after a single 90 mg dose of each product in healthy adults under non-fasting conditions. For the primary endpoint, the sponsor reports a test-to-reference geometric mean ratio of 107.81 with a 90% confidence interval from 97.37 to 119.38. The interval includes the equal-ratio value of 100, but it also covers values on both sides of that point. The registry does not report the prespecified acceptance limits needed to determine whether the interval met a formal bioequivalence criterion.

The unadjusted difference between posted means is 5.46 ng/mL, with an interval from -2.585 to 13.51. It is a distinct summary-based analysis and does not use the within-person pairing of the crossover design. Neither the sponsor interval nor the recalculated interval should be interpreted as proving exact equality. Failure to distinguish an effect from a reference value is not the same as demonstrating that the effect is absent.

The study does not compare symptom relief, disease outcomes, quality of life, or long-term use. It also does not establish how results would apply to people with a health condition, since the participants were healthy volunteers. Its focus is relative absorption following a single dose, with blood samples collected over a 25 day period.

Statistical uncertainty and incomplete reporting both matter. The registry does not give the sponsor's detailed model, the bioequivalence margin, the multiplicity approach, or full participant-flow and missing-data details. The posted results can be described, but these omissions prevent a complete independent assessment of the planned decision rule and its execution. No treatment recommendation follows from these registry results alone.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines a randomized crossover design with a pharmacokinetic comparison. A crossover design can make efficient use of a small participant group by comparing products within the same individuals. That benefit depends on a suitable analysis that accounts for the pairing and relevant period or sequence features. The registry identifies the crossover structure but does not provide enough detail to evaluate how those features were handled.

The difference between the sponsor's geometric-mean ratio and an unadjusted difference in arithmetic means illustrates why the estimand and scale matter. Both summarize a comparison of the products, but they are not the same quantity and need not be interpreted in the same way. The primary result is expressed as a ratio because that is the sponsor's reported form; the recalculation gives an unadjusted difference from group means. Treating them as interchangeable would obscure the analysis question.

The confidence interval is as important as the point estimate. A point estimate alone can make a comparison appear more decisive than the underlying precision supports. Here, the primary ratio interval extends to either side of 100. Without the acceptance limits, the interval cannot be translated into a registry-based bioequivalence decision. This shows why full reporting of decision thresholds and methods is essential for interpreting relative-bioavailability studies.

Finally, the record highlights the distinction between planned design assumptions and retrospective planning illustrations. The displayed planning scenarios are based on observed effects, not the original trial design. They do not reveal the rationale for enrolling 26 participants. Understanding that rationale would require a sample-size justification and protocol details that are not reported in the registry record.

19. Limitations

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

The registry entry leaves several trial-specific details unavailable. Although it identifies randomization and a crossover model, it does not report the treatment sequence, washout duration, period structure, or whether carryover was assessed. These details would help readers evaluate the design and the validity of a paired comparison.

The sponsor analysis method is not identified, and the record does not report its model assumptions or the bioequivalence acceptance limits. The reported ratio and confidence interval can be described, but the decision rule cannot be reconstructed. The unadjusted recalculation from group summaries does not use participant-level paired data, so it cannot address the design as fully as an appropriate crossover analysis could.

The primary analysis population is described as participants who completed the study and had samples analyzed. The registry does not provide a participant flow, reasons for withdrawal or exclusion, missing-sample handling, or sensitivity analyses. It also does not report a multiplicity approach for the secondary outcomes or clarify the status of all six listed outcome measures and analyses.

The sample is small and consists of healthy adults receiving a single dose. The record does not give demographic details that would support assessment of population coverage. Safety results are descriptive, with no serious adverse events listed and other adverse events recorded, but the registry does not describe event types or provide enough detail for a comparative safety assessment. These limitations constrain interpretation of the registry entry; they do not establish that unreported procedures were absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: 90 mg Fluoxetine Hydrochloride Capsules Under Non-Fasting Conditions — NCT01247285.
• Registry record last updated 2011-02-21; status last verified 2011-01.
• Results first posted 2011-02-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed Phase 1 study compared a single 90 mg dose of Teva Fluoxetine Hydrochloride Capsules with 90 mg PROZAC WEEKLY® in 26 healthy adults under non-fasting conditions. It was randomized, unmasked, and crossover. The primary endpoint was fluoxetine Cmax, measured using blood samples collected over a 25 day period.

The sponsor reported a test-to-reference geometric mean ratio of 107.81 with a 90% confidence interval from 97.37 to 119.38. An unadjusted recalculation of posted means gave a difference of 5.46 ng/mL, with an interval from -2.585 to 13.51 and an unadjusted p-value of 0.183. These analyses use different scales and are not interchangeable. The registry record does not report the bioequivalence acceptance limits or detailed sponsor method.

Three secondary norfluoxetine outcomes are listed. Serious adverse events were recorded for zero participants in each treatment group; other adverse events were recorded for 11 participants in each. The record does not report a multiplicity strategy, full missing-data handling, or detailed crossover analysis methods.