Study of Glycopyrronium in Axillary Hyperhydrosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Glycopyrronium in Axillary Hyperhydrosis (NCT02530281), a randomized phase 3 study. The primary outcome is Percentage of Subjects Who Have a ≥4-point Improvement in the Weekly Mean Score of ASDD Item #2 From Baseline at Week 4.

2. Clinical Question

The primary endpoint is a responder outcome: each participant either met the specified improvement threshold or did not. In the posted results, 52.8% of participants in the glycopyrronium group met that threshold, compared with 28.3% in the vehicle group. These percentages describe the endpoint response in the two groups; they do not describe the average score change for every participant.

The endpoint is one measure of symptom severity. Two secondary outcomes assess improvement on the Hyperhidrosis Disease Severity Scale and reduction in gravimetrically measured sweat production. Together, these outcomes address diary-rated sweating, reported disease severity, and measured sweat production. The primary question remains specifically about the ASDD Item 2 response at Week 4, not about every dimension of hyperhidrosis or about longer-term outcomes.

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, vehicle-controlled, parallel-group study of glycopyrronium topical wipes in participants with axillary hyperhidrosis. The listed masking is quadruple. The study is marked completed, and the registry lists enrollment of 344 participants. Its brief summary says the wipes were used once daily and that the study assessed efficacy and safety against vehicle.

The primary endpoint compares the percentage meeting a prespecified improvement threshold at Week 4. The glycopyrronium group had 229 participants in the posted primary outcome, and the vehicle group had 115. The observed responder percentages were 52.8% and 28.3%, respectively. These outcome denominators add to the registry enrollment, but the record does not describe the analysis population or explain how participants with missing Week 4 data were handled. The safety denominators are different: 227 and 114, respectively.

Randomization and masking are important design features because they can reduce systematic differences in treatment assignment and expectations between groups. Vehicle control provides a comparator for the active wipe formulation, while the parallel-group design means participants were assigned to one study group rather than moving between treatments. These are general descriptions of design concepts; the registry does not report the operational details of sequence generation, concealment, masking procedures, or the vehicle formulation.

The registry lists the study start as 2015-07 and primary completion as 2016-03. It does not report the planned sample-size justification, the original target enrollment, protocol deviations, the timing of any interim analyses, or details of the statistical analysis plan. Those items should not be inferred from the final enrollment or from planning illustrations based on the observed results.

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

Analysis population for the primary outcome, as defined in the registry: Participant

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 Percentage of Subjects Who Have a ≥4-point Improvement in the Weekly Mean Score of ASDD Item #2 From Baseline at Week 4, measured over From Baseline to Week 4.

The primary endpoint is the percentage of participants with at least a four-point improvement from baseline in the weekly mean score for ASDD Item 2 at Week 4. Item 2 asks participants to rate how severe their underarm sweating was at its worst during the past 24 hours. The diary description gives a scale from 0, meaning no sweating at all, to 10, meaning worst possible sweating.

ASDD is described as a four-item instrument intended to measure axillary hyperhidrosis severity and its impact on daily activities. Its other items ask whether underarm sweating occurred, how much it affected activities, and how bothered the participant was. The primary endpoint therefore focuses on a change in the participant's rating of worst sweating, rather than the impact or bother items.

A threshold-based endpoint is often useful because it expresses results as the proportion meeting a defined response criterion. It is not the same as reporting the mean score change: participants just meeting the threshold and participants exceeding it are both counted as responders. The registry reports the responder percentages but does not describe the validation basis for the particular four-point threshold, the baseline score distribution, or the handling of diary entries needed to form the weekly mean. Those details are not reported in the registry record.

7. Results Posted in the Registry

• Glycopyrronium: 52.8% (121/229) versus 28.7% (33/115) on control; risk difference 24.1 percentage points (95% CI 13.6 to 34.6), risk ratio 1.84 (1.35–2.52); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Subjects Who Have a ≥2 Grade Improvement in Hyperhidrosis Disease Severity Scale (HDSS) From Baseline at Week 4

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Glycopyrronium: 56.3% (129/229) versus 23.5% (27/115) on control; risk difference 32.9 percentage points (95% CI 22.8 to 42.9), risk ratio 2.40 (1.69–3.40); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Glycopyrronium than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Subjects Who Have at Least a 50% Reduction in Gravimetrically Measured Sweat Production From Baseline at Week 4

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Glycopyrronium: 72.5% (166/229) versus 53.0% (61/115) on control; risk difference 19.4 percentage points (95% CI 8.6 to 30.2), risk ratio 1.37 (1.13–1.65); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Glycopyrronium than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Both posted secondary outcomes have higher response percentages in the glycopyrronium group than in the vehicle group, and both registry analyses report p < 0.001. This gives a consistent broad direction across the primary diary-based endpoint and secondary measures based on disease-severity improvement and gravimetrically measured sweat reduction. The secondary outcomes therefore provide related evidence about different aspects of the condition, rather than simply repeating the primary measurement.

The secondary outcomes are not identical in what they measure. HDSS improvement reflects a threshold on a disease severity scale, while the sweat-production outcome concerns a threshold reduction in gravimetrically measured production. Agreement in direction across distinct measures can be informative, but it does not eliminate the need to consider how each endpoint was defined, analyzed, and handled when data were missing. Details about those matters are not reported in the registry record.

Secondary results generally carry less confirmatory weight when the statistical plan does not report how multiple outcomes were handled. Testing several endpoints creates more opportunities for a statistically significant result by chance across the collection of tests. This is a general multiplicity concern, not evidence that any particular posted result is false. The registry lists six outcome measures and six analyses, but does not report a multiplicity adjustment or a hierarchy governing interpretation of secondary findings.

The secondary results should therefore be read as supportive descriptions of the pattern in the posted data, not as a replacement for the primary comparison or as independent proof of an effect. Their interpretation is limited by the missing details about multiplicity, analysis populations, and missing-data handling. The registry also does not report a combined endpoint or a formal synthesis across the primary and secondary outcomes.

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

• Percentage of Subjects Who Have a ≥2 Grade Improvement in Hyperhidrosis Disease Severity Scale (HDSS) From Baseline at Week 4
• Percentage of Subjects Who Have at Least a 50% Reduction in Gravimetrically Measured Sweat Production From Baseline at Week 4

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a Cochran-Mantel-Haenszel test for the primary comparison. The posted arm percentages and response counts also permit a simple unadjusted comparison of the proportions. These are related but not identical approaches: the registry analysis is the sponsor-reported method, while the recalculation uses the summary counts without adjustment. The registry does not give the strata or other implementation details for its reported method.

What does a responder proportion measure?

A binary responder outcome classifies participants according to whether they crossed a defined threshold. Here, the threshold is at least a four-point improvement in the weekly mean ASDD Item 2 score from baseline to Week 4. The reported percentages are the proportions classified as responders within each arm. This presentation is straightforward to interpret, but it discards information about the size of changes beyond the threshold. Two participants with different score changes can count identically if both meet the criterion.

For a two-group binary outcome, a risk difference is the difference between the two response proportions. It expresses the contrast on the absolute proportion scale. A risk ratio compares the proportions as a relative quantity, and an odds ratio compares the odds of response. These measures answer different questions and can communicate the same data in different ways. The posted recalculation includes these measures, but the explanations focus on the response percentages and the unadjusted risk-difference interval. No newly calculated effect measure is introduced.

What does the reported test contribute?

The Cochran-Mantel-Haenszel method is a general method for comparing categorical outcomes across groups while accounting for strata. The registry identifies this method but does not say which strata were used, how they were formed, or how missing outcomes were treated. It is therefore possible to identify the named method, but not to reconstruct all details of the sponsor's analysis from the record. The reported result is p < 0.001.

The simple recalculation is not the same as the registry's Cochran-Mantel-Haenszel analysis. It is an unadjusted calculation from the posted response counts. Its value is transparency: readers can relate the arm-level counts to an unadjusted contrast and its interval. It cannot reproduce undocumented features of the sponsor's method, and should not be described as an adjusted result. The registry does not report a sponsor effect estimate or interval alongside its p-value.

Why distinguish an estimate from a p-value?

An effect estimate describes the direction and magnitude of a contrast on a chosen scale. A confidence interval describes uncertainty around an estimate under a specified method. A p-value evaluates compatibility with a null model under assumptions. These summaries are complementary, not interchangeable. A small p-value alone does not convey the size of a contrast, the range of values compatible with the data, or the relevance of the result to a clinical decision.

General statistical interpretation also depends on the analysis population, outcome ascertainment, and missing-data rules. Randomization supports a comparison of assigned groups, but the interpretation of an analyzed result still depends on who was included and how incomplete observations were handled. The record lists the arm denominators for the outcome, but it does not report an intention-to-treat definition, a per-protocol population, imputation methods, or sensitivity analyses. No assumptions about those choices should be made.

What role does over-dispersion play?

Over-dispersion is a general concern when observed variability exceeds what a statistical model assumes. For a binary outcome, the basic response is each participant's responder status, and methods may differ in how they account for stratification, clustering, or other design features. The registry does not report over-dispersion as an issue or describe a model for the primary outcome beyond naming the Cochran-Mantel-Haenszel method. It would be inappropriate to claim that over-dispersion was assessed or to infer its effect on the results.

What is the role of the confidence interval?

In general, a confidence interval gives a range of estimates compatible with the observed data and the method used, reflecting sampling uncertainty. It is not a range containing a fixed proportion of individual participant outcomes, and it is not the probability that the true effect lies in the particular interval. The recalculated interval for the primary unadjusted risk difference has bounds above zero. The registry's reported analysis does not include its own effect interval or confidence level in the listed result, so the recalculated interval should remain clearly distinguished from the sponsor's reported test.

11. Confidence Intervals and Precision

The posted arm percentages are 52.8% for glycopyrronium and 28.3% for vehicle. A percentage alone does not show how uncertain the underlying response proportion or between-group contrast may be. The recalculation includes a confidence interval for the unadjusted risk difference, and its lower and upper limits are both above zero. This indicates that the interval does not include a zero difference under the recalculation's method.

A confidence interval is useful because it presents a range of estimates compatible with the observed data under specified assumptions. General interpretation should focus on both its location and its width: an interval entirely on one side of zero supports a directional contrast in this calculation, while a wider interval indicates less precision about its exact magnitude. The registry does not report the confidence level for the sponsor's analysis, and it does not report a sponsor effect interval for the primary endpoint. No numerical interval limits are repeated because the recalculated limits are stated to more than three decimal places in the record.

Precision is affected by the number of observed responses and nonresponses, as well as by the analysis method. The primary outcome denominators were 229 and 115, and the recalculation uses the posted counts. These denominators are not interchangeable with the safety denominators, which were 227 and 114. The registry does not explain the difference between the outcome and safety populations.

An interval does not resolve questions about missing data, measurement, or clinical importance. The record does not state how missing diary data were handled or give a clinically important threshold for the between-group contrast. The unadjusted interval therefore describes statistical uncertainty for the summary-count comparison, not every source of uncertainty relevant to interpretation.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations are participants per arm, not total events. They are planning illustrations derived from the observed effect, not the trial's original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the estimated participants per arm for a planning scenario designed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding per-arm planning count for a 90% chance. Higher planned power generally requires more participants for the same effect. These are prospective planning quantities; they do not describe the probability that the completed trial found a true effect.

The rows consider planning for 100%, 75%, and 50% of the observed effect. For the primary endpoint, the corresponding 80% power figures are 64, 112, and 244 participants per arm; the 90% power figures are 85, 149, and 325 participants per arm. The figures increase as the target effect becomes smaller, because smaller differences are harder to distinguish from sampling variation. The secondary endpoint calculations have their own observed effects and therefore different planning counts.

These illustrations are not observed power. They do not establish that the trial was adequately powered under its original design, because the original sample-size justification and design assumptions are not reported in the registry record. Planning from an observed effect is also conditional on that effect being a useful planning value; it should not be read as a new estimate of the trial's success or as a guarantee of future results.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.287; treatment proportion p₁ = 0.528; average p̄ = 0.408.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6949 = 1.3621.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6737 = 0.5670.
4. n = (1.3621 + 0.5670)² / (0.2414)² = 63.8, rounded up to 64 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 <- 0.28695652173913                          # control proportion
p1 <- 0.528384279475983                          # 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(2530281)
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 = 64 (80% power), 85 (90% power)
 75% of observed effect: n per arm = 112 (80% power), 149 (90% power)
 50% of observed effect: n per arm = 244 (80% power), 325 (90% power)
power.prop.test: 63.8 
Simulated power at n = 64 per arm: 0.807 (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.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary comparison using the Cochran-Mantel-Haenszel method, with p < 0.001. It does not list a sponsor-reported effect estimate, confidence interval, or detailed description of the strata for that analysis. The posted arm response percentages and counts support a separate, simple unadjusted recalculation, which also reports p < 0.001 and includes an unadjusted risk-difference interval.

The recalculation is useful for interpreting the contrast from the published summary counts, but it is not a reproduction of the sponsor's analysis. The two methods may differ because one is identified as Cochran-Mantel-Haenszel and the other is unadjusted. The record does not provide enough detail to determine the exact consequences of that distinction for the sponsor's result.

The discrepancy flag is false, and both analyses report p < 0.001. This does not make the recalculation adjusted, nor does it supply the sponsor's missing effect estimate or interval. The sponsor result should be described as the registry's reported analysis; the recalculation should be described as an unadjusted analysis of posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and six analyses. It identifies one primary endpoint and two secondary endpoints in the posted results. It does not report whether the testing plan adjusted for multiple comparisons, assigned a testing hierarchy, or treated any secondary outcomes as confirmatory. Without such information, the reported p-values should not be interpreted as if the multiplicity issue were resolved. This is a limitation in what the record documents, not a claim about what may have been specified elsewhere.

The record reports a Cochran-Mantel-Haenszel method for the primary and secondary analyses, but does not provide the detailed analysis plan, strata, covariates, or implementation choices. The registry does not report whether an interim analysis occurred, whether any interim monitoring rule was used, or whether outcomes were analyzed according to a prespecified protocol. Those details are not reported in the registry record.

The outcome denominators are listed for each arm, but the record does not explain the analysis population. It does not specify whether the primary analysis included all randomized participants, how eligibility after randomization was handled, or whether a per-protocol analysis was performed. Missing-data procedures are also not reported: there is no stated imputation method, rule for incomplete diary records, or sensitivity analysis for missing outcomes.

These omissions matter because the interpretation of a randomized comparison depends not only on assignment but also on the analysis set and outcome availability. Different missing-data assumptions can affect a responder proportion, particularly when a participant's outcome cannot be classified from the available diary data. No assumption about such handling can be recovered from the arm denominators alone.

The registry does not report the protocol's original sample-size justification or its planned statistical assumptions. The planning illustrations based on observed effects are separate from that missing design information. Taken together, the record supports describing the posted estimates and named analyses, while leaving important aspects of confirmatory interpretation undocumented.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: unilateral mydriasis (0.4%).

The safety summaries list serious adverse events among 227 participants in the glycopyrronium group and 114 in the vehicle group. There was one participant with a serious adverse event in the glycopyrronium group and none in the vehicle group. The listed serious event term is unilateral mydriasis, reported as 0.4%. Deaths are listed as zero in both groups.

The record also lists other adverse events affecting 68 participants in the glycopyrronium safety group and 16 in the vehicle safety group. These are counts of participants affected, not counts of all event occurrences. The registry does not provide further detail about the other adverse events in this summary or their severity, timing, or relationship to study treatment.

These figures describe the posted safety record, but they do not establish whether an event was caused by a treatment. The registry does not report the observation period for these safety counts or additional details about event adjudication. The safety denominators differ from the primary outcome denominators, and the record does not explain that difference. Rare-event counts should be read cautiously because the displayed counts alone provide limited precision about event rates.

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

The posted primary results show that a greater percentage of participants in the glycopyrronium group met the specified ASDD Item 2 improvement criterion at Week 4 than in the vehicle group. The registry's reported test has p < 0.001, and the unadjusted recalculation gives a confidence interval for the risk difference with both bounds above zero. These findings describe the observed comparison for the endpoint and time point recorded.

They do not show that every participant improved, that the same response would occur in a different population, or that the observed contrast persists beyond Week 4. The endpoint is a threshold response based on a diary score; it does not report the full distribution of score changes. The result also does not by itself establish how participants experienced changes in daily activities or bother, even though the ASDD instrument includes separate items on those topics.

A statistically significant result is not automatically a measure of clinical importance. The registry does not report a threshold for a clinically important between-group difference, and the p-value does not quantify the value of the result to an individual. The posted secondary outcomes address other measurements, but their interpretation is limited by the absence of reported multiplicity procedures and further analysis details.

Randomization and masking are features of the reported design, but the record does not provide all operational details needed to assess implementation. Missing-data handling, analysis populations, and the original statistical plan are not reported. These limitations do not erase the posted arm-level results; they define what can and cannot be concluded from the registry record alone.

The safety summary records one serious adverse event in the glycopyrronium group, none in the vehicle group, and no deaths in either group. These counts are descriptive and do not establish causation or characterize all potential safety outcomes. The registry findings are therefore best understood as a comparison of specific efficacy and safety summaries, with uncertainty about unreported methods and information beyond the recorded outcomes.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint must be understood before interpreting a treatment comparison. The primary outcome is not a general measure of all symptoms: it is the proportion meeting a four-point improvement criterion on the weekly mean of a particular diary item at Week 4. That definition determines what the percentages mean and what they leave out.

It also demonstrates the value of distinguishing an arm-level percentage, an effect estimate, a confidence interval, and a p-value. The percentages describe observed response proportions. The unadjusted risk-difference interval adds information about uncertainty in their contrast, while the reported Cochran-Mantel-Haenszel p-value represents the registry's named test. These are complementary summaries, and the record does not provide enough detail to treat the unadjusted calculation as a reconstruction of the reported analysis.

The secondary outcomes raise a further general issue: repeated testing across outcomes can affect how strongly individual p-values support confirmatory conclusions. The registry lists several outcomes but does not report a multiplicity plan. Recognizing this gap helps avoid overstating supportive findings without dismissing the observed pattern.

Finally, sample-size planning based on an observed effect is not the same as the original design calculation or observed power. The planning illustrations show how required participants per arm change when the target effect changes, under stated assumptions. They do not reveal the trial's original rationale, which is not reported. The distinction is useful for preventing retrospective planning figures from being mistaken for evidence about whether the completed study was adequately designed.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific details unavailable. It does not describe the eligibility criteria in detail, the baseline characteristics of the randomized groups, the sequence-generation procedure, allocation concealment, or the practical methods used to maintain quadruple masking. The vehicle is named, but its composition is not described in the posted record. These omissions limit assessment of how the design was implemented and how broadly the results may apply.

The primary endpoint is based on diary ratings, but the record does not state the minimum diary completion required to calculate a weekly mean, the handling of incomplete entries, or the imputation approach for missing endpoint data. It also does not provide the analysis population definition. The outcome denominators are 229 and 115, while safety denominators are 227 and 114; the reason for this difference is not reported.

The sponsor reports a Cochran-Mantel-Haenszel analysis, but does not identify its strata or provide a primary effect estimate and confidence interval in the listed result. The unadjusted recalculation supplies a separate summary-count analysis, not a substitute for those missing details. Multiplicity procedures, interim analyses, protocol deviations, and sensitivity analyses are not reported.

The posted primary and secondary results assess outcomes at Week 4. Longer-term outcome information is not reported in these results. The record also does not report a clinically important threshold for the between-group contrast or enough detail to assess the importance of the observed effect to participants. Safety summaries are limited to the listed counts and do not provide fuller event descriptions, attribution, or observation-period details.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Glycopyrronium in Axillary Hyperhydrosis — NCT02530281.
• Registry record last updated 2021-08-25; status last verified 2021-08.
• Results first posted 2018-08-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, double-blind, vehicle-controlled, parallel-group Phase 3 study of once-daily glycopyrronium topical wipes for axillary hyperhidrosis. Enrollment was 344, with 229 participants in the glycopyrronium primary outcome group and 115 in the vehicle group. The primary endpoint was the percentage with at least a four-point improvement in the weekly mean ASDD Item 2 score from baseline to Week 4.

The posted primary response percentages were 52.8% with glycopyrronium and 28.3% with vehicle. The registry reports a Cochran-Mantel-Haenszel p-value of p < 0.001. The simple unadjusted recalculation also reports p < 0.001 and gives a risk-difference interval whose limits are above zero. The registry does not report the sponsor's effect estimate or interval, detailed analysis populations, missing-data procedures, or multiplicity plan. Safety summaries list one serious adverse event in the glycopyrronium group, none in the vehicle group, and zero deaths in both groups.