Field of Effects of Two Commercial Preparations of Botulinum Toxin Type A: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Field of Effects of Two Commercial Preparations of Botulinum Toxin Type A (NCT00989768), a randomized phase 4 study. The primary outcome is Horizontal Action Halo Diameter at 28 Days.

2. Clinical Question

3. Trial Design

The registry identifies this as a completed phase 4 trial with randomized allocation, double masking, and a parallel-group model. The listed condition is wrinkles in the frontal area, and the official title describes the preparations as administered to the frontalis muscles. The sponsor is Hexsel Dermatology Clinic. The recorded start is 2005-05, primary completion is 2007-11, and enrollment is 29.

The primary outcome compares Dysport® 5U with Botox® 2U. Each outcome arm lists 28 participants. The registry does not reconcile the arm counts with the recorded enrollment, so the relationship between those figures is unclear from the record alone. It also does not state whether all enrolled participants contributed primary endpoint data or describe any exclusions from the analysis population.

The intervention listings include Dysport® and Botox® preparations, with Dysport® appearing in more than one intervention entry. The arm description characterizes the comparison as Dysport® versus Botox®. Details such as the randomization sequence, allocation concealment, dosing procedure, and the roles of the masked participants are not reported in the registry record. The protocol’s original sample-size assumptions and its statistical analysis plan are also not reported.

The registry describes the study objective as comparing the field of effects using two equivalence-ratios, alongside supportive information about wrinkle reduction and duration of action. The equivalence-ratios themselves and any formal equivalence margin are not reported in the registry record. The posted primary analysis is labelled as a two-sided t-test and as a superiority-or-other analysis; the record does not explain the relationship between that analysis and the stated objective of comparing equivalence-ratios.

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.

Before assignment: 13 volunteers were excluded; Screen failure: Iodine allergy = 2; Minor´s Test failure = 6 Mild wrinkles = 3 Inclusion criteria failure = 2 Minor's test allows the visualization of the area covered by the effects of botulinum toxin on sweat glands also known as action halos.

Overall Study

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 Horizontal Action Halo Diameter at 28 Days, measured over 28 Days.

The primary endpoint is the horizontal action-halo diameter at 28 days, measured in centimeters and summarized as a mean with a standard deviation. The registry describes the halo as the colored area produced by Minor’s test, which visualizes the area where botulinum toxin affects sweat glands. The diameter was quantified using Mirror® software.

This measurement is used to represent the spatial extent of the observed field effect. Comparing group means addresses whether the average measured horizontal extent differed between the two preparations at the specified time. A diameter is a one-dimensional measure of the halo, however, and does not describe its full shape or area. The result is also not a direct measure of wrinkle reduction, patient experience, or duration of action.

The endpoint is recorded at 28 days. Although the study objective mentions wrinkle reduction and duration as supportive information, the primary outcome entry does not describe those as part of this endpoint. The registry record does not report additional measurement details such as the number of readings per participant, the handling of repeated measurements, or whether measurement assessment was blinded.

7. Results Posted in the Registry

• Botox® 2U: mean 1.12 versus 1.28 on control; difference -0.16 (95% CI -0.31 to -0.01), standardized effect d = -0.56; z-test p = 0.036.

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.

ECMAP in m. Frontialis

• 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:
  • Botox ® 2U: mean 468.27 versus 492.53 on control; difference -24.26 (95% CI -169.54 to 121.02), standardized effect d = -0.09; z-test p = 0.743.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Botox ® 2U and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoint information concerns electrical muscle activity in the frontalis muscle at 28 days. Its recalculated estimate is close to zero relative to the variability, and its confidence interval is broad and crosses zero. The recalculated p-value is 0.743, while the registry’s reported secondary analysis gives p = 0.61. The record does not provide a reported effect estimate or interval for that sponsor analysis.

This pattern does not mirror the primary result’s p-value pattern: the primary recalculation gives p = 0.036, whereas the secondary recalculation gives p = 0.743. The endpoints also measure different things. The primary measure is a diameter in centimeters representing the visible halo; the secondary measure is electrical muscle activity in microvolts. They should not be treated as interchangeable measures of one underlying outcome.

In general, secondary outcomes are often interpreted with less weight than a prespecified primary outcome, especially when many endpoints or comparisons are tested. Testing multiple hypotheses increases the chance that at least one result appears statistically notable by chance. Whether the trial adjusted for multiplicity, and how its secondary outcomes were prioritized, are not reported in the registry record. The unadjusted secondary results therefore warrant cautious interpretation and should not be used alone to make broad claims.

The registry lists ECMAP in the frontalis twice among secondary outcomes and records two secondary outcomes posted. The available outcome details do not establish whether these entries represent distinct measures, repeated listings, or different analyses. The registry record does not clarify that point. Overall, the secondary information provides an additional physiological measurement but does not resolve the uncertainty about the broader interpretation of the primary comparison.

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

• ECMAP in m. Frontialis
• ECMAP in m. Frontialis

9. Statistical Interpretation

10. Statistical Methods Explained

For a continuous endpoint, a group mean summarizes the average measured value among the participants included in that group’s analysis. The standard deviation describes the spread of individual measurements around that group mean. It is not the same as the uncertainty around the mean: uncertainty in a mean comparison also depends on the number of observations and the variability of the measurements.

What does a mean difference represent?

The primary outcome is a continuous measurement in centimeters. A mean difference subtracts one group mean from the other. The recalculation uses Botox® minus Dysport®, so its estimate of -0.16 cm indicates that the posted Botox® mean is lower in this ordering. Reversing the order changes the sign, not the underlying distance between the two means. It is important to state the ordering because the sign alone has no interpretation without it.

The reported analysis gives a positive mean difference of 0.16. This is compatible with describing the comparison in the reverse direction, although the registry does not explicitly state the subtraction order for that result. The recorded method is a two-sided t-test. In general, a two-sided test assesses evidence for a difference in either direction rather than prespecifying only one direction. The registry does not give enough detail to determine whether the sponsor used precisely the same calculation as the unadjusted recalculation.

What does the confidence interval add?

In general, a confidence interval gives a range of values reasonably compatible with the observed data under the assumptions of the calculation. It communicates uncertainty about the estimated difference, whereas a point estimate gives only one central value. A narrow interval indicates greater precision than a wide interval on the same measurement scale. It does not represent a range containing a fixed proportion of individual participant measurements, and it does not guarantee that the true value lies within the realized interval.

For the primary recalculation, the interval is on the negative side and approaches zero at its upper end. This indicates that the summary statistics are compatible with a negative mean difference in the specified ordering, while values close to no difference are also near the interval boundary. The registry does not post confidence-interval bounds for its own analysis. The secondary interval is much broader in relation to its estimate and crosses zero, indicating substantial uncertainty about the direction and size of that secondary mean difference.

Why can standard deviations and sample sizes matter?

In general, the standard error of a mean difference reflects both the variability in the groups and the amount of information available. More variable measurements or fewer observations tend to increase uncertainty, all else equal. The primary groups each list 28 participants, with standard deviations of 0.26 cm and 0.31 cm. The recalculation uses the posted group summaries and is unadjusted. It does not incorporate participant-level data, covariates, or any undisclosed analysis choices.

The registry’s enrollment is 29, while each primary arm lists 28 participants. These quantities should not be treated as interchangeable. The record does not say how many participants were randomized, treated, measured, or included in each analysis, nor does it explain the relation between enrollment and the arm counts. Without those details, it is not possible to assess from the registry whether the comparison used a complete analysis population or whether exclusions occurred.

Why does over-dispersion matter in general?

For count outcomes, over-dispersion means that the observed variability exceeds what a basic model assumes. Ignoring it can make standard errors too small and uncertainty look less than it is. The outcomes discussed in the posted primary and secondary summaries are continuous means, not counts, so over-dispersion is not the central issue for these comparisons. More generally, the statistical model should match the outcome’s scale and variability; the registry record does not give a detailed model specification beyond the listed t-test for the reported comparison.

What can and cannot be inferred from the p-values?

In general, a p-value measures how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of a difference. The recalculated primary p-value is 0.036, while the registry’s reported value is p < 0.001. Since the record does not explain the discrepancy, these values should be distinguished rather than combined into a single claim.

The registry labels the primary analysis as superiority-or-other and describes an objective involving equivalence-ratios. In general, demonstrating equivalence requires a prespecified acceptable margin and an analysis that evaluates the estimate’s uncertainty against that margin. The margin and the ratios are not reported in the registry record. A test for a difference, by itself, does not establish equivalence or show that two treatments are sufficiently similar for a particular purpose.

11. Confidence Intervals and Precision

The primary recalculation estimates a Botox®-minus-Dysport® mean difference of -0.16 cm. Its 95% confidence interval remains negative but reaches close to zero. Thus, the interval indicates a directionally consistent estimate while also leaving room for a small difference near zero. Because the interval bounds are not reproduced to more than three decimal places, the numerical bounds are not stated.

Precision is about the range of effects reasonably compatible with the data, not simply whether a p-value crosses a conventional threshold. An interval that approaches zero makes clear why the estimated difference should be read with attention to uncertainty, even though the recalculated p-value is 0.036. The registry’s analysis reports p < 0.001 but does not report its confidence-interval bounds, so its precision cannot be evaluated from that analysis entry in the same way.

For the secondary electrical muscle activity measure, the recalculated 95% interval extends from -169.5 to 121.0 microvolts around an estimate of -24.26 microvolts. It includes zero and a broad range of values in both directions. This is limited precision for distinguishing the size or direction of the group difference. In general, confidence intervals depend on the data and the analysis assumptions; they do not account for unreported sources of bias, measurement error, or selective reporting.

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 events. They are illustrations based on the observed primary effect, not the original trial’s design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

For example, planning for 75% of the observed primary effect gives 90 participants per arm for 80% power and 120 participants per arm for 90% power. The 80% power column means that, under the stated assumptions and if the chosen effect were the true effect, the design would have an 80% chance of detecting that effect using the stated testing framework. The 90% column describes the analogous planning target with a higher chance of detection. These are design probabilities, not guarantees for a particular study.

The figures increase as the effect to detect becomes smaller: a smaller difference is harder to distinguish from sampling variation, so more participants are generally required under the same assumptions. For the primary outcome, planning for the full observed effect gives 51 participants per arm for 80% power and 68 for 90% power; planning for 50% gives 201 and 269 per arm, respectively. These are planning illustrations, not observed power. The registry does not state that these illustrations were used to design or size the trial.

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 = -0.160; pooled standard deviation σ = 0.286.
2. n = 2 × (1.96 + 0.842)² × 0.286² / -0.160² = 50.2, rounded up to 51 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 <- -0.16                      # observed difference in means
sigma <- 0.286094390018399                     # 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(989768)
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 = 51 (80% power), 68 (90% power)
 75% of observed effect: n per arm = 90 (80% power), 120 (90% power)
 50% of observed effect: n per arm = 201 (80% power), 269 (90% power)
power.t.test: 51.2 
Simulated power at n = 51 per arm: 0.800 (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 registry’s primary reported analysis is a two-sided t-test. It lists a mean difference of 0.16 and p < 0.001. The unadjusted recalculation from the posted group summaries gives a Botox®-minus-Dysport® difference of -0.16 cm and p = 0.036. The estimates have the same magnitude when the comparison direction is reversed, but the p-values differ substantially. The registry does not explain why.

The sign can depend on which group is subtracted from which, so the positive reported estimate and negative recalculated estimate may reflect opposite ordering. The record does not state the sponsor’s subtraction order explicitly. The recalculation is based on the posted means, standard deviations, and group counts; the registry’s reported result is the trial’s own analysis entry. Its confidence-interval bounds are not reported.

The discrepancy flag in the record is false, but that does not explain the numerical difference between the two p-values. No reason for the difference is reported in the registry record. The reported analysis and the unadjusted recalculation should therefore remain distinct, with neither treated as a substitute for the other.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists four outcome measures and four analyses, and the secondary outcome name ECMAP in the frontalis appears twice in the outcome listing. It does not describe a prespecified hierarchy among secondary outcomes, a correction for multiple testing, or whether any secondary analyses were exploratory. Those details are not reported in the registry record.

In general, multiplicity arises when several outcomes, time points, groups, or hypotheses are examined. If each is tested separately without adjustment, the chance of at least one apparently unusual result can rise. This is why a secondary p-value should be interpreted in the context of the full set of analyses and the analysis plan. The registry does not provide enough information to judge whether the posted tests were adjusted or how multiplicity was handled.

The record also does not report a missing-data method, the number of missing primary or secondary measurements, reasons for missingness, or sensitivity analyses. The outcome-arm counts are 28 in each primary group, while overall enrollment is 29; the record does not explain the relationship. Consequently, the extent and handling of any missing outcome data cannot be determined from the registry record.

Analysis-population definitions are not reported. The record does not say whether analyses used all randomized participants, only treated participants, participants with an available measurement, or another population. Nor does it explain exclusions or deviations from assigned treatment. These omissions limit assessment of whether the posted comparisons preserve the advantages of randomization and how robust the results are to participant inclusion choices.

The trial’s detailed statistical analysis plan, including any planned interim analyses, is not reported in the registry record. No interim analysis should be inferred from the available information. Similarly, no missing-data mechanism or imputation approach can be assumed. These gaps matter because analytic decisions can influence estimates, uncertainty, and the interpretation of tests.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event entry lists 29 participants at risk for serious adverse events and zero serious adverse events. It also lists 29 participants at risk for other adverse events and one affected participant. The registry does not list a death count, so deaths are not reported in the registry record.

These are counts, not estimates that establish the frequency of events beyond the recorded group and observation period. The registry entry does not give event descriptions for the one other adverse event, the observation duration for safety, or a breakdown by treatment arm. No serious adverse-event terms are listed. A zero count in this record does not show that serious events are impossible or that the preparations have no safety risks; it means none are reported in the listed serious-event count.

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

The posted primary summaries show different average action-halo diameters at 28 days: 1.28 cm for Dysport® 5U and 1.12 cm for Botox® 2U. The unadjusted recalculation gives a Botox®-minus-Dysport® mean difference of -0.16 cm, with a 95% confidence interval that stays negative but approaches zero. The registry’s own analysis reports a difference of 0.16 and p < 0.001; its p-value does not match the recalculated p = 0.036, and the record does not explain the difference.

These findings describe a measured spatial endpoint at one stated time point. They do not directly establish the degree of wrinkle reduction, the duration of action, or a participant-centered benefit. The registry mentions those as supportive interests, but their detailed results are not present in the primary outcome entry. The electrical muscle activity result is a separate secondary measure and does not resolve the uncertainty about what the halo difference means in practical terms.

The record’s stated objective refers to comparing equivalence-ratios, but the ratios and any equivalence margin are not reported. A difference test or its p-value cannot establish equivalence without an appropriate margin and analysis. The posted results therefore should not be interpreted as proof that the preparations are equivalent, nor as proof of a clinically meaningful difference.

The trial record also leaves the analysis population, missing-data handling, relationship between enrollment and arm counts, and reason for the divergent p-values unexplained. These limitations affect how confidently the estimates can be interpreted. The reported adverse-event counts are limited and do not establish absence of risk. No treatment recommendation follows from these registry results.

18. Why This Trial Matters Statistically

This trial illustrates why the estimate, its uncertainty, and the analysis description all matter. The primary mean difference is small on the centimeter scale, and its recalculated interval approaches zero even though it remains on one side of zero. Reporting only a p-value would omit that information about magnitude and precision. Reading the estimate with its interval gives a fuller account of what the summary data support.

It also shows why comparison direction should be explicit. The recalculation uses Botox® minus Dysport® and is negative, while the registry’s reported estimate is positive. Opposite subtraction orders can reverse the sign without changing the magnitude. Separately, the reported and recalculated p-values differ, and the registry does not explain why. Keeping these issues distinct prevents a direction convention from being mistaken for an explanation of the test-result difference.

The stated objective invokes equivalence-ratios, while the posted primary analysis is labelled as a two-sided t-test and superiority-or-other. Without the ratios, margin, and detailed analysis plan, readers cannot determine whether the displayed test addresses an equivalence question. This distinction is important in trial interpretation: absence of strong evidence for a difference is not the same as evidence that two treatments are sufficiently similar.

Finally, the record gives a planning illustration based on the observed effect, but does not report the original design assumptions. Those figures show how sample-size requirements vary with the target effect under stated assumptions; they do not describe the actual design rationale. Distinguishing prospective planning from calculations based on an observed result is essential for sound statistical reading.

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.

Several limitations are specific to the information in this record. Enrollment is listed as 29, whereas the two primary outcome arms each list 28 participants. The record does not reconcile these counts or explain who contributed measurements. This prevents a clear assessment of analysis denominators and participant flow.

The registry identifies the trial as randomized and double-masked, but does not report the sequence-generation method, allocation concealment, who was masked, or how masking was maintained. It also does not provide participant characteristics, detailed eligibility criteria, or the intervention administration procedures beyond the arm labels. These omissions limit assessment of group comparability and the practical context of the comparison.

The primary outcome is a halo diameter measured at 28 days. The registry does not report the measurement protocol in enough detail to evaluate repeatability, assessor procedures, or possible measurement error. The listed outcome is not itself a direct measure of wrinkle reduction, although the study objective mentions wrinkle assessment and duration of action as supportive interests.

The reported primary p-value and the recalculated p-value differ, with no explanation in the record. The reported analysis does not include confidence-interval bounds. The stated equivalence objective is also not accompanied by its ratios or an equivalence margin. These gaps make it difficult to connect the posted test to the intended comparison.

Finally, missing-data procedures, analysis-population definitions, multiplicity handling, and the trial’s original sample-size assumptions are not reported in the registry record. Safety reporting is limited to aggregate counts without event descriptions or a listed death count. These limits mean that the posted summaries cannot answer every question about trial conduct, precision, or safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Field of Effects of Two Commercial Preparations of Botulinum Toxin Type A — NCT00989768.
• Registry record last updated 2010-06-02; status last verified 2009-10.
• Results first posted 2010-04-27.
• 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 record describes a completed phase 4, randomized, double-masked, parallel comparison of Dysport® 5U and Botox® 2U for wrinkles in the frontal area. Enrollment is listed as 29. The primary endpoint is mean horizontal action-halo diameter at 28 days, measured in centimeters. The recorded start is 2005-05 and primary completion is 2007-11; the sponsor is Hexsel Dermatology Clinic.

The primary outcome arms each list 28 participants. Their means are 1.28 cm for Dysport® and 1.12 cm for Botox®. The registry’s analysis reports a mean difference of 0.16 and p < 0.001; the unadjusted recalculation gives -0.16 cm in the Botox®-minus-Dysport® direction and p = 0.036. The record does not explain the difference between the p-values.

A secondary electrical muscle activity measure is also posted. Serious adverse events are listed as zero among 29 at risk, and one other adverse event is listed among 29 at risk. Important details—including the original sample-size assumptions, analysis populations, missing-data handling, multiplicity approach, and equivalence margin—are not reported in the registry record.