Efficacy and Safety of DaxibotulinumtoxinA for Injection for the Treatment of Adult Upper Limb Spasticity: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of DaxibotulinumtoxinA for Injection for the Treatment of Adult Upper Limb Spasticity (NCT03821402), a randomized phase 2 study. The primary outcome is Change From Baseline at Week 6 on the Modified Ashworth Scale (MAS) in the Suprahypertonic Muscle Group (SMG) Score.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, double-blind, placebo-controlled, parallel-group, dose-ranging, multicenter trial. The registry classifies masking as quadruple; it does not identify which roles were masked or give further operational details. The study was conducted in the United States, with approximately 30 study centers described in the study summary.

The summary describes four groups assigned in a 1:1:1:1 ratio: daxibotulinumtoxinA at 250 U, 375 U, or 500 U, or placebo. The registry record reports 83 participants enrolled. The initial protocol described approximately 128 adult participants, and the study summary states that the protocol was amended and the trial completed with fewer participants than initially described because of the impact of COVID-19 on enrollment.

The study included a 21-day screening period, a treatment visit, and follow-up visits. The registry gives a start date of 2018-12-12 and a primary completion date of 2020-11-23, and lists the trial status as completed. More detailed information about the treatment and follow-up schedule is not reported in the registry record.

The primary endpoint was assessed at Week 6 in the intent-to-treat population. Eight outcome measures and 12 analyses are listed in the record. Four secondary outcomes are named: muscle tone improvement responder rate, Physician Global Impression of Change responder rate, change from baseline at Weeks 6 and 12 on the Disability Assessment Scale functional impairment measure, and duration of effect. The registry record does not give a full statistical analysis plan, the exact definition of the analysis populations beyond the primary endpoint description, or the rationale for the original enrollment target.

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: Intent to treat population

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Safety population

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline at Week 6 on the Modified Ashworth Scale (MAS) in the Suprahypertonic Muscle Group (SMG) Score, measured over Week 6.

The primary endpoint was mean change from baseline at Week 6 on the Modified Ashworth Scale (MAS) in the suprahypertonic muscle group (SMG) score. The muscle group was one of the elbow, wrist, or finger flexors. The MAS score ranges from 0, described as normal tone, to 4, described as the affected part being rigid in flexion or extension. The posted measure is a continuous score, and the reported arm summaries are least-squares means with standard errors.

A change from baseline expresses how the measured score at the specified follow-up differs from its starting value. The MAS was used to measure muscle tone in the selected muscle group. In general, a continuous endpoint retains information about the size and direction of change rather than reducing each participant's result to a responder category. The registry does not explain why Week 6 was selected as the primary time point, or state a threshold for a change that would be considered important to participants or clinicians.

All four group means were negative: -0.9 for 250 U, -1.0 for 375 U, -1.5 for 500 U, and -0.8 for placebo. These are within-group changes, not treatment-versus-placebo effects. The central comparison is the difference in mean change between each dose and placebo, interpreted alongside its uncertainty. A lower group mean alone does not establish that the group differs from placebo.

7. Results Posted in the Registry

• DAXI 250 U: mean -0.90 versus -0.80 on control; difference -0.10 (95% CI -0.81 to 0.61), standardized effect d = -0.08; z-test p = 0.782.
• DAXI 375 U: mean -1.00 versus -0.80 on control; difference -0.20 (95% CI -0.92 to 0.52), standardized effect d = -0.16; z-test p = 0.586.
• DAXI 500 U: mean -1.50 versus -0.80 on control; difference -0.70 (95% CI -1.43 to 0.03), standardized effect d = -0.57; z-test p = 0.062.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is continuous: it is a score measured on a numeric scale, and the analysis summarizes average change from baseline. The registry reports least-squares means and standard errors for each arm. A least-squares mean is a model-based group mean; in general, it can reflect adjustment for variables included in the model. The exact covariates and model specification used for the sponsor's analysis are not reported in the registry record, so the posted least-squares means should not be treated as a fully described adjusted analysis.

What does the unadjusted comparison represent?

The recalculated comparisons subtract the placebo mean change from the mean change in each dose group. They are simple, unadjusted comparisons based on posted summary statistics. The estimated mean differences are -0.1 for 250 U, -0.2 for 375 U, and -0.7 for 500 U, in MAS score units. A negative difference means that the dose-group mean change is more negative than the placebo mean change. This direction describes the arithmetic of the score changes; it is not, on its own, a judgment about clinical importance.

The recalculations use approximate pooled standard deviations derived from the reported standard errors and group sizes. Because these standard deviations are approximate, the corresponding standardized effects and intervals are also approximate. These calculations do not reproduce the sponsor's ANCOVA model. Differences between an unadjusted comparison and a model-based analysis can arise from the method and information included in each analysis. The exact reason for the discrepancy in this trial is not reported in the registry record.

What do standard errors and intervals convey?

A standard error describes the estimated variability of a sample mean as an estimate of the underlying mean. It is not the spread of individual participants' scores. The posted standard errors are 0.25, 0.26, and 0.27 for the active-dose arms, and 0.26 for placebo. In general, a confidence interval combines an estimate with its uncertainty to give a range of values compatible with the data under the analysis assumptions. The recalculated intervals for each dose-versus-placebo comparison include zero. The confidence level for these recalculated intervals is not stated in the registry record.

In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the statistical model. It is not a measure of the probability that the null hypothesis is true, and it does not measure the probability that a result will replicate. The recalculated p-values are unadjusted. The sponsor-reported p-values come from ANCOVA and are not interchangeable with the recalculated values. Because the record identifies a discrepancy, the sponsor's own analysis takes precedence for the trial's reported analysis.

Why can over-dispersion matter?

General statistical context: over-dispersion occurs when the variation in observed outcomes exceeds what a particular model assumes. If a model understates variability, its standard errors can be too small and its intervals too narrow. The MAS endpoint is a bounded score, but the registry record does not report a specific over-dispersion assessment or describe a model that addresses it. It would therefore be inappropriate to claim that over-dispersion was present or that it affected the trial's analysis.

How should the analysis structure be understood?

The sponsor analyses are labeled ANCOVA, a method that generally compares group outcomes while accounting for one or more covariates. Which covariates were included, whether baseline MAS score was included, how assumptions were checked, and how the model handled missing values are not reported in the registry record. The record lists three sponsor comparisons, one for each dose against placebo, and labels them as superiority analyses. It does not provide sponsor estimates or confidence intervals for those comparisons.

There are 12 analyses listed across eight outcome measures, and four secondary outcomes are named. The registry record does not state how the primary endpoint was distinguished from other analyses in the multiplicity strategy, whether the three dose comparisons were treated as a family, or whether any adjustment was made. In general, testing several hypotheses can increase the chance of at least one apparently positive result when all null hypotheses are true. That general concern does not establish that the sponsor's result is false; it means the testing plan is important context and is not available in the registry record.

For sample-size planning, the listed figures use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They illustrate planning based on the observed effect or a stated fraction of it, rather than reconstructing the trial's original design. The original sample-size assumptions and justification are not reported in the registry record. These planning calculations should be interpreted as prospective illustrations, not as a measure of the trial's observed power.

10. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the data under the analysis assumptions. The posted arm summaries include standard errors, and the simple recalculations include intervals for the dose-versus-placebo mean differences. Each recalculated interval includes zero, so each is compatible with no difference as well as with differences in either direction under that calculation. The 500 U estimate is farther from zero than the other recalculated estimates, but its interval still includes zero.

The registry record does not state the confidence level for the recalculated intervals. Exact endpoints are therefore not repeated. The intervals belong to approximate, unadjusted calculations based on posted summary statistics; they are not intervals from the sponsor's ANCOVA. The sponsor's own analysis takes precedence because the registry record identifies a discrepancy between the sponsor analysis and the recalculations. However, sponsor estimates and intervals are not reported, so the precision of the sponsor's estimated differences cannot be assessed from the record.

In general, a wider interval reflects greater uncertainty about the magnitude of an estimate, while a narrower interval reflects greater precision, conditional on the model and data. Precision is not the same as clinical importance: an estimate can be precise without being important, or uncertain while still allowing effects of potential interest. The registry record does not give a threshold for a clinically important MAS change, and the posted results do not supply enough information to compare the sponsor model's precision across doses. The small arm sizes and the trial's reduced enrollment relative to the initial protocol are relevant context, but they do not identify the direction or size of any bias.

11. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed dose-versus-placebo effect, not the trial's own design calculations. For these continuous-outcome comparisons, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were real. The 90% power column expresses the corresponding planning target for a 90% chance. These are prospective design quantities, not descriptions of what happened in the trial. They do not show the probability that the trial's observed result is true, and they are not observed power.

The rows that plan for 100%, 75%, and 50% of the observed effect use progressively smaller effects as the target. Smaller effects need more participants to detect at the same significance level and power. The figures vary substantially across dose comparisons because their observed effect estimates differ. For example, planning for 100% of the observed 500 U effect gives 48 participants per arm for 80% power and 64 participants per arm for 90% power; planning for 100% of the observed 250 U effect gives 2,362 and 3,162 participants per arm, respectively. The registry record's original sample-size rationale, including any effect assumed during protocol planning, is not reported.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.100; pooled standard deviation σ = 1.227.
2. n = 2 × (1.96 + 0.842)² × 1.227² / -0.100² = 2,361.4, rounded up to 2,362 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 <- -0.1                      # observed difference in means
sigma <- 1.22650834782024                     # 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(3821402)
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 = 2,362 (80% power), 3,162 (90% power)
 75% of observed effect: n per arm = 4,199 (80% power), 5,621 (90% power)
 50% of observed effect: n per arm = 9,446 (80% power), 12,646 (90% power)
power.t.test: 2362.4 
Simulated power at n = 2,362 per arm: 0.795 (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.

13. Analyses Reported by the Sponsor

The sponsor's analyses are reported as ANCOVA superiority comparisons of each dose with placebo. Their p-values are 0.764 for 250 U, 0.551 for 375 U, and 0.049 for 500 U. The sponsor analysis therefore reports a p-value below 0.05 for the 500 U comparison and values above 0.05 for the other dose comparisons. Estimates and confidence intervals from those ANCOVA comparisons are not reported in the registry record.

The simple recalculations use unadjusted comparisons of posted group summaries, with approximate pooled standard deviations. Their p-values are 0.782, 0.586, and 0.062 for 250 U, 375 U, and 500 U, respectively. The recalculated intervals all include zero. These results differ from the sponsor's reported analysis for 500 U, and the registry record flags a discrepancy. The analyses should not be blended or treated as if they estimate the same model-based quantity.

For the trial's reported inferential result, the sponsor's own analysis takes precedence. The recalculation is useful as a transparent check on the posted summaries, but it is not a replacement for the sponsor's ANCOVA. The record does not provide enough methodological detail to explain the discrepancy or reproduce the ANCOVA results independently.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists 12 analyses across eight outcome measures and names four secondary outcomes. There are three sponsor-reported superiority comparisons, one for each dose against placebo. The record does not report whether the three comparisons were included in a prespecified multiplicity strategy, whether testing was adjusted across doses or outcomes, or whether a hierarchy of tests was used. This is important context because, in general, conducting multiple tests can increase the chance of at least one small p-value when no effect exists. The available information does not establish whether that issue altered the sponsor's conclusions.

The primary endpoint is described as analyzed in the intent-to-treat population. The record does not define the analysis population in greater detail or say how participants were handled if they did not receive assigned treatment or lacked a Week 6 measurement. The number of missing primary endpoint values, reasons for missingness, and methods used to handle missing data are not reported in the registry record. It is also not reported whether sensitivity analyses were conducted to assess the effect of missing data assumptions.

The sponsor analyses are labeled ANCOVA, but the covariates, model specification, assumption checks, and handling of missing observations are not reported. The registry identifies the sponsor's p-values but does not provide the corresponding sponsor estimates or intervals. The simple recalculations are unadjusted and should not be taken as a substitute for the absent model details. The original sample-size justification and any planned interim analyses are also not reported in the registry record. These omissions limit independent assessment of how the analysis plan addressed multiple comparisons, incomplete outcomes, and the originally intended enrollment.

15. 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: covid-19 (5.6%), coronavirus infection (4.5%), pleuritic pain (4.5%), cerebrovascular accident (4.2%), seizure (4.2%).

The posted serious adverse event counts were 2 participants among 22 at risk in DAXI 250 U, 0 among 19 in DAXI 375 U, 1 among 18 in DAXI 500 U, and 2 among 24 in placebo. No deaths were reported in any of the four groups. These are counts of participants with serious adverse events, not a measure of the severity or duration of every event experienced by participants.

The registry also lists serious adverse event terms with percentages, including COVID-19, coronavirus infection, pleuritic pain, cerebrovascular accident, and seizure. It does not give further context in the listed terms about which treatment group each term occurred in. Serious-event counts should be read separately from the listed terms and from other adverse events. The other adverse event counts were 4, 12, 6, and 4 in the 250 U, 375 U, 500 U, and placebo groups, respectively; these are not serious-event counts.

These summaries are descriptive. The arm sizes are small, and the registry record does not provide a comparative safety analysis, event-level timing, duration, or causal assessment. The counts alone do not establish whether an event was caused by treatment or whether the groups differ in safety.

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

The posted results describe mean change in MAS score at Week 6 for three daxibotulinumtoxinA dose groups and placebo. The dose-group means were -0.9, -1.0, and -1.5, compared with -0.8 for placebo. The simple unadjusted comparisons estimate mean differences of -0.1, -0.2, and -0.7 for the three dose groups, respectively. Each recalculated interval includes zero, and the recalculated p-values are 0.782, 0.586, and 0.062.

The sponsor's ANCOVA analysis reports a p-value below 0.05 for 500 U, while the p-values for 250 U and 375 U are above 0.05. Because the registry record identifies a discrepancy, the sponsor's own analysis takes precedence for the reported trial analysis. The sponsor estimates and confidence intervals are not available in the record, so the magnitude and precision of those model-based comparisons cannot be evaluated from the posted analysis details alone.

In general, a statistical result is not the same as a clinical conclusion. A p-value does not describe the probability that a treatment effect is true, and a difference in means does not establish whether the size of a change matters to participants. The registry record does not report a threshold for a clinically important MAS change. Nor does it provide enough information about missing data, multiplicity, or the sponsor's model to support a complete independent evaluation.

The results concern the Week 6 MAS endpoint in the intent-to-treat population. They do not, by themselves, answer questions about all secondary outcomes, duration of effect, later follow-up, or outcomes for particular subgroups. The registry's outcome list includes other measures, but the information summarized for the primary endpoint cannot be generalized to those outcomes. These results should be understood as findings from a completed Phase 2 trial with 83 enrolled participants and smaller group counts for the primary endpoint, rather than as a definitive answer to every question about treatment effects or safety.

17. Why This Trial Matters Statistically

This trial illustrates several practical issues in reading randomized clinical trial results. First, the reported change within each group is not the same as the treatment contrast. The placebo group also had a negative mean change, so the relevant comparison is the difference in change between each dose group and placebo, not the dose-group mean in isolation.

Second, the sponsor's ANCOVA results and the simple unadjusted recalculations do not match for the 500 U comparison. The record flags this discrepancy, and the sponsor's own analysis takes precedence. Yet the registry does not provide the sponsor's estimates or intervals, which makes it harder to judge the magnitude and precision of its model-based findings. The difference demonstrates why an analysis method and its specification are essential context, not merely a p-value.

Third, enrollment was lower than the initial protocol description because of COVID-19's impact on enrollment. The observed arm sizes are consequently modest, and the posted simple recalculations have substantial uncertainty. The sample-size planning illustrations also show that required enrollment depends strongly on the effect targeted: planning for a smaller fraction of the observed effect requires more participants.

Finally, the record leaves multiplicity and missing-data handling unclear. Those details matter when several outcomes or comparisons are analyzed, and when the primary outcome may not be available for every participant. The trial is therefore a useful example of why statistical interpretation depends on effect estimates, uncertainty, the analysis plan, and the completeness of registry reporting together.

18. 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 reports 83 participants enrolled, fewer than the approximately 128 described in the initial protocol summary. It attributes the reduction to the impact of COVID-19 on enrollment. The record does not report the resulting effect on precision or whether the protocol amendment changed any analysis objectives.

Primary endpoint group counts were 22 for 250 U, 19 for 375 U, 18 for 500 U, and 24 for placebo. These counts are small, and the simple recalculations show considerable uncertainty. The registry record does not give a clinically important difference threshold for the MAS score, so the clinical importance of the numerical changes cannot be determined from the score differences alone.

The sponsor's reported ANCOVA results do not include estimates or confidence intervals. Covariates and other model details are not reported, and the record identifies a discrepancy with simple unadjusted recalculations. Multiplicity adjustment, missing outcome counts, missing-data methods, sensitivity analyses, and interim analyses are not reported. These omissions prevent a full independent reconstruction of the primary analysis.

The endpoint was measured at Week 6, while the study summary describes follow-up visits without giving their full timing. The registry lists secondary measures, but their results are not included in the registry record described for the primary endpoint. The record also does not provide detailed eligibility criteria or the distribution of participants by stroke versus traumatic brain injury. These limitations restrict interpretation beyond the reported primary outcome and prevent conclusions about particular participant subgroups or later outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of DaxibotulinumtoxinA for Injection for the Treatment of Adult Upper Limb Spasticity — NCT03821402.
• Registry record last updated 2023-09-21; status last verified 2023-08.
• Results first posted 2023-09-21.
• 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.

22. Record Summary

NCT03821402 is a completed Phase 2 randomized, double-blind, placebo-controlled, parallel-group, dose-ranging trial sponsored by Revance Therapeutics, Inc. It studied daxibotulinumtoxinA for adult upper limb spasticity after stroke or traumatic brain injury. The registry reports 83 participants enrolled, assigned among doses of 250 U, 375 U, and 500 U or placebo.

The primary endpoint was mean change from baseline at Week 6 on the MAS score for the suprahypertonic muscle group, in the intent-to-treat population. The sponsor reported ANCOVA p-values of 0.764, 0.551, and 0.049 for the three dose comparisons. The registry flags a discrepancy with unadjusted recalculations; the sponsor's own analysis takes precedence. The record does not report sponsor estimates or confidence intervals, and it does not give details on multiplicity or missing-data handling.