BOTOX® Economic Spasticity Trial (BEST): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BOTOX® Economic Spasticity Trial (BEST) (NCT00549783), a randomized phase 4 study. The primary outcome is Physician Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Active Functional Goal at Week 24.

2. Clinical Question

The study addressed whether adding botulinum toxin type A to standard care was associated with a different rate of physician-assessed functional goal attainment than placebo. The registry summary describes spasticity as stiffness or frequent cramps, sometimes accompanied by pain and abnormal movements, that can interfere with everyday tasks. The endpoint focuses on an individual patient’s stated functional goal rather than a single common task applied to everyone.

The registry record describes a randomized, double-blind, parallel-group study and reports 274 participants enrolled. The primary assessment was at week 24, or 10 weeks after a second injection where one was given. The treatment schedule allowed a second injection, but the registry record does not report how many participants received one or the reasons for receiving or not receiving it. The posted primary results describe the proportion meeting the endpoint in each group; they do not by themselves establish why any difference arose or how the result relates to every aspect of function or quality of life.

3. Trial Design

The registry record identifies this as a phase 4, randomized, double-blind, parallel-group trial sponsored by Allergan. It lists a total enrollment of 274 and a completed status. The recorded start is 2007-10 and primary completion is 2010-01. The study summary describes recruitment at about 33 locations in Europe and Canada and participation lasting about 1 year.

Participants were assigned to botulinum toxin type A 900kD or placebo. Both groups were scheduled to receive an intramuscular injection at the baseline visit, with an optional second injection of the randomized treatment after a minimum of 12 weeks to a maximum of 24 weeks after baseline. Although the record calls the trial double-blind, it does not specify in the posted record which groups of people were blinded or how blinding was maintained. Details of the randomization sequence and allocation concealment are not reported in the registry record.

The primary outcome population is described as intent-to-treat, consisting of all patients who were randomized, started the study, and received a baseline injection. The arm-level outcome counts reported for the primary endpoint are 139 for botulinum toxin type A 900kD and 134 for placebo. The registry record does not explain the relationship between the total enrollment figure and those endpoint denominators, or report a participant flow account that would show exclusions, withdrawals, or missing endpoint assessments.

The primary endpoint was physician-assessed achievement of the principal active functional goal at week 24. Secondary outcomes listed in the record include physician and patient assessments of functional goal achievement at other time points and activities of daily living quality-of-life scores. Some secondary results are posted, while results for the remaining listed secondary outcomes are not reported in the registry record. The trial’s original sample-size justification, detailed statistical analysis plan, and any planned interim analyses are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat, which consists of all patients who were randomized (started study) and received a baseline injection.

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 Physician Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Active Functional Goal at Week 24, measured over Week 24.

The primary endpoint is the percentage of patients who achieved their principal active functional goal at week 24, as assessed by a physician. The registry description defines achievement as a goal attainment scale score from 0 to +2 inclusive. The scale has six points: -3 means function is worse than at the start, 0 means the expected goal was attained, and +2 means function is much better than expected. The endpoint is also described as being assessed at week 24 or 10 weeks after a second injection.

This outcome represents whether an individualized functional goal was judged to have been reached, rather than a change in a single standardized task for every participant. That can make the result relevant to patients’ varied functional priorities, while also making the outcome dependent on the goal selected and on the assessment process. The registry record does not provide further details about how goals were selected, how assessments were standardized, or whether the assessment was independently reviewed.

A percentage is useful for describing the share of participants meeting a defined binary criterion: each participant is counted as having achieved the endpoint or not having achieved it. The measure does not show the size of improvement among participants who did achieve their goal, nor does it summarize every dimension of spasticity or daily function. The posted result should therefore be read as a comparison of the proportion meeting this specific physician-assessed threshold at the stated time point.

7. Results Posted in the Registry

• Botulinum Toxin Type A 900kD: 41.0% (57/139) versus 33.6% (45/134) on control; risk difference 7.4 percentage points (95% CI -4.0 to 18.9), risk ratio 1.22 (0.90–1.67); unadjusted two-proportion z-test p = 0.205.

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.

Physician Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 12

• 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:
  • Botulinum Toxin Type A 900kD: 33.1% (46/139) versus 29.1% (39/134) on control; risk difference 4.0 percentage points (95% CI -7.0 to 15.0), risk ratio 1.14 (0.80–1.62); unadjusted two-proportion z-test p = 0.477.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Botulinum Toxin Type A 900kD and the control. The interval gives the range of effects that remain compatible with the data.

Physician Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 52

• 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:
  • Botulinum Toxin Type A 900kD: 45.3% (63/139) versus 52.2% (70/134) on control; risk difference -6.9 percentage points (95% CI -18.7 to 4.9), risk ratio 0.87 (0.68–1.11); unadjusted two-proportion z-test p = 0.253.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Botulinum Toxin Type A 900kD and the control. The interval gives the range of effects that remain compatible with the data.

Patient Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 12

• 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:
  • Botulinum Toxin Type A 900kD: 33.1% (46/139) versus 27.6% (37/134) on control; risk difference 5.5 percentage points (95% CI -5.4 to 16.4), risk ratio 1.20 (0.83–1.72); unadjusted two-proportion z-test p = 0.325.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Botulinum Toxin Type A 900kD and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary assessments of physician- and patient-rated goal achievement at multiple follow-up times, along with activities of daily living quality-of-life scores. Results are posted for a limited subset of these outcomes: physician assessments at week 12 and week 52, and a patient assessment at week 12. The other listed secondary outcome results, including the week-24 and week-52 patient assessments and the quality-of-life scores, are not reported in the registry record.

Across the posted secondary goal assessments, the observed direction is not uniform across assessment time and assessor. The physician and patient assessments at week 12 have higher reported percentages in the botulinum toxin group than in the placebo group, while the physician assessment at week 52 has a higher reported percentage in the placebo group. This mixed pattern gives context to the week-24 primary comparison, but it does not replace it: the primary endpoint is a distinct physician assessment at a specified time point and uses the active functional goal definition.

Secondary outcomes are often used to explore other dimensions of an intervention or to assess whether a pattern is consistent over time. They generally carry less confirmatory weight when many outcomes and time points are considered, particularly when the registry record does not explain how multiplicity was handled. Looking at several results increases the chance that some differences will appear notable by chance alone. The record does not report a multiplicity adjustment or a complete analysis plan, so the secondary results are best treated as exploratory descriptions rather than independent confirmation of the primary finding.

The absence of results for some listed outcomes also limits an overall account of function and quality of life. It is not possible from the registry record to determine whether those results were collected but not posted, were not analyzed, or were unavailable for another reason. No explanation is reported in the registry record.

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

• Physician Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 12
• Physician Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 52
• Patient Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 12
• Patient Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 24
• Patient Assessment of Success, as Determined by Percentage of Patients Who Achieve Their Principal Functional Goal at Week 52
• Activities of Daily Living Quality of Life (QOL) Score at Week 12
• Activities of Daily Living Quality of Life (QOL) Score at Week 24
• Activities of Daily Living Quality of Life (QOL) Score at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a patient either met the defined goal-attainment threshold or did not. A percentage expresses the number meeting that threshold relative to the number in the reported group. For this endpoint, the registry reports 40.9% in the botulinum toxin type A 900kD group and 33.3% in the placebo group. The denominators reported for the groups are 139 and 134, respectively.

What does a risk difference describe?

A risk difference compares the proportion experiencing an outcome in one group with the proportion in another group, on the same proportion scale. The posted unadjusted recalculated risk difference is 0.074 for botulinum toxin type A 900kD relative to placebo. A positive estimate indicates that the observed proportion was higher in the botulinum toxin group in this comparison; it does not, on its own, establish that the difference is reliable or attributable to the assigned treatment. A negative estimate would indicate the reverse direction. The confidence interval describes uncertainty around the estimated difference.

How should a confidence interval be read?

A confidence interval is a range of values compatible with the observed data under the statistical method’s assumptions. For the primary risk difference, the interval runs from -0.040 to 0.189. Because it contains zero, the data do not rule out no difference under this unadjusted comparison. The interval also spans values in both directions, so it does not establish a single direction or a precise magnitude. The interval is not a range that contains a fixed proportion of individual patient outcomes, and it is not a probability statement about the true effect after the data have been observed.

What does the p-value add?

The unadjusted p-value is 0.205. In general, a p-value measures how compatible the observed data are with a specified null model, assuming the model and analysis conditions hold. Smaller values indicate that the data would be less expected under that model. A p-value is not the probability that the null hypothesis is correct, and it does not measure the clinical importance of an effect. The registry record does not report a sponsor analysis for the endpoint, so the posted p-value should be treated as an unadjusted recalculation from summary results rather than as a reported sponsor result.

Why distinguish unadjusted from adjusted analyses?

An unadjusted comparison looks at the group results without accounting for other variables or a more complex model. It can be a useful transparent description of the posted counts. A prespecified analysis might use adjustment or other methods, but the registry record does not report whether such methods were planned or used. There are no reported analyses listed for the primary outcome in the record, and the original detailed statistical plan is not reported in the registry record. The unadjusted comparison therefore should not be presented as a substitute for an undocumented sponsor analysis.

Why can over-dispersion matter?

Over-dispersion is a general concern for outcomes modeled as counts or rates when variability exceeds what a chosen statistical model expects. It can make standard errors too small if ignored, which can make confidence intervals too narrow and p-values too small. The primary endpoint is reported as a percentage of participants meeting a binary criterion, not as a count or event rate over person-time. The registry record does not report use of a model that requires an over-dispersion adjustment, so there is no basis to claim that over-dispersion affected this endpoint’s posted comparison.

The population description matters when interpreting any estimate. The registry defines the primary outcome population as all randomized patients who started the study and received a baseline injection. That definition is narrower than simply referring to everyone enrolled, and the record does not describe missing endpoint data or how any such data were handled. The reported arm denominators and percentages are the available basis for the unadjusted comparison; the record does not give enough detail to reconstruct any additional analyses.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate the estimated group difference. The primary unadjusted recalculated risk difference is 0.074, and its confidence interval extends from -0.040 to 0.189. The interval is wide enough to include zero as well as values on both sides of zero. This means that the observed point estimate should not be read as a precise measure of the underlying difference.

The interval conveys uncertainty under the assumptions of the calculation. It does not account for uncertainties that cannot be evaluated from the posted summary results, such as the effects of missing assessments, departures from the planned analysis, or choices in defining and assessing individualized goals. Those issues are particularly difficult to evaluate because the registry record does not report a detailed analysis plan or missing-data procedures.

The unadjusted p-value of 0.205 is another summary of the data’s compatibility with a no-difference model, but it is not a measure of precision and does not replace the interval. The range of the confidence interval is more informative about the variety of effect values compatible with the comparison. Because the interval includes both no difference and nonzero values, the posted data leave substantial uncertainty about the magnitude and direction of the group difference.

Precision also depends on the outcome and the number of participants with usable assessments. The record reports group denominators for the primary result, but does not provide a participant flow or report how many week-24 outcomes were missing. As a result, the impact of missingness on the estimate cannot be assessed from the registry record.

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 estimates are illustrations based on the observed effect, not the trial’s original design calculation. For these binary outcomes, 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 scenario targets the stated fraction of the observed effect.

For the primary endpoint, planning for 100% of the observed effect gives 665 participants per arm for 80% power and 890 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,171 participants per arm for 80% power and 1,567 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,605 participants per arm for 80% power and 3,487 participants per arm for 90% power. These are scenario-based planning figures, not descriptions of the participants enrolled in this trial.

In general, 80% power means that a study designed under the stated assumptions would have an 80% chance of detecting the target effect if that effect were the true one. The 90% power column describes the corresponding design with a higher chance of detecting that target effect, under the same assumptions. Smaller target effects require more participants because they are harder to distinguish from random variation. A curve representing such planning scenarios should be read as illustrating how the required sample size changes with the effect being targeted, not as a result observed in the trial.

These figures are not observed power. They do not show the probability that the completed trial detected an effect, and they do not revise the trial’s original sample-size justification. That original justification and its assumptions are not reported in the registry record.

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 = 0.336; treatment proportion p₁ = 0.410; average p̄ = 0.373.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6839 = 1.3404.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6819 = 0.5739.
4. n = (1.3404 + 0.5739)² / (0.0743)² = 664.7, rounded up to 665 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 <- 0.335820895522388                          # control proportion
p1 <- 0.410071942446043                          # 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(549783)
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 = 665 (80% power), 890 (90% power)
 75% of observed effect: n per arm = 1,171 (80% power), 1,567 (90% power)
 50% of observed effect: n per arm = 2,605 (80% power), 3,487 (90% power)
power.prop.test: 664.7 
Simulated power at n = 665 per arm: 0.802 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists multiple secondary endpoints across physician and patient assessments, different follow-up times, and activities of daily living quality-of-life scores. Considering many outcomes creates a multiplicity issue: even if there is no underlying group difference for any outcome, a collection of statistical tests can produce an apparently unusual result by chance. A prespecified approach to multiplicity can help define which comparisons are confirmatory and how uncertainty should be interpreted across the outcome family.

The registry record does not report whether multiplicity was addressed, what testing hierarchy was planned, or whether any secondary results were intended to be confirmatory. It also does not report a full statistical analysis plan. This matters when interpreting the secondary outcomes because their p-values and estimates cannot be placed within a documented overall testing strategy. The primary comparison is presented as an unadjusted recalculation, and the record lists no reported analyses for the primary outcome.

Missing-data handling is also not reported in the registry record. The primary population is defined as randomized patients who started the study and received a baseline injection, but there is no account of missing week-24 assessments, withdrawals, or the methods used for any incomplete outcomes. It is therefore not possible to assess whether the observed percentages are affected by missingness or to establish how participants without an observed endpoint were treated in the underlying analysis.

The arm counts for the posted primary result are 139 and 134, while total enrollment is reported as 274. The registry record does not include a participant flow that explains the relationship between these figures. It also does not describe any per-protocol or other analysis populations, so it is not possible to compare the stated intent-to-treat population with additional populations.

Interim analyses and any associated stopping rules are not reported in the registry record. Their absence from the record should not be taken as evidence that they were or were not conducted. The same applies to the original sample-size assumptions and other prespecified analysis decisions: without those details, the posted results cannot be fully compared with a documented analysis plan.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (3.0%), epilepsy (3.0%), fall (2.2%), convulsion (2.2%), angina pectoris (1.5%).

The registry record reports serious adverse event counts for 47 of 139 participants in the botulinum toxin type A 900kD group and 45 of 134 in the placebo group. Other adverse event counts are 60 of 139 and 45 of 134, respectively. These are group-level counts as recorded; they do not, by themselves, describe event severity beyond the serious-event classification or establish that an event was caused by the assigned treatment.

The serious adverse event terms listed most often include Pneumonia and Epilepsy, each reported as 3.0%, and Fall and Convulsion, each reported as 2.2%. Angina Pectoris and Cardiac Failure are each reported as 1.5%. These percentages are registry entries for the listed terms. The record does not provide additional context on overlap between terms, timing, recurrence, or attribution.

Death counts are not reported in the registry record. Safety figures should be read as descriptive summaries from the posted record, not as a complete assessment of comparative safety. The registry record does not report a detailed adverse-event analysis plan or further information about how events were assessed.

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

The posted primary data describe physician-assessed functional goal attainment at week 24 in the two randomized groups. The reported percentages were 40.9% for botulinum toxin type A 900kD and 33.3% for placebo. The unadjusted recalculated risk difference was 0.074, with a confidence interval from -0.040 to 0.189 and an unadjusted p-value of 0.205. Together, these values describe an observed difference with considerable uncertainty; they do not establish a definitive direction or magnitude of a group effect.

The endpoint is specific: it records whether the physician judged that a participant achieved an individualized active functional goal according to a defined goal attainment scale threshold. It does not capture every aspect of spasticity, daily activity, or quality of life. A participant who did not meet the threshold may still have experienced some change, while meeting the threshold does not convey the size or durability of improvement. The outcome is also tied to the choice of goal and the assessment process, details not fully described in the registry record.

The primary comparison cannot establish that the assigned intervention caused the observed group difference beyond the assumptions of the trial design and analysis. The record describes randomization and double masking, but does not report full implementation details, missing-data handling, or the original analysis plan. The posted comparison is an unadjusted recalculation from summary results, and the registry record does not report a sponsor analysis for the primary endpoint.

The record lists additional functional and quality-of-life outcomes, but only a subset has posted results. The available secondary results vary in direction across assessor and time point, and multiplicity handling is not reported. They therefore provide context, not a definitive resolution of the primary result or a comprehensive picture of all listed outcomes.

These findings are a statistical description of the registry record. They are not medical advice, and they do not answer every question about individual response, long-term function, quality of life, or safety.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be considered alongside its uncertainty. The primary group percentages differ in the observed data, but the confidence interval for the unadjusted risk difference spans values on both sides of zero. Reporting the estimate alone would obscure how much uncertainty remains; reporting only a p-value would likewise fail to show the range of differences compatible with the comparison.

It also demonstrates the importance of defining the outcome precisely. Functional goal attainment is a meaningful type of endpoint for a population with varied needs, but it depends on an individualized goal and a threshold on the goal attainment scale. Statistical interpretation must remain tied to that operational definition rather than treating the percentage as a general measure of all functional change.

The registry record provides group counts, percentages, and a range of outcomes, but does not report a full analysis plan, missing-data methods, multiplicity approach, or original sample-size justification. Such omissions make it harder to judge how closely the posted summaries reflect the trial’s intended analyses. The contrast between a primary endpoint and many secondary outcomes also shows why outcome hierarchy and multiplicity plans matter: broad collections of comparisons need a clear interpretive framework.

Finally, planning estimates based on an observed effect can help illustrate how target effect size and desired power relate to participant requirements. They are useful as planning scenarios, but are not evidence about the power or design assumptions of the completed trial. Keeping those planning illustrations separate from the observed results is essential for sound statistical interpretation.

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

The registry record leaves several trial-specific limitations difficult to assess. Although the study is described as randomized and double-blind, details of sequence generation, allocation concealment, blinding roles, and maintenance of blinding are not reported in the registry record. The optional second injection also means that exposure could differ across participants, but the number receiving a second injection and the reasons are not reported.

The primary outcome depends on an individualized functional goal and physician assessment. The registry describes the scale and the achievement threshold, but does not report how goals were selected, whether assessors were trained to a common procedure, or whether assessment reliability was evaluated. The result therefore depends on measurement details that cannot be examined from the posted record.

There is no reported participant flow or account of missing primary endpoint data. The registry defines the primary population as randomized patients who started the study and received a baseline injection, but does not describe exclusions, withdrawals, or missing outcome handling. The enrollment figure and endpoint group denominators are both reported, without an explanation of their relationship.

The record also lacks a reported original sample-size justification, detailed statistical plan, multiplicity approach, and interim-analysis information. Only some listed secondary outcomes have posted results. These gaps limit assessment of the intended analysis, the completeness of outcome reporting, and the extent to which secondary findings should be considered confirmatory.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: BOTOX® Economic Spasticity Trial (BEST) — NCT00549783.
• Registry record last updated 2012-08-22; status last verified 2012-07.
• Results first posted 2012-08-22.
• 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

NCT00549783, the BOTOX® Economic Spasticity Trial (BEST), is listed as a completed phase 4 randomized, double-blind, parallel-group trial sponsored by Allergan. It reports enrollment of 274 and compares botulinum toxin type A 900kD with placebo in patients with muscle spasticity following stroke.

The primary endpoint was physician-assessed achievement of a principal active functional goal at week 24. The posted percentages are 40.9% in the botulinum toxin group and 33.3% in the placebo group. The unadjusted recalculated risk difference is 0.074, with a confidence interval from -0.040 to 0.189 and an unadjusted p-value of 0.205.

The record lists additional functional and quality-of-life outcomes, but results are not posted for all of them. It does not report the original sample-size justification, detailed statistical plan, missing-data procedures, or multiplicity approach.