BOTOX® in the Treatment of Crow's Feet Lines in Japan: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for BOTOX® in the Treatment of Crow's Feet Lines in Japan (NCT01797081), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving None or Mild on the Investigator's Assessment of the Severity of Crow's Feet Lines (CFL) at Maximum Smile Using the Facial Wrinkle Scale-Asian (FWS-A).

2. Clinical Question

3. Trial Design

The registry record describes NCT01797081, titled “BOTOX® in the Treatment of Crow's Feet Lines in Japan.” It is listed as a Phase 3, randomized, double-masked, parallel-group trial sponsored by Allergan. The record reports an enrollment of 300 and a completed status. The recorded study start was 2013-01-31, and the primary completion date was 2013-07-18.

Three groups are reported for the primary outcome: botulinum toxin Type A at 24 U, botulinum toxin Type A at 12 U, and placebo. The active-dose arm descriptions specify injections into bilateral crow’s feet areas on Day 1. They also state that participants could be eligible for up to 5 treatment cycles, depending on retreatment criteria. The placebo arm description specifies normal saline on Day 1 and for subsequent treatments when applicable until day 180, followed by botulinum toxin Type A for additional treatments from day 180 onward. The description of retreatment criteria in the registry record is incomplete, so their details are not reported in the registry record.

Randomization means that assignment to study groups was intended to occur by chance; double masking means the record identifies the trial as double-masked, although it does not report who was masked or how masking was maintained. A parallel design compares groups followed under their assigned regimens rather than having every participant receive each regimen in sequence. These design labels alone do not establish that all potential sources of bias were eliminated.

The primary endpoint is reported for an intent-to-treat population described as including all enrolled participants. The registry record does not report the original sample-size justification, the specific randomization procedure, or a detailed statistical analysis plan. Those omissions limit what can be concluded about the trial’s planning and analysis procedures.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat population included all enrolled participants.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving None or Mild on the Investigator's Assessment of the Severity of Crow's Feet Lines (CFL) at Maximum Smile Using the Facial Wrinkle Scale-Asian (FWS-A), measured over Day 30.

The primary endpoint is the percentage of participants rated as having none or mild crow’s feet lines at maximum smile on Day 30. Investigators used the Facial Wrinkle Scale-Asian, described as a four-point scale: 0 means none, 1 mild, 2 moderate, and 3 severe. The endpoint groups the first two categories together and reports the share of participants with either rating.

This is a binary outcome for analysis: each assessed participant either meets the none-or-mild criterion or does not. Reporting a percentage makes the result easier to interpret as the frequency of the specified rating in each group. It does not show the full distribution of all scale categories, nor does it describe change in every participant’s score.

The endpoint is an investigator assessment at a specified facial expression and time point. That focus is important: a rating at maximum smile on Day 30 is not interchangeable with an assessment at rest, a participant’s own rating, or an assessment at another time. The registry record also lists secondary outcomes for ratings at rest and participant-reported perceptions, which address related but distinct questions.

The primary outcome description identifies the intent-to-treat population as including all enrolled participants. The posted percentages are 68.3% for the 24 U group, 56.6% for the 12 U group, and 8.2% for placebo. The number of participants contributing to each reported arm outcome differs, and the registry record does not explain the reasons for those denominators. The endpoint therefore describes the recorded Day 30 outcomes, while the precise handling of missing outcome assessments is not reported in the registry record.

7. Results Posted in the Registry

• Botulinum Toxin Type A (24U): 68.3% (71/104) versus 8.2% (8/97) on control; risk difference 60.0 percentage points (95% CI 49.5 to 70.5), risk ratio 8.28 (4.21–16.28); unadjusted two-proportion z-test p = <0.001.
• Botulinum Toxin Type A (12U): 56.6% (56/99) versus 8.2% (8/97) on control; risk difference 48.3 percentage points (95% CI 37.1 to 59.5), risk ratio 6.86 (3.45–13.62); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants Achieving a ≥1-Grade Improvement From Baseline on the Investigator's Assessment of the Severity of CFL at Rest Using the FWS-A

• 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 (24U): 61.6% (61/99) versus 17.3% (14/81) on control; risk difference 44.3 percentage points (95% CI 31.7 to 57.0), risk ratio 3.56 (2.16–5.88); unadjusted two-proportion z-test p = <0.001.
  • Botulinum Toxin Type A (12U): 43.6% (41/94) versus 17.3% (14/81) on control; risk difference 26.3 percentage points (95% CI 13.4 to 39.3), risk ratio 2.52 (1.49–4.28); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Botulinum Toxin Type A (24U) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Botulinum Toxin Type A (12U) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Much Improved or Very Much Improved in the Subject's Assessment of Appearance of CFL as Measured by the Global Assessment of Change in Crow's Feet Lines

• 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 (24U): 49.0% (51/104) versus 1.0% (1/97) on control; risk difference 48.0 percentage points (95% CI 38.2 to 57.8), risk ratio 47.57 (6.70–337.58); unadjusted two-proportion z-test p = <0.001.
  • Botulinum Toxin Type A (12U): 39.4% (39/99) versus 1.0% (1/97) on control; risk difference 38.4 percentage points (95% CI 28.5 to 48.2), risk ratio 38.21 (5.36–272.66); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Botulinum Toxin Type A (24U) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Botulinum Toxin Type A (12U) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Rate Themselves in a Younger Self-Perception of Age Category Than at Baseline

• 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 (24U): 32.0% (32/100) versus 7.6% (7/92) on control; risk difference 24.4 percentage points (95% CI 13.8 to 35.0), risk ratio 4.21 (1.95–9.06); unadjusted two-proportion z-test p = <0.001.
  • Botulinum Toxin Type A (12U): 30.5% (29/95) versus 7.6% (7/92) on control; risk difference 22.9 percentage points (95% CI 12.2 to 33.6), risk ratio 4.01 (1.85–8.70); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Botulinum Toxin Type A (24U) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Botulinum Toxin Type A (12U) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the three posted secondary outcomes, the overall descriptive pattern is that the reported outcome percentage was higher in each active-dose group than in placebo. The outcomes address investigator-assessed change at rest, participants’ global assessment of change in crow’s feet lines, and participants’ self-perception of age. They complement the primary endpoint by considering a different expression condition, a participant-reported judgment, and a broader perception rather than the investigator’s maximum-smile threshold alone.

This directional consistency provides context for the primary result, but the measures are not interchangeable. The secondary outcomes have different definitions and, in some cases, different outcome denominators. They should not be combined into a single estimate or treated as repeated measurements of exactly the same construct. The registry record reports them at Day 30, so they do not establish whether the pattern persisted at later time points.

The posted secondary comparisons are unadjusted recalculations. The registry record does not report a multiplicity adjustment, a hierarchy among secondary outcomes, or a detailed analysis plan specifying how these results were to be interpreted. When multiple outcomes and group comparisons are examined, the chance of at least one apparently notable finding can increase. General statistical context: a prespecified testing strategy can help control that concern, but such a strategy is not reported in the registry record.

For that reason, the secondary findings carry less inferential weight than a prespecified primary analysis. Their role is best understood as supportive descriptive context, not independent confirmation that resolves every uncertainty about the primary endpoint. The record does not report whether the secondary analyses were prespecified, how missing observations were handled for each measure, or whether any adjustment was made outside the registry results.

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

• Percentage of Participants Achieving a ≥1-Grade Improvement From Baseline on the Investigator's Assessment of the Severity of CFL at Rest Using the FWS-A
• Percentage of Participants Much Improved or Very Much Improved in the Subject's Assessment of Appearance of CFL as Measured by the Global Assessment of Change in Crow's Feet Lines
• Percentage of Participants Who Rate Themselves in a Younger Self-Perception of Age Category Than at Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

For a binary outcome, a risk difference is the difference between the proportions meeting the defined outcome in two groups. It is expressed on the proportion scale. In the primary comparison, the recalculated risk difference for 24 U versus placebo is 0.600; for 12 U versus placebo it is 0.483. A positive value means the outcome proportion was higher in the active-dose group in this comparison. This arithmetic description is not, by itself, a causal interpretation: causal conclusions depend on the trial conduct, outcome ascertainment, analysis population, and assumptions behind the comparison.

Risk differences can be directly connected to absolute outcome frequencies, unlike relative measures such as a risk ratio or odds ratio. The registry record also contains recalculated relative measures, but the risk difference is used to describe the absolute separation in the observed proportions. None of these measures says how important a difference is to participants; that requires context about the outcome and its relevance, which is not reported in the registry record.

What does a confidence interval add?

A confidence interval is a range of values compatible with the observed data under the calculation and its assumptions. It communicates uncertainty around an estimate rather than giving a guarantee that the true effect lies in that particular interval. The intervals reported for the primary risk differences quantify statistical precision for these unadjusted recalculations. They do not account for missing data or unreported analysis choices unless those are incorporated into the calculation, and the registry record does not report such adjustments.

When interpreting an interval, consider both its location and width. Its location indicates which values are compatible with the estimate, while its width conveys how much uncertainty remains. A narrow interval generally indicates greater precision than a wide interval, but precision does not ensure freedom from bias or clinical importance. The primary intervals are entirely above zero, which is consistent with a higher recorded outcome proportion in each active-dose comparison under the stated unadjusted calculation. This observation does not answer questions about unreported analyses or outcomes at other times.

Why distinguish the posted results from recalculated comparisons?

The registry record posts arm-level percentages and outcome denominators. The risk differences, confidence intervals, and unadjusted p-values described for the comparisons are recalculated from the posted summary statistics. They are therefore simple, unadjusted calculations, not a claim about the exact methods used by the study sponsor. The record lists no reported analyses. If a recalculation were inconsistent with a sponsor’s own reported analysis, the sponsor’s analysis would take precedence; the recorded discrepancy flag is false, and no conflicting sponsor analysis is reported.

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor a measure of effect size. The primary unadjusted p-values are <0.001 for both comparisons. They should be considered together with the outcome percentages and confidence intervals, not as stand-alone evidence. In particular, the registry record does not report an adjustment for multiple comparisons.

Why can binary outcomes need careful analysis?

A percentage reduces each participant’s assessment to whether the threshold was met. That makes the outcome straightforward to summarize, but it discards detail about the scale scores within each category and about individual changes. The reported endpoint is a Day 30 status, rather than a summary of the entire course of scores. The record does not report participant-level data, so it is not possible to reconstruct individual trajectories or alternative summaries.

General statistical context: estimates based on binary outcomes depend on how the outcome is defined and who has an observed assessment. If missing outcomes differ across groups or are related to the outcome, a complete-case percentage may not describe the intended population without further assumptions or analysis. The primary endpoint description names an intent-to-treat population, but the registry record does not report how missing Day 30 assessments were handled, whether imputation was used, or how the differing outcome denominators arose.

What do the planned sample-size illustrations mean?

The sample-size figures are planning illustrations calculated from observed effects, not the original trial’s documented design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. The illustrations give participants per arm for the binary outcomes. General statistical context: a smaller target effect is harder to distinguish from random variation at a fixed significance level and power, so it generally requires more participants. The illustrations do not establish what sample size the trial should have used, because the original design rationale is not reported in the registry record.

Power is the probability, under a specified assumed effect and analysis, of rejecting the null hypothesis when that effect is present. The 80% and 90% columns describe different planned power targets under the stated assumptions. They are prospective planning quantities, not evidence about the probability that the observed result is true. The trial’s own sample-size justification and any interim analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The primary comparison intervals indicate the range of unadjusted risk-difference values compatible with the posted outcome counts under the recalculation. For 24 U versus placebo, the estimate is 0.600 and the 95% confidence interval is 0.495 to 0.705. For 12 U versus placebo, the estimate is 0.483 and the 95% confidence interval is 0.371 to 0.595. Both intervals lie above zero, indicating that the data are compatible with a higher outcome proportion in the active-dose groups under these calculations.

The intervals are not so narrow that they specify a single precise effect. The range of plausible risk differences remains appreciable, and the record does not report a prespecified adjusted analysis that could be compared with these recalculations. The estimates are unadjusted and do not incorporate any unreported treatment of missing data or multiplicity. Precision should therefore be understood as conditional on the posted counts and the calculation used, not as a complete measure of uncertainty about all possible sources of error.

The primary arm denominators are 104, 99, and 97. The registry record does not explain why these differ from one another or how the outcome denominators relate to all enrolled participants. The endpoint description says the intent-to-treat population included all enrolled participants, but the posted outcome denominators do not provide a full account of assessment availability or missing-data handling. That makes it difficult to assess whether the observed percentages represent all participants as intended.

Statistical precision and practical importance are separate questions. A confidence interval describes uncertainty in an estimated difference; it does not define what magnitude would matter to participants or clinicians. The registry record does not report a threshold for a clinically important difference. The results therefore support a description of the recorded group separation and its statistical uncertainty, but do not settle the importance or broader applicability of that separation.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are participants per arm for the binary outcomes, 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 illustration uses a target effect set to a stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm under those assumptions for a planned analysis with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher planned chance of detection. These are planning targets; they do not mean that a result is certain or that there is an 80% or 90% chance the treatment effect is real.

Read the effect-fraction rows as scenarios: planning for the full observed effect, for 75% of the observed effect, or for 50% of the observed effect. Smaller effects require more participants to detect under the same assumptions, so the figures increase as the target effect is reduced. The estimates are derived from the observed effect in this trial; future studies may have different underlying effects, event proportions, or analysis requirements.

This is not observed power. It is a planning illustration based on assumed effects and a specified calculation, rather than a retrospective measure of what the completed trial established. It does not replace the unreported original sample-size rationale, and it should not be used to infer that the trial was adequately or inadequately designed.

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 = 0.082; treatment proportion p₁ = 0.683; average p̄ = 0.383.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6873 = 1.3471.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5406 = 0.4550.
4. n = (1.3471 + 0.4550)² / (0.6002)² = 9.0, rounded up to 10 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 <- 0.0824742268041237                          # control proportion
p1 <- 0.682692307692308                          # 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(1797081)
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 = 10 (80% power), 12 (90% power)
 75% of observed effect: n per arm = 16 (80% power), 20 (90% power)
 50% of observed effect: n per arm = 30 (80% power), 40 (90% power)
power.prop.test: 9 
Simulated power at n = 10 per arm: 0.834 (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 one primary endpoint and three secondary outcomes. It does not report a multiplicity procedure, such as an adjustment to account for evaluating several outcomes or comparisons. The primary unadjusted p-values are therefore best read as results of the recalculated pairwise comparisons, not as values known to control the overall false-positive risk across all endpoints and comparisons. The record also does not report a testing hierarchy that would establish which secondary outcomes, if any, were intended to support formal claims after the primary analysis.

The record lists no reported analyses. The comparison estimates discussed for the primary and secondary outcomes are recalculated from the posted summary statistics. The detailed statistical analysis plan, including any covariate adjustment, stratification, sensitivity analysis, or interim analysis, is not reported in the registry record. The absence of those details means that the posted figures cannot be evaluated against a complete prespecified analysis plan.

The primary endpoint description identifies the intent-to-treat population as all enrolled participants. However, the outcome denominators differ by arm and across some outcomes. The registry record does not explain the reasons for those denominators, the amount or pattern of missing data, or the method used to handle missing assessments. It is therefore not possible to determine from the record whether all enrolled participants contributed to each endpoint in the intended way. Nor is it possible to assess whether missingness could have affected the group comparisons.

General statistical context: an intent-to-treat approach aims to preserve the benefits of random assignment by analyzing participants in their assigned groups, but the label alone does not specify how missing outcome data are treated. Imputation, complete-case analysis, and other strategies rely on different assumptions. The registry record does not report which strategy was used for these endpoint summaries. These gaps do not invalidate the posted percentages, but they limit the conclusions that can be drawn about robustness and the intended population.

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: inguinal hernia (1.0%), pneumothorax spontaneous (1.0%), cellulitis (0.7%), intervertebral disc protrusion (0.7%), cerebral infarction (0.7%).

The safety summaries report serious adverse events in 3 participants in the 24 U group, 2 in the 12 U group, and 2 in the placebo group. The corresponding numbers at risk in those safety summaries were 151, 143, and 97. Other adverse events were reported for 23, 39, and 5 participants, respectively, with the same group-specific numbers at risk. These are counts of participants affected as recorded, not measures of event severity beyond the serious-event classification.

The registry record lists serious-event terms with percentages: inguinal hernia and spontaneous pneumothorax at 1.0% each, and cellulitis, intervertebral disc protrusion, cerebral infarction, and diverticulitis at 0.7% each. It does not specify in that list which treatment group each term belongs to. The safety denominators differ from the primary-outcome denominators, and the record does not explain the populations or exposure periods underlying those safety summaries.

The deaths field is not reported in the registry record. These safety figures are descriptive and do not, on their own, establish whether an event was caused by treatment or whether groups differed reliably in risk. The record does not provide the detail needed to assess event timing, exposure-adjusted rates, or causal attribution.

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

The posted primary results show a higher percentage meeting the none-or-mild investigator rating at maximum smile on Day 30 in each botulinum toxin Type A group than in the placebo group. The recalculated unadjusted risk differences are positive, and their confidence intervals lie above zero. This describes the group-level results recorded for this endpoint and time point.

The result does not establish that every participant in an active-dose group improved, or that every participant in placebo did not. A group percentage is not an individual prediction. It also does not provide the full distribution of scale ratings or each participant’s change from baseline. The endpoint records a threshold status at Day 30, not the durability of an effect over time.

The record includes secondary outcomes that address other assessments, and their overall descriptive pattern is consistent with higher reported percentages in the active-dose groups. However, the registry record does not report multiplicity control or a full statistical analysis plan. Those secondary comparisons therefore do not eliminate uncertainty about how strongly to interpret the set of results.

The posted numbers alone do not establish clinical importance, long-term outcomes, or applicability to people beyond the trial population. The registry record does not report a threshold for a clinically important difference, detailed participant characteristics, missing-data methods, or results at later time points for the primary endpoint. The safety summaries also cannot establish causal relationships between study treatment and reported events.

These findings are statistical descriptions of a completed randomized trial, not individualized medical advice. They should be interpreted with the record’s incomplete reporting in mind, including the lack of detailed analysis methods and the unexplained variation in endpoint denominators.

17. Why This Trial Matters Statistically

This trial is statistically informative because it reports a binary, investigator-assessed endpoint with arm-specific percentages and denominators for two active-dose groups and placebo. The comparison allows readers to see both the observed outcome frequencies and the recalculated absolute differences, rather than relying on a p-value alone. The posted results also include confidence intervals, which make uncertainty around the unadjusted comparisons visible.

The endpoint definition matters. It reduces a graded facial-wrinkle scale to whether the participant reached the none-or-mild category at maximum smile on Day 30. That makes the outcome interpretable as a proportion, while also limiting what it captures: it does not preserve the full scale distribution or participant-level changes. The other listed outcomes show why an investigator’s assessment, a participant’s view, and an assessment at rest may provide related but distinct information.

The record also illustrates why registration details and analysis reporting matter. It identifies randomization, masking, and a parallel design, but does not report the original sample-size rationale, detailed statistical plan, handling of missing data, or a multiplicity strategy. The calculated sample-size illustrations can help readers understand the relationship between target effect and planning requirements, but they are not a record of the trial’s original design process.

Finally, the different denominators for efficacy and safety summaries reinforce the importance of understanding which population contributes to each result. Without explanations of those denominators and missing assessments, readers cannot fully assess the robustness or generalizability of the posted estimates. The trial is therefore useful for examining how binary outcomes and uncertainty are reported, while also demonstrating the limits of registry-level result detail.

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.

Several limitations are specific to the information in this registry record. Although the trial is described as randomized and double-masked, the record does not report the randomization procedure, who was masked, or how masking was maintained. The arm descriptions indicate a change from placebo to active treatment for additional treatments from day 180 onward, but the detailed retreatment criteria are incomplete. The record therefore does not support a detailed assessment of treatment exposure or later treatment patterns.

The primary outcome is a threshold-based investigator rating at maximum smile on Day 30. It does not provide the full distribution of scale categories, participant-level changes, or longer-term primary-outcome results. The registry record does not report participant characteristics that would help evaluate how closely the enrolled population resembles other populations.

Outcome denominators vary among arms and endpoints, but the record does not explain why. It does not report the amount or pattern of missing data or how missing assessments were handled. The primary description names an intent-to-treat population, but the posted denominators leave uncertainty about how that population contributed to the outcome summaries.

The record does not report inferential analyses or a detailed statistical analysis plan, and it does not describe adjustment for multiplicity. The comparisons are unadjusted recalculations from the posted summary statistics. The safety results also lack detail on event timing, exposure periods, and group assignment for the listed serious-event terms. These reporting gaps limit assessment of robustness, causal attribution, and applicability; they do not change what the posted counts and percentages state.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: BOTOX® in the Treatment of Crow's Feet Lines in Japan — NCT01797081.
• Registry record last updated 2019-04-16; status last verified 2019-04.
• Results first posted 2015-02-10.
• 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

NCT01797081 is a completed, randomized, double-masked, parallel-group Phase 3 trial sponsored by Allergan, titled “BOTOX® in the Treatment of Crow's Feet Lines in Japan.” The registry record reports enrollment of 300. The primary endpoint is the percentage rated none or mild on the investigator’s Facial Wrinkle Scale-Asian assessment of crow’s feet lines at maximum smile on Day 30.

The posted primary percentages were 68.3% for botulinum toxin Type A 24 U, 56.6% for 12 U, and 8.2% for placebo. Recalculated unadjusted risk differences versus placebo were 0.600 and 0.483, respectively; both unadjusted p-values were <0.001. The registry record does not report a detailed statistical analysis plan, multiplicity handling, or missing-data methods. The estimates should therefore be read as descriptions of the posted results, with those reporting limitations in mind.