Efficacy and Safety of Esflurbiprofen Hydrogel Patch in the Treatment of Local Acute Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Esflurbiprofen Hydrogel Patch in the Treatment of Local Acute Pain (NCT04908748), a randomized phase 2 study. The primary outcome is Change of Pain-on-movement (POM) Compared to Baseline.

2. Clinical Question

The trial’s stated objective was to assess efficacy and safety and to test whether the active patch was superior to placebo, with acceptable local tolerability. Pain-on-movement was assessed on a visual analogue scale, with 0 indicating no pain and 100 indicating extreme pain. The reported primary outcome is a change from baseline, so negative values represent a reduction in the recorded pain score.

This is a comparison of group averages at a specified follow-up, not a description of every participant’s experience. The posted results also include responder and resolution outcomes at 72 hours and 168h. Those outcomes provide related perspectives on the short-term course of symptoms, but they do not replace the primary question about mean change in pain-on-movement.

3. Trial Design

The registry identifies this as a completed Phase 2 study with randomized allocation, quadruple masking and a parallel-group model. Enrollment was 200. The active arm received an esflurbiprofen hydrogel patch; the control arm received a placebo patch described as otherwise indistinguishable from the investigational patch. The sponsor was Teikoku Seiyaku Co., Ltd. The registry lists the study start as 2021-05-20 and primary completion as 2021-11-09.

The clinical setting was acute soft-tissue injury involving the extremities after blunt trauma. The listed conditions include soft tissue injuries, contusions, strains, sprains and bruises. The stated treatment purpose was local, symptomatic and short-term treatment. The primary outcome population was the Full Analysis Set, defined in the record as all randomized patients who received at least one dose of study drug.

Random allocation is intended, in general, to make the groups comparable at the start of a trial with respect to both measured and unmeasured characteristics. Masking is intended to limit the influence of knowledge about treatment assignment on care, assessments or reporting. These are general design considerations; the registry record does not specify how masking was implemented for each role or describe checks of masking.

The record reports the primary outcome as a mean change from baseline to Visit 5, 72 hours after initiating treatment. It also posts several secondary outcomes, including pain measures, response and resolution measures, and global efficacy assessments. Details of the full visit schedule, treatment duration beyond the primary timeframe, eligibility criteria and the original sample-size justification 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: The Full Analysis Set (all randomized patients who received at least one dose of study drug).

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 Change of Pain-on-movement (POM) Compared to Baseline, measured over Change from baseline to Visit 5 (72 hours after initiating treatment).

The primary endpoint is change in pain-on-movement from baseline to Visit 5, 72 hours after treatment began. Pain-on-movement was rated using a visual analogue scale ranging from 0 for no pain to 100 for extreme pain. The registry describes the outcome as a mean and gives standard deviations for each group. A change score captures how the recorded pain rating shifted between baseline and the specified follow-up; a negative change indicates a lower score at follow-up than at baseline.

Pain during movement is relevant to acute extremity injuries because it records symptoms during activity rather than only at rest. As a continuous measure, it retains information across the scale rather than reducing each rating to a binary category. Comparing group means is therefore one way to summarize the average short-term change in the two randomized groups.

Mean change does not show the range of individual experiences. Participants can have different changes even when their group mean is the same, and a group average does not establish how many people experienced a particular degree of improvement. The standard deviations describe variability in the group-level outcome; they are not confidence intervals for the mean. The posted primary result concerns the specified 72-hour assessment, not longer-term pain or function.

7. Results Posted in the Registry

• Active Arm: mean -50.70 versus -21.60 on control; difference -29.10 (95% CI -32.29 to -25.91), standardized effect d = -2.53; 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.

Responder Rate 1

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Arm: 94.9% (93/98) versus 14.7% (15/102) on control; risk difference 80.2 percentage points (95% CI 72.1 to 88.3), risk ratio 6.45 (4.03–10.32); 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 Active Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Resolution of Soft Tissue Injury/Contusion

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Arm: 93.9% (92/98) versus 48.0% (49/102) on control; risk difference 45.8 percentage points (95% CI 35.0 to 56.6), risk ratio 1.95 (1.59–2.41); 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 Active Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Responder Rate 2 at 168h

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Arm: 93.9% (92/98) versus 48.0% (49/102) on control; risk difference 45.8 percentage points (95% CI 35.0 to 56.6), risk ratio 1.95 (1.59–2.41); 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 Active Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes extend the short-term picture beyond mean pain-on-movement change. They include responder outcomes, resolution of soft-tissue injury or contusion, pain at rest, pain-on-movement over time, time-to-reduction and resolution, and patient global assessments. Among the posted comparisons with numerical results, the binary responder and resolution outcomes favor the active arm. This is directionally consistent with the primary group-mean result, but these outcomes measure different aspects of symptoms and response.

The record lists 13 posted secondary outcomes and 16 outcome measures overall, while numerical comparisons are included for a subset of the secondary outcomes. A secondary endpoint’s result should be understood according to its own definition and timeframe; it should not be treated as another measurement of the primary endpoint. The posted results do not establish that all secondary endpoints were analyzed or reported in the same way.

The secondary comparisons are unadjusted, and the registry record does not report a multiplicity procedure. In general, evaluating many outcomes increases the chance that some results will appear statistically notable by chance, even if each test is considered separately. This is why secondary findings without a stated adjustment generally carry less inferential weight than the designated primary result. The secondary pattern can support context and consistency, but it does not independently confirm the primary analysis or resolve concerns about selective reporting.

Interpretation is further limited because the record does not give detailed definitions for every secondary outcome, analysis populations for each one, or handling of missing observations. The count-based results should therefore be read as posted endpoint summaries rather than a complete account of every participant’s clinical course.

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

• Pain-on-movement (POM) on VAS
• Area-under-the-curve for POM on VAS
• Pain-at-rest on VAS
• Time to Meaningful and Optimal Reduction
• Time to Complete Resolution of Pain
• Responder Rate 1
• Global Efficacy Assessments 1 by Patient
• Global Efficacy Assessments 2 by Patient

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant has a change score on the visual analogue scale, and the arm-level result is expressed as a mean. The registry gives a standard deviation for each arm. In general, a mean describes the center of a group’s observed values, while a standard deviation describes how dispersed those values are around the mean. The standard deviation is not the uncertainty around the estimated mean difference.

What does the unadjusted comparison represent?

The recalculated comparison subtracts the placebo-arm mean change from the active-arm mean change using the posted summary statistics. The estimate is -29.1 units. This is a simple unadjusted contrast between the posted group means, not an estimate adjusted for baseline measurements or other covariates. The negative sign follows the order of the comparison and the scale direction: more negative change corresponds to a greater decrease in the pain score.

The recalculation uses the posted group sizes, means and standard deviations to estimate uncertainty around that contrast. This approach relies on a statistical approximation for the sampling distribution of the difference in means. It is useful as a transparent check based on summary statistics, but it cannot reproduce an analysis that uses participant-level observations or covariate adjustment.

What does ANCOVA add?

The registry reports an ANCOVA result as a least-squares mean difference. In general, analysis of covariance estimates a group contrast while accounting for one or more covariates in a statistical model. For a change outcome, baseline measurements may be among the relevant covariates, but the exact covariates and model specification are not reported in the registry record. A least-squares mean difference is therefore a model-based estimate and need not have exactly the same confidence limits as an unadjusted calculation.

The sponsor-reported ANCOVA estimate is -29.1 with a 95% confidence interval from -32.2 to -26.0 and p < 0.001. The recalculated unadjusted interval is -32.29 to -25.91, with p < 0.001. Both estimates point in the same direction and are close in magnitude. The registry’s own analysis is the trial’s reported inferential analysis; the recalculation is a supplementary summary-statistic analysis.

How should the p-value be read?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null model and its assumptions were correct. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The posted primary p-values are below the stated conventional thresholds in their respective formats, but the record does not provide the full model specification or a broader statistical analysis plan.

The registry reports one primary analysis and labels it a superiority analysis. The record does not report whether the endpoint, analysis population, direction of testing, covariates or handling of missing observations were specified in advance in a protocol or statistical analysis plan. These details matter when assessing how the reported inferential result relates to the original analysis plan.

Why does variability matter?

In general, variability affects the precision of a group comparison: more variation makes it harder to estimate a mean difference precisely when other features are held constant. Here, the reported standard deviations are 11.1 in the active arm and 11.9 in the placebo arm. A standard deviation describes spread among observed scores; a confidence interval describes uncertainty in an estimated quantity. They answer different questions and should not be interchanged.

The posted secondary outcomes include binary counts as well as continuous pain measures. For a binary outcome, the reported comparison can be expressed as a difference between the proportions of participants meeting the outcome. In general, such comparisons depend on both the number of events and the number of participants assessed. The registry posts unadjusted comparisons for the listed secondary results; details about any covariate-adjusted or multiplicity-controlled secondary analyses are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor-reported primary 95% confidence interval for the least-squares mean difference extends from -32.2 to -26.0 units. The unadjusted recalculation gives a 95% confidence interval from -32.29 to -25.91 units. Both intervals lie on the negative side of zero, consistent with the active arm having a larger mean reduction in pain-on-movement on the scale used.

In general, a confidence interval describes uncertainty in an estimated population quantity under the assumptions of the analysis. A 95% confidence interval is produced by a method that, over repeated comparable studies under its assumptions, would cover the target quantity at the stated rate. It is not a statement that there is a 95% probability that this particular interval contains the true effect, and it does not describe the distribution of individual responses.

The sponsor’s interval comes from ANCOVA, whereas the recalculated interval comes from an unadjusted comparison of posted summary statistics. Their endpoints differ because they arise from different analytical approaches and rounding. The registry record gives the sponsor analysis as the reported trial result; the recalculation offers a separate check rather than a replacement.

Precision should be considered separately from practical importance. The interval indicates that the estimated average difference is relatively tightly bounded under the stated analysis, but the record does not report a clinically important difference threshold for this scale. It also does not provide a distribution of individual changes or subgroup-specific intervals. Consequently, the group-level interval cannot establish how consistently participants experienced a reduction or whether the magnitude meets a particular clinical criterion.

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 calculations. For outcomes other than time-to-event outcomes, the figures are participants per arm; the time-to-event convention of total events does not apply to these outcomes. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The trial’s original sample-size assumptions are not reported in the registry record.

The 80% power column describes the estimated number of participants per arm under those planning assumptions for a design with an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities under a model, not probabilities that the treatment effect is true.

For the primary outcome, the planning illustration lists 3 participants per arm for 80% power and 4 for 90% power when planning for 100% of the observed effect. For 50% of the observed effect, it lists 10 participants per arm for 80% power and 14 for 90% power. The figures change with the assumed effect size: smaller effects need more participants to detect, all else being equal. The curve represents this relationship across effect assumptions; it does not establish the sample size needed for a different population or study design.

These planning calculations are not observed power. They are retrospective illustrations tied to the observed estimate, which is itself uncertain, and should not be interpreted as evidence that the completed trial was adequately planned. The posted enrollment and group results are trial details; the planning estimates are hypothetical design calculations.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -29.100; pooled standard deviation σ = 11.515.
2. n = 2 × (1.96 + 0.842)² × 11.515² / -29.100² = 2.5, rounded up to 3 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 <- -29.1                      # observed difference in means
sigma <- 11.515027511294                     # 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(4908748)
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 = 3 (80% power), 4 (90% power)
 75% of observed effect: n per arm = 5 (80% power), 6 (90% power)
 50% of observed effect: n per arm = 10 (80% power), 14 (90% power)
power.t.test: 3.7 
Simulated power at n = 3 per arm: 0.647 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry’s own primary analysis is an ANCOVA reported as a least-squares mean difference of -29.1 units, with a 95% confidence interval from -32.2 to -26.0 and p < 0.001. The additional recalculation uses the posted arm-level means and standard deviations to form a simple unadjusted mean difference. It gives -29.1, with a 95% confidence interval from -32.29 to -25.91 and p < 0.001.

The point estimates match at the precision reported, and the intervals support the same direction of difference. Small differences in confidence limits and p-value presentation are expected when the analyses use different methods and rounding. The recalculation does not reconstruct the ANCOVA or account for any covariates that may have been included in the sponsor’s model.

The sponsor-reported analysis should be treated as the trial’s primary inferential result. The recalculation is useful as a transparent, unadjusted check of the posted summary data, but it should not be given precedence over the registry’s reported model-based analysis. Details needed to reproduce the ANCOVA, including its covariates and full specification, are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and reports one primary analysis. It also lists multiple secondary outcomes and posts several secondary comparisons. When many outcomes or comparisons are examined, the chance of at least one apparently significant result can increase. In general, a multiplicity plan may control that risk through a prespecified testing hierarchy or other adjustment. Whether such a plan was used for the secondary outcomes is not reported in the registry record.

The posted secondary p-values are unadjusted. They should therefore be interpreted as individual comparisons, without assuming control of the overall false-positive risk across the set of secondary analyses. The record does not report a family-wise error procedure, false-discovery procedure, hierarchy among secondary endpoints or adjustment of their confidence intervals. This does not change the numerical results, but it limits how strongly a collection of nominally significant secondary results can be interpreted.

The primary analysis population is described as all randomized patients who received at least one dose of study drug. This definition does not include randomized participants who received no dose, and it is not the same description as an all-randomized population. The record does not report the number of participants excluded from this population, the reasons for any exclusions, or whether additional analysis populations were used.

Missing-data methods are also not reported in the registry record. The posted primary outcome is a change from baseline to a 72-hour visit, but the record does not explain how missing baseline or follow-up measurements were handled, whether imputation was used, or whether sensitivity analyses assessed alternative assumptions. Missingness can affect an estimate if the probability of having an observed measurement is related to outcomes or treatment assignment. Without those details, the reader cannot assess the robustness of the result to missing observations.

The record does not report the original statistical analysis plan, interim analyses, or the detailed rules for endpoint assessment and analysis. These omissions leave uncertainty about prespecification and analytic flexibility. They are limitations of the information available in the registry record, not evidence that a particular procedure was or was not used.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events in 0 participants in the active arm and 0 in the control arm. Deaths are also reported as 0 in each arm. The record lists other adverse events in 9 participants in the active arm and 16 in the control arm. These are counts, not rates adjusted for exposure time, and the registry extract does not give further detail about event types or severity for the non-serious events.

No serious adverse event terms are listed. The absence of reported serious events in these groups should not be read as proof that serious events cannot occur; a trial’s safety counts describe what was observed and reported under its conduct and follow-up. The record does not provide enough information to evaluate event timing, duration, causal attribution, withdrawals due to adverse events or the completeness of safety follow-up. The stated objective included local tolerability, but the detailed local tolerability findings are not reported in the registry record.

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

The posted primary result shows a larger mean reduction in pain-on-movement in the active arm than in the placebo arm at the specified 72-hour assessment. The sponsor-reported ANCOVA estimate and the unadjusted recalculation agree in direction and have similar point estimates. Their confidence intervals are on the negative side of zero, indicating a difference favoring a greater reduction in the active arm under the outcome’s scale direction.

This is a result for a group average in a particular trial population and at a particular follow-up. It does not mean every participant had the same response, and it does not reveal the number of participants who experienced a particular amount of change. The posted responder and resolution results provide additional categorical summaries, but they do not describe all dimensions of recovery.

The result does not establish how long any difference lasted, whether it affected function, or whether it applies equally across the different injury types listed in the record. The registry does not report a clinically important threshold for the visual analogue scale, detailed subgroup results, or longer-term primary follow-up. Statistical evidence of a group difference is not by itself a judgment about clinical importance.

Safety interpretation is similarly limited. The registry reports no serious adverse events or deaths in either arm, alongside other adverse-event counts. Those observations are not proof of no risk, and the extract lacks enough detail to characterize the events fully. The findings should be read as evidence from a completed Phase 2 trial with the posted population, outcomes and follow-up, not as a guarantee of results in other settings or for other patients.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition and direction of a scale matter. The outcome is change in pain-on-movement, and lower scores correspond to less pain. Negative changes indicate reductions from baseline, while the negative between-group estimate indicates a larger reduction in the active arm under the comparison’s stated ordering. Without those conventions, the sign of the estimate could be misread.

It also demonstrates the distinction between a raw group comparison and an adjusted model. The simple recalculation from means and standard deviations gives a useful independent check, while the registry’s ANCOVA supplies the reported model-based result. Similar point estimates do not make the analyses identical; they answer the comparison using different methods and may rely on different assumptions.

The confidence interval contributes information beyond the p-value by displaying the range of effect estimates compatible with the analysis. Yet statistical precision does not settle clinical importance. The registry does not give a clinically important threshold for the scale, and group averages do not describe the spread of individual responses.

Finally, the secondary outcomes and safety counts show why interpretation depends on more than statistical significance. Multiple unadjusted secondary comparisons require caution, while sparse safety summaries cannot establish the absence of risk. The trial record supports a focused reading of the short-term primary comparison, with clear limits on broader conclusions.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint is limited to change in pain-on-movement at 72 hours. The registry record does not report a longer-term primary assessment or a clinically important difference threshold for the visual analogue scale. Thus, the posted estimate describes a short-term average score contrast without establishing its practical meaning or durability.

The record does not report the ANCOVA covariates, full statistical model, original sample-size justification, detailed eligibility criteria or full analysis plan. The available information is therefore insufficient to reproduce the sponsor’s model or assess all prespecification decisions. The summary-statistic recalculation is unadjusted and cannot address these gaps.

The stated primary population includes randomized patients who received at least one dose. The record does not give further detail on exclusions, missing data, imputation, sensitivity analyses or whether other populations were examined. It also does not describe how each secondary endpoint was defined and analyzed in full. Several secondary results are unadjusted, and a multiplicity approach is not reported.

The safety summary gives counts of serious events, other adverse events and deaths but not detailed event descriptions, timing, exposure-adjusted rates, withdrawals or local tolerability findings. Zero reported serious events and deaths do not establish that risks are absent. The posted material also does not provide subgroup estimates that would show whether results differed among strains, sprains, bruises or other listed conditions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Esflurbiprofen Hydrogel Patch in the Treatment of Local Acute Pain — NCT04908748.
• Registry record last updated 2023-09-28; status last verified 2023-09.
• Results first posted 2023-09-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed Phase 2 trial was randomized, quadruple-masked and parallel-group, comparing an esflurbiprofen hydrogel patch with a placebo patch for acute pain after extremity strains, sprains or bruises following blunt trauma. The primary endpoint was mean change in pain-on-movement from baseline to Visit 5, 72 hours after treatment began, in the Full Analysis Set.

The reported ANCOVA estimate was a least-squares mean difference of -29.1 units, with a 95% confidence interval from -32.2 to -26.0 and p < 0.001. The unadjusted recalculation gave -29.1, with a 95% confidence interval from -32.29 to -25.91 and p < 0.001. The record also posts secondary response and resolution results and safety counts, with important limits around multiplicity, missing-data methods and detailed safety reporting not described in the registry record.