Study Investigating the Safety and Efficacy of HP802-247 in the Treatment of Venous Leg Ulcers >12 cm2 to ≤ 36 cm2: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Investigating the Safety and Efficacy of HP802-247 in the Treatment of Venous Leg Ulcers >12 cm2 to ≤ 36 cm2 (NCT01737762), a randomized phase 3 study. The primary outcome is Wound Closure.

2. Clinical Question

This question focuses on whether complete closure was recorded by the end of the stated treatment period. It is a comparison of proportions, not a comparison of how quickly wounds closed or of the amount of change in wound size. The registry also lists time in days to closure as a secondary outcome, which addresses timing rather than the primary outcome’s closed-or-not-closed status.

The clinical comparison is between two assigned treatment strategies that both include compression therapy. Thus, the posted contrast is not HP802-247 versus no care: it is HP802-247 with compression compared with vehicle with compression. The record identifies a randomized, quadruple-masked, parallel-group study. It does not report further details about who was masked or the eligibility criteria beyond the stated condition and ulcer-size range. The primary result should therefore be interpreted as a comparison in the trial’s recorded outcome groups, with those limits in mind.

3. Trial Design

The registry describes NCT01737762 as a Phase 3 randomized, quadruple-masked, parallel-group, vehicle-controlled study. It is marked completed. The record gives enrollment as 155, with a start date of 2012-11 and primary completion in 2015-11. Healthpoint is named as sponsor.

The study compared HP802-247 plus compression therapy with vehicle plus compression therapy. The HP802-247 description specifies fibrinogen and thrombin solutions containing living, irradiated, growth-arrested keratinocytes and fibroblasts, with administration every 14 days. The vehicle is described as the same types of solutions without cells. The primary outcome was the number of participants with complete wound closure over the 16-week treatment period from baseline.

The registry’s brief summary says at least 250 subjects would participate and describes approximately 50 sites in the United States and Canada. That narrative differs from the enrollment value recorded in the trial information. The record does not explain the difference, so the two statements should not be reconciled by assumption. Nor does the registry record report the original sample-size justification or the original design assumptions.

The primary outcome groups include 69 participants assigned to HP802-247 and 70 assigned to vehicle. These are the group counts attached to the posted primary outcome, not an account of every participant enrolled or of all analysis populations. The record does not describe how participants moved through the trial, whether all randomized participants contributed to each outcome, or how missing outcome data were handled. The adverse-event risk groups have different recorded counts, which should be read as the denominators for those safety summaries rather than treated as the primary outcome group sizes.

4. Participant Flow and Accounting

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

Before assignment: Subjects entered a 2-week run-in; subjects whose wound radius decreased by \< 0.349 cm/2weeks and met all other inclusion/exclusion (I/E) criteria were eligible for randomization. After completion of the treatment period, subjects entered a three-month follow up period.

Overall Study

Reasons for not completing this period:

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 Wound Closure, measured over 16 Weeks.

The primary endpoint is wound closure, recorded as the number of participants with complete wound closure during the 16-week treatment period from baseline. The endpoint turns each participant’s wound status into a binary outcome for the comparison: closure was either recorded or was not recorded within the stated period. The registry does not provide a separate definition of how complete closure was assessed.

This kind of endpoint is useful when the clinical question concerns the proportion of participants reaching a defined state by a specified time. It differs from an endpoint based on wound area, which would retain information about the degree of change, and from time to closure, which concerns how long closure takes. Time in days to closure is listed as a secondary outcome in this trial; it does not replace the primary question about the proportion with closure during the period.

The posted primary outcome records 17 participants with closure among 69 in the HP802-247 group and 23 among 70 in the vehicle group. The comparison is therefore an unadjusted contrast in the observed closure proportions. It does not, by itself, describe the experience of people outside the trial or establish why any participant’s wound did or did not close. The registry record does not report further details about endpoint adjudication, assessment procedures, or the handling of participants whose closure status was unavailable.

7. Results Posted in the Registry

• HP802-247: 24.6% (17/69) versus 32.9% (23/70) on control; risk difference -8.2 percentage points (95% CI -23.2 to 6.8), risk ratio 0.75 (0.44–1.28); unadjusted two-proportion z-test p = 0.285.

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.

Time in Days to Closure

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • HP802-247: mean 83.40 versus 87.10 on control; difference -3.70 (95% CI -16.46 to 9.06), standardized effect d = -0.10; z-test p = 0.570.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between HP802-247 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: time in days to closure. Its direction is broadly consistent with the primary result in the limited sense that neither posted comparison shows a clear separation between groups. However, the endpoints measure different things. The primary outcome concerns whether closure was recorded during the stated period; the secondary outcome concerns the average recorded time to closure. Agreement or disagreement between them should not be treated as independent confirmation because they describe related aspects of wound closure.

The secondary mean comparison is imprecise: its confidence interval includes no difference and values in either direction. The registry record lists no reported analyses for this endpoint. It does not describe how time was defined for participants without recorded closure, whether observations were censored, or which analysis population was used. Those omissions make it especially important not to infer a particular time-to-event analysis from the endpoint’s title alone.

Secondary outcomes are often useful for adding context, but their evidential weight depends on how they were planned and analyzed. When many outcomes or comparisons are examined, the chance of seeing an apparently notable result by chance can increase. In general, multiplicity procedures may address that issue, but the registry record does not report whether any were planned or used. The secondary result is unadjusted, and no hierarchy or confirmatory role is reported.

Accordingly, the secondary outcome can be considered supportive context rather than a separate decisive test of the primary question. Its uncertainty, the absence of a reported analysis description, and the unreported multiplicity approach all limit the strength of interpretation. The registry record does not report additional secondary endpoint results that would establish a broader pattern across other clinical outcomes.

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

• Time in Days to Closure

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant is counted according to whether complete wound closure was recorded during the 16-week period. The posted group summaries give the number with closure and the number in each outcome group. A comparison of proportions addresses the difference in the frequency of this event between assigned groups. Because both groups received compression therapy, the comparison concerns adding HP802-247 rather than replacing compression therapy with it.

What does the risk difference describe?

The risk difference is the HP802-247 group’s event proportion minus the vehicle group’s event proportion. A negative value means the observed proportion was lower in the HP802-247 group; a positive value would mean it was higher. The posted estimate is negative, consistent with the counts of 17 closures among 69 participants and 23 among 70 participants. The confidence interval describes a range of values compatible with the data under the method’s assumptions. Because the interval includes zero, the results do not distinguish clearly between a negative difference, no difference, and a positive difference.

Risk differences use the event proportions directly and preserve an absolute scale. Other measures can express the contrast differently. A risk ratio compares the event proportions as a ratio, while an odds ratio compares the odds of the event. These measures answer related but non-identical questions and can have different numerical values. The registry posts ratio estimates as well, but an interpretation should not rely on a single scale without considering the uncertainty attached to it. No adjusted estimate is reported in the registry record.

How should the p-value be read?

The posted primary p-value is unadjusted. In general, a p-value describes how compatible the observed data are with a specified null model, under the test assumptions. It does not give the probability that a treatment effect exists, and it does not tell whether a difference is important to patients. A p-value is also not a substitute for the size and precision of the estimated contrast. In this trial, the interval around the primary risk difference includes zero, which is an important part of the interpretation alongside the p-value.

The registry record does not report the detailed test specification, covariate adjustment, or analysis population for the primary result. It is therefore not possible to say from the record whether the reported comparison accounts for baseline factors or how participants with unavailable outcome data were treated. The result should be understood as the posted unadjusted comparison, without attributing unreported analytical choices to the investigators.

What does the secondary mean comparison measure?

Time in days to closure is summarized by a mean and standard deviation for each group. The mean is the arithmetic average of the recorded times, while the standard deviation describes variation among observations around that mean. The posted means are 83.4 days for HP802-247 and 87.1 days for vehicle; the mean difference is -3.7 days. Its confidence interval extends from -16.46 to 9.056, and the unadjusted p-value is 0.57. Since the interval includes zero, the data do not yield a precise distinction in average time between the groups.

A mean-based comparison is sensitive to the distribution of times and to how observations without closure are handled. The registry record does not report those details, nor does it provide a reported secondary analysis. The displayed summaries should not be taken as evidence that the time-to-closure outcome was analyzed with a particular survival method or under a particular censoring rule.

Why do confidence intervals matter?

A confidence interval communicates uncertainty around an estimate, rather than merely identifying a single best estimate. In general, a wider interval indicates less precision under the specified method. An interval that includes the no-difference value leaves a range of interpretations consistent with the data. It does not prove there is no effect; it indicates that the estimate is not sufficiently precise to rule out values on either side of no difference under that method.

For a binary outcome, the amount of information depends in part on the event counts and group sizes. For a mean outcome, information also depends on variability. The registry reports standard deviations of 33.8 days and 42.5 days for the secondary endpoint. Greater variability can make a mean difference harder to estimate precisely when other features are similar. These general principles explain why the reported uncertainty deserves attention, but they do not establish what design or analysis choices were made in the original trial.

Finally, these are unadjusted re-calculations from the posted summaries, and the registry does not identify a discrepancy between the posted values and the calculations. Such calculations are useful for understanding the numerical contrast but do not replace a sponsor’s prespecified analysis, if one exists. The registry record does not report a sponsor analysis for the secondary outcome or provide enough information to reconstruct a comprehensive analysis plan.

11. Confidence Intervals and Precision

Precision concerns how narrowly a result estimates the underlying contrast. The primary risk-difference confidence interval extends from -0.232 to 0.068. It includes zero and covers negative as well as positive values. Thus, the data are compatible with a lower closure proportion in the HP802-247 group, little or no difference, or a higher proportion under the interval’s assumptions. The point estimate gives the direction of the observed contrast, but the interval shows why that direction should not be treated as a precise conclusion.

The secondary mean-difference interval runs from -16.46 to 9.056 days. It also includes zero and spans both directions. The posted mean difference is -3.7 days, but the interval indicates substantial uncertainty about the magnitude and direction of the average-time contrast. The posted unadjusted p-values, 0.285 for the primary comparison and 0.57 for the secondary comparison, should be read alongside these intervals rather than as standalone verdicts.

In general, confidence intervals summarize sampling uncertainty under a statistical method and its assumptions. They do not account automatically for every potential source of bias, such as missing outcomes, differences in follow-up, or outcome measurement issues. The registry record does not report enough information to assess those issues in detail. Nor does an interval describe the range of outcomes for individual participants; it concerns uncertainty in the estimated group contrast.

The posted primary outcome group counts are 69 and 70, and the event counts are 17 and 23. The secondary summaries show standard deviations of 33.8 days and 42.5 days. These features help contextualize precision: estimates based on limited event information or variable measurements can remain uncertain. The record does not report a prespecified precision target, so the intervals should be interpreted as the uncertainty around the posted estimates, not as evidence that the study met a particular precision goal.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power, not total event counts. The registry states that the illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each outcome, the effect to detect is set as a stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For the primary outcome, planning for 100% of the observed effect gives 475 participants per arm for 80% power and 636 participants per arm for 90% power. Planning for 75% of the observed effect gives 863 participants per arm for 80% power and 1,155 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,980 participants per arm for 80% power and 2,650 participants per arm for 90% power.

For time in days to closure, the corresponding figures are 1,694 and 2,267 participants per arm for 100% of the observed effect; 3,011 and 4,031 for 75%; and 6,774 and 9,068 for 50%. Within each pair, the first figure targets 80% power and the next targets 90% power.

In plain terms, power is the chance that a study using the stated assumptions would detect an effect of the specified size under the planning model. The higher power target requires more participants per arm. Smaller effects also require more participants per arm because they are harder to distinguish from random variation. These figures are planning illustrations based on the observed effects, not observed power and not a reconstruction of the trial’s original design.

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 = 0.329; treatment proportion p₁ = 0.246; average p̄ = 0.287.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6401 = 1.2545.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6374 = 0.5365.
4. n = (1.2545 + 0.5365)² / (-0.0822)² = 474.8, rounded up to 475 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 <- 0.328571428571429                          # control proportion
p1 <- 0.246376811594203                          # 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(1737762)
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 = 475 (80% power), 636 (90% power)
 75% of observed effect: n per arm = 863 (80% power), 1,155 (90% power)
 50% of observed effect: n per arm = 1,980 (80% power), 2,650 (90% power)
power.prop.test: 474.8 
Simulated power at n = 475 per arm: 0.799 (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 does not report a multiplicity strategy for the primary and secondary outcomes, nor does it identify a hierarchy of outcomes or a confirmatory testing sequence. This matters because interpreting several outcomes or analyses as separate opportunities to find a difference can make isolated findings less persuasive. In general, prespecifying a primary outcome and controlling the interpretation of additional tests can help readers distinguish confirmatory evidence from exploratory findings. The primary endpoint is identified, but further multiplicity details are not reported in the registry record.

The record does not report whether interim analyses were planned or conducted. It also does not describe the original statistical analysis plan, the handling of protocol deviations, or whether the primary result was adjusted for baseline characteristics. Those details should not be inferred from the posted unadjusted estimates.

Missing-data methods and analysis populations are also not reported in the registry record. The primary outcome summaries include 69 participants in the HP802-247 group and 70 in the vehicle group, but the record does not say whether these counts represent all randomized participants, an intention-to-treat population, a per-protocol population, or another defined set. It does not state how participants with missing closure status were handled or whether sensitivity analyses were performed. For the secondary endpoint, the record also does not explain how missing times or participants without closure were treated.

These omissions affect interpretation because analysis choices can influence estimates and uncertainty, particularly when outcome data are unavailable or when different populations are used. They do not demonstrate that the trial’s analyses were inappropriate; they mean that the registry record does not provide enough detail to assess those choices. The adverse-event risk groups are reported separately, with different denominators from the primary outcome summaries, and should not be assumed to define the efficacy analysis population.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cellulitis (2.6%), sepsis (1.3%), skin infection (1.3%), fall (1.3%), rib fracture (1.3%).

The safety summaries use risk groups of 77 participants for HP802-247 and 78 for vehicle. Serious adverse events were recorded for 7 participants in each group. Other adverse events were recorded for 23 participants in the HP802-247 group and 19 in the vehicle group. No deaths were recorded in either group. These are descriptive counts for the safety summaries; the denominators differ from the primary outcome group counts, and the record does not explain the relationship between those populations.

The registry lists cellulitis at 2.6% among the leading serious adverse-event terms. Sepsis, skin infection, fall, rib fracture, and encephalopathy are each listed at 1.3%. These terms and percentages describe the reported serious-event summaries. The record does not provide enough detail to determine event duration, severity grading beyond serious-event classification, relatedness to treatment, or whether participants could have experienced more than one event. Therefore, the counts and terms should not be interpreted as proof that treatment caused or prevented an event, or as a complete account of individual safety histories.

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

The posted results describe observed outcomes in the trial groups, not a guarantee of what would happen for an individual or in another setting. For wound closure, the recorded proportion was lower in the HP802-247 group than in the vehicle group. The confidence interval includes no difference and extends to values in either direction, so the estimate is uncertain. The result does not establish that HP802-247 improves or worsens wound closure.

The secondary mean comparison likewise has an interval that includes no difference. It does not establish a clear difference in average time to closure. Because the primary endpoint concerns closure status during the treatment period and the secondary endpoint concerns days to closure, neither result should be substituted for the other. The registry does not report the analysis details needed to determine how participants without a recorded closure contributed to the secondary summary.

The study compared HP802-247 plus compression therapy with vehicle plus compression therapy. Its results therefore speak to that comparison in the reported trial groups, rather than to HP802-247 without compression or to a comparison with no treatment. The registry record identifies venous leg ulcers within the stated area range, but provides limited detail on the wider characteristics of participants and their care. Generalizing beyond the recorded study population requires information not reported in the registry record.

Safety counts are also descriptive. The record reports serious and other adverse events and no deaths in either safety group, but does not provide event attribution or enough detail to assess all aspects of safety. A count in a group cannot by itself show that an event was caused by the assigned intervention. Absence of recorded deaths in these summaries does not establish the absence of other risks.

Overall, the registry results provide estimates and uncertainty for a defined clinical comparison. They do not settle the treatment effect, demonstrate a mechanism, or answer questions about outcomes beyond those reported. The missing analysis details, the difference between the narrative enrollment statement and the recorded enrollment value, and the unreported original design assumptions further limit conclusions about how the trial was planned and analyzed.

17. Why This Trial Matters Statistically

This trial illustrates why a numerical point estimate should not be interpreted without its uncertainty. The primary comparison has an observed direction, but its confidence interval includes no difference and values on both sides. The secondary comparison also has an interval spanning both directions. Reading the estimate, interval, and outcome definition together gives a more careful account than treating any single number as a verdict.

It also demonstrates the distinction between outcomes that may sound similar but answer different questions. Wound closure during a specified period is a binary outcome, while time in days to closure summarizes timing. Related outcomes can provide context, but they are not interchangeable, and the available registry descriptions do not establish how the secondary outcome was analyzed.

The treatment contrast is another important statistical detail. Both groups received compression therapy, so the comparison is HP802-247 plus compression versus vehicle plus compression. Clear description of the comparator prevents readers from interpreting the contrast as treatment versus no treatment. The vehicle description also makes explicit that it contained the fibrinogen and thrombin solutions without cells.

Finally, the registry record distinguishes information that is reported from information that is not. It includes group outcome summaries, an unadjusted comparison, and planning illustrations based on observed effects. It does not report the trial’s original sample-size justification, missing-data methods, analysis populations, or multiplicity approach. Recognizing those boundaries is part of sound statistical interpretation: estimates can be described precisely while avoiding claims that the available record cannot support.

18. Limitations

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

The registry record leaves several trial-specific questions unanswered. It does not explain the difference between the enrollment value of 155 and the brief summary’s statement that at least 250 subjects would participate. It also does not report the original sample-size justification or design assumptions, so the posted planning illustrations should not be treated as a description of the trial’s original power calculation.

The record does not give detailed eligibility criteria beyond venous leg ulcers in the stated area range, nor does it provide baseline characteristics for the outcome groups. It does not describe the process for confirming complete closure, the timing or frequency of wound assessments, or the handling of participants whose closure status was unavailable. These omissions restrict assessment of measurement and missing-data concerns.

For time in days to closure, the registry does not report how participants without closure were handled or whether follow-up ended at a particular point for all participants. It lists no reported analyses for this endpoint. The absence of those details means the mean summaries cannot be interpreted as a fully described time-to-event analysis.

The record also does not report the analysis population, covariate adjustment, multiplicity strategy, or whether interim analyses were conducted. Safety summaries do not include event attribution, and their risk-group denominators differ from the primary outcome denominators. These are limits on what can be evaluated from the registry record; they do not establish that a particular method was or was not used outside the information posted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study Investigating the Safety and Efficacy of HP802-247 in the Treatment of Venous Leg Ulcers >12 cm2 to ≤ 36 cm2 — NCT01737762.
• Registry record last updated 2017-07-26; status last verified 2016-09.
• Results first posted 2017-07-26.
• 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

NCT01737762 is a completed, randomized, quadruple-masked, parallel-group Phase 3 study sponsored by Healthpoint. It compared HP802-247 plus compression therapy with vehicle plus compression therapy for venous leg ulcers larger than 12 cm2 and no larger than 36 cm2. The recorded enrollment is 155, while the brief summary states that at least 250 subjects would participate; the registry record does not explain the difference.

The primary endpoint was complete wound closure during the 16-week treatment period from baseline. Closure was recorded for 17 of 69 participants assigned to HP802-247 and 23 of 70 assigned to vehicle. The unadjusted risk-difference interval includes no difference, and the unadjusted p-value is 0.285. The secondary endpoint was time in days to closure; its posted mean-difference interval also includes no difference. The registry record does not report the original sample-size justification, missing-data methods, analysis populations, or multiplicity strategy.