Cooling Leg and Foot Ulcer Skin Post Healing to Prevent Ulcer Recurrence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cooling Leg and Foot Ulcer Skin Post Healing to Prevent Ulcer Recurrence (NCT02626156), a randomized phase 2 study. The primary outcome is Number of Participants With Ulcer Recurrence.

2. Clinical Question

The study also set out to measure pain, physical activity, quality of life, adherence, and participants’ responses to study instructions and procedures. The primary recurrence result is a count of participants with an event, not a measure of time until recurrence. The record does not report a separate primary question about how quickly recurrence occurred.

3. Trial Design

MUSTCOOL is identified in the registry as a phase 2, randomized, double-masked, parallel-group study. The sponsor was the Medical University of South Carolina, and the record marks the study as completed. It lists enrollment of 140 participants and a final completion of 117 individuals (84%) in the primary outcome description. The reason that the final completion count differs from the enrollment figure is not reported in the registry record.

The four reported outcome groups combine pack assignment with ulcer category: cooling gel pack for venous leg ulcer, cooling cotton pack for venous leg ulcer, cooling gel pack for diabetic foot ulcer, and cotton cooling pack for diabetic foot ulcer. In the primary outcome description, the randomized groups are also characterized as placebo control and intervention, with venous leg ulcer and diabetic foot ulcer counts shown within each. The arm titles and descriptions identify the packs as gel and cotton; the record does not explain the precise relationship between those labels and the placebo-control wording.

The intervention was intended for home use. Participants were to monitor affected-skin temperature daily and apply the assigned pack preventively three times a week. The summary describes additional cooling for 5 consecutive days when temperature became elevated. The arm descriptions are truncated in the registry record, so further operational details cannot be recovered from them.

The primary outcome was assessed through study completion at 6 months from baseline. The record lists 10 outcome measures and 3 secondary outcomes, including adherence, ease or acceptability of study activities, and knowledge of study instructions. It does not report the original design’s sample-size justification, the randomization procedure, or further details of masking. The number and timing of interim analyses are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 246 individuals approached, 211 prescreened eligible, 71 ineligible due to type of wound, could not make regular appointments for study visits, not interested in study, lost contact or developed infection or ulcer changed in size (healed or enlarged indicating deterioration prior to eligibility screening visit); 140 were enrolled - 58 in the DFU group (29 intervention and 29 control)and 82 in VLU group (42 intervention and 40 control)

Baseline (Visit 1 to Visit 2)

Study Visit 3

Study Visit 4

Analysis population for the primary outcome, as defined in the registry: A total of 140 participants were randomized to either the placebo control group (n=57; 34 VLU, 23 DFU) or the intervention (n=60; 35 VLU, 25 DFU), with a final completion of 117 individuals (84%)

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 Number of Participants With Ulcer Recurrence, measured over Through study completion at 6 months from baseline.

The primary endpoint is the number of participants with ulcer recurrence through study completion at 6 months from baseline. The registry describes the event as a recurrent ulcer developing during the study period among participants with a previously healed venous leg ulcer or diabetic foot ulcer. The outcome is therefore a binary participant-level event: a participant either had a recurrence during the stated period or did not.

This endpoint is used because recurrence is the prevention outcome the intervention was designed to address. A count of participants with recurrence can be compared between pack groups within each ulcer category. The registry also reports risk differences, which express the difference between the event proportions in two groups. A risk difference is measured on an absolute scale and is distinct from a relative comparison such as a risk ratio.

The endpoint does not describe the number of separate recurrent ulcers per participant, the severity of recurrence, or the time from healing to recurrence. Although the study summary mentions outcomes such as pain, physical activity, and quality of life, the registry record’s primary endpoint is recurrence. The event definitions, rules for handling multiple recurrences, and detailed ascertainment procedures are not reported in the registry record.

7. Results Posted in the Registry

• Cooling Cotton Pack - Venous Leg Ulcer: 8.8% (3/34) versus 17.1% (6/35) on control; risk difference -8.3 percentage points (95% CI -24.0 to 7.4), risk ratio 0.51 (0.14–1.89); unadjusted two-proportion z-test p = 0.305.
• Cooling Gel Pack - Diabetic Foot Ulcer: 44.0% (11/25) versus 17.1% (6/35) on control; risk difference 26.9 percentage points (95% CI 3.7 to 50.0), risk ratio 2.57 (1.09–6.02); unadjusted two-proportion z-test p = 0.023.
• Cotton Cooling Pack - Diabetic Foot Ulcer: 21.7% (5/23) versus 17.1% (6/35) on control; risk difference 4.6 percentage points (95% CI -16.4 to 25.6), risk ratio 1.27 (0.44–3.67); unadjusted two-proportion z-test p = 0.662.

8. Statistical Interpretation

9. Statistical Methods Explained

The endpoint is binary at the participant level: recurrence is recorded as an event, and the analysis compares event proportions. For two groups, a risk difference subtracts one group’s event proportion from the other’s. A negative estimate means the first group named in the comparison has a lower observed proportion than its reference group; a positive estimate means a higher observed proportion. The order of the comparison matters, so each estimate must be read together with the stated group labels.

What does a confidence interval express?

A confidence interval describes uncertainty around an estimate under the assumptions of the statistical method. A narrow interval indicates greater precision than a wide interval, while a wide interval leaves a broader range of effects compatible with the data. For a risk difference, zero represents no difference between the compared event proportions. An interval that includes zero is compatible with no difference as well as with effects in either direction covered by the interval. This does not prove that the true difference is zero.

The recalculated intervals in the posted results are simple, unadjusted estimates from the posted summary statistics. They should not be confused with a fully adjusted analysis or with the sponsor’s analysis. The registry’s sponsor analysis uses a chi-squared method and reports a risk difference across the four groups. The record does not provide enough detail to reconstruct its full model or determine whether it accounts for any design features beyond the listed groups.

How should p-values be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the magnitude of an effect. The recalculated p-values are explicitly unadjusted. The registry reports the sponsor’s p-value separately. Since the sponsor analysis and simple pairwise recalculations address different comparisons, their p-values should not be treated as competing tests of one identical question.

The 0.05 threshold is part of the stated assumptions for the planning illustrations, but the registry does not report that this was the threshold for the trial’s own analysis. The original statistical analysis plan and its significance threshold are not reported in the registry record. It is therefore inappropriate to infer a prespecified testing strategy from the recalculated results or the planning assumptions.

Why does the comparison structure matter?

The outcome data are arranged across four groups defined by both ulcer category and pack. The designated reference group in the recalculations is the venous leg ulcer gel-pack group. Consequently, estimates against that reference are not necessarily the direct gel-versus-cotton contrast within the same ulcer category. For example, an estimate involving a diabetic foot ulcer group and the venous leg ulcer reference changes both pack assignment and ulcer category. It cannot isolate a pack contrast within diabetic foot ulcer participants.

The sponsor’s reported analysis combines all four groups and reports a single risk difference. Its exact interpretation and coding are not fully described in the record. A single aggregate result can answer a different question from within-category comparisons, particularly if the group composition or event risks differ by ulcer category. The registry record does not report an interaction test or enough methodological detail to establish whether a common pack effect across the two conditions was assessed.

Why can over-dispersion matter?

For general statistical context, over-dispersion means that observed variability is greater than a model assumes. If a method assumes less variability than is present, its uncertainty estimates may be too small and inference may appear more precise than warranted. This concept is relevant to count and clustered data, but the primary outcome is reported as participants with an event, and the registry does not report an over-dispersion assessment. No conclusion about over-dispersion or its handling can be drawn from the record.

What details are missing?

The registry record does not report the exact analysis population for the sponsor’s primary analysis, how missing recurrence outcomes were handled, or whether analyses followed intention-to-treat principles. The record also does not state whether covariate adjustment was used, how any protocol deviations were handled, or whether sensitivity analyses were conducted. The randomization sequence and allocation concealment procedures are not described in the available record. These omissions limit assessment of the assumptions behind the reported analysis.

The listed event counts and recalculated comparisons are useful descriptive summaries, but they do not substitute for a complete analysis plan. In particular, the record does not report a multiplicity strategy for the several pack and ulcer-category comparisons, or how the secondary outcomes were incorporated into inference. The sponsor’s analysis should remain the primary reference for the sponsor-reported overall result, while recalculations should be understood as unadjusted explorations of the posted summaries.

10. Confidence Intervals and Precision

Precision is best judged from the confidence intervals alongside the point estimates. For the venous leg ulcer comparison of cotton pack with the designated gel-pack reference, the recalculated risk difference is -0.083, and its confidence interval runs from -0.240 to 0.074. This interval covers zero and spans effects in both directions. It therefore leaves substantial uncertainty about the direction and size of the risk difference.

For the diabetic foot ulcer gel-pack group compared with the designated reference, the recalculated estimate is 0.269, with a confidence interval from 0.037 to 0.500. This interval does not include zero, but its width still indicates uncertainty about the size of the difference. The comparison also changes ulcer category relative to the reference, so it is not an isolated within-diabetic-foot-ulcer pack contrast. The diabetic foot ulcer cotton-pack comparison against that reference has an estimate of 0.046 and an interval from -0.164 to 0.256; the interval includes zero and allows a range of directions.

The sponsor-reported estimate is 0.13, with a 95% confidence interval from -0.02 to 0.3. That interval includes zero. The sponsor’s analysis is the relevant reported overall analysis, and the discrepancy flag means the sponsor’s own analysis takes precedence over simple recalculations. The different comparisons should not be combined as if they estimated the same quantity.

Confidence intervals do not correct for unreported issues such as missing outcomes, multiplicity, or analysis-population choices. The registry record does not report whether the intervals were adjusted for multiple comparisons. Thus, the intervals communicate sampling uncertainty under their respective methods, not every source of uncertainty in the study.

11. Planning a Similar Trial: Sample Size

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

The planning figures are expressed as participants per arm for the binary recurrence outcome; they are not total event counts. They are illustrative calculations based on the observed effect, not the trial’s original design assumptions. The stated planning 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 to the stated fraction of the observed effect. The original trial design’s sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a design that would have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities calculated for hypothetical future studies; they do not describe the probability that the completed study found an effect or the chance that its result is correct.

Each planning row uses a different fraction of the observed effect. Planning for 100% of the observed effect uses the full observed estimate; planning for 75% or 50% assumes a smaller effect to detect. Smaller effects need more participants because they are harder to distinguish from random variation. The figures can therefore rise sharply as the assumed effect becomes smaller.

The estimates depend on the observed effect, which may itself be uncertain, and the assumptions may not match a future study. The registry record does not report the trial’s original sample-size justification or whether its initial design used these assumptions. These figures are planning illustrations, not observed power.

12. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.171; treatment proportion p₁ = 0.088; average p̄ = 0.130.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4753 = 0.9317.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4717 = 0.3970.
4. n = (0.9317 + 0.3970)² / (-0.0832)² = 255.1, rounded up to 256 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 <- 0.171428571428571                          # control proportion
p1 <- 0.0882352941176471                          # 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(2626156)
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 = 256 (80% power), 341 (90% power)
 75% of observed effect: n per arm = 485 (80% power), 649 (90% power)
 50% of observed effect: n per arm = 1,160 (80% power), 1,552 (90% power)
power.prop.test: 255.1 
Simulated power at n = 256 per arm: 0.808 (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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s own primary analysis as a chi-squared analysis across the four listed groups, with risk difference 0.13, 95% confidence interval -0.02 to 0.3, and p-value 0.091. The interval includes zero. The record also flags a discrepancy between the sponsor-reported analysis and the simple recalculations from the posted group summaries. Under that circumstance, the sponsor’s own analysis takes precedence.

The recalculations are unadjusted comparisons based on the posted summary statistics and a designated reference group. They are not a reconstruction of the sponsor’s full analysis. The reported overall result and the recalculated pairwise estimates have different comparison structures, so differences between their estimates or p-values do not by themselves identify an error or explain the discrepancy. The registry record does not provide enough detail to determine the precise source of the difference.

The sponsor’s result should be interpreted according to its stated four-group scope, rather than as a direct pack comparison within each ulcer category. The record does not describe enough of the analysis to clarify how the overall risk difference was defined. Accordingly, the unadjusted recalculations are best treated as descriptive checks, not as replacements for the reported sponsor analysis.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple groups, a primary recurrence outcome, and secondary outcomes concerning adherence, study instructions, thermometer use, logs, treatment performance, helpfulness, and knowledge. Several group contrasts can be considered, and additional outcomes create further opportunities for statistical testing. When many hypotheses are tested, the chance of at least one apparently notable result can increase unless the analysis accounts for multiplicity.

The registry record does not report a multiplicity adjustment or a prespecified hierarchy for the comparisons. It does not state whether the sponsor’s analysis was the sole primary test or how the several group combinations were handled. The recalculated p-values are unadjusted and should not be read as multiplicity-controlled evidence. The record also does not report whether any secondary outcome analyses were intended to be confirmatory or exploratory.

Missing-data handling is also not described in sufficient detail. The primary outcome description reports 140 randomized participants and a final completion of 117 individuals (84%), but does not explain the availability of recurrence outcomes for each group or how participants without a completed assessment were treated. It does not report imputation, censoring rules, or a sensitivity analysis for missing recurrence data. Completion status alone cannot establish which participants were included in a particular analysis.

The analysis population is not reported in the registry record. It is not stated whether the primary analysis followed intention-to-treat principles, included only participants with outcome data, or used another population definition. The record does not report how protocol deviations, withdrawals, or participants who did not follow the pack schedule were handled in the efficacy analysis.

These omissions matter because analysis choices can affect both the estimate and its uncertainty. They do not show that a particular approach was used or that the reported result is invalid. They mean that the posted record does not permit a full assessment of multiplicity control, missing-data assumptions, or alignment between the randomized groups and the analyzed 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: amputation (6.9%), heart attack or failure (4.8%), shortness of breath (4.8%), stroke (3.4%), infection (3.4%).

The registry reports serious adverse events and other adverse events separately for the four outcome groups. For serious adverse events, the record lists 4 affected participants among 42 at risk in the venous leg ulcer gel-pack group, 2 among 40 at risk in the venous leg ulcer cotton-pack group, 3 among 29 at risk in the diabetic foot ulcer gel-pack group, and 4 among 29 at risk in the diabetic foot ulcer cotton-pack group. The listed deaths are 1, 0, 0, and 0, respectively.

These figures are group-level counts, not a comparison adjusted for differences in participant characteristics or follow-up. The registry record does not explain why the serious-event at-risk counts differ from the primary outcome group counts, so they should not be assumed to use the same analysis population. The listed serious-event terms include amputation, heart attack or failure, shortness of breath, stroke, infection, and fainting; the record gives percentages for these terms but does not provide enough detail to interpret them as risks for a specific pack group.

Serious adverse events are distinct from the primary recurrence outcome. These counts do not establish that a pack caused an event or that groups had comparable safety experience. The registry record does not report event timing, relatedness assessments, or a statistical comparison of safety outcomes.

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

The registry record describes recurrence counts for participants assigned to cooling gel packs or cooling cotton packs, with results divided between venous leg ulcers and diabetic foot ulcers. The sponsor’s reported analysis across the four groups gives a risk difference of 0.13, a 95% confidence interval from -0.02 to 0.3, and a p-value of 0.091. Its confidence interval includes zero, and the sponsor analysis is the primary reported result to use in preference to the recalculated summaries because the record flags a discrepancy.

The recalculated estimates offer additional descriptive views, but their comparisons use the designated venous leg ulcer gel-pack reference. They are not all direct comparisons of gel versus cotton within the same ulcer category. One recalculated interval excludes zero, while the other listed pairwise intervals include zero; that pattern does not establish a uniform effect across the two ulcer categories. The record does not report an interaction analysis that would test whether the pack comparison differs by ulcer category.

These results do not establish that either pack prevents recurrence, nor do they establish that the packs are equivalent. A lack of a clear difference in a given comparison can reflect uncertainty as well as a small underlying difference. The observed counts and confidence intervals should be interpreted together, and the limitations in analysis details, missing-data reporting, and multiplicity information remain relevant.

The findings apply to the particular study population and follow-up described in the registry. The primary outcome covers recurrence through 6 months from baseline, not long-term recurrence or time to recurrence. The registry also lists outcomes such as pain, activity, quality of life, and adherence, but the primary result is the recurrence endpoint. No clinical recommendation follows from these statistical summaries alone.

17. Why This Trial Matters Statistically

This trial raises several important statistical issues in a compact prevention study. First, the outcome is binary, but the clinical groups are defined by both ulcer category and pack assignment. The distinction matters: comparisons that change both ulcer category and pack cannot isolate the effect of pack choice. Clear labeling of the contrast is essential before interpreting a risk difference.

Second, the event counts are limited, and the confidence intervals are correspondingly important. A point estimate alone can suggest a strong direction while concealing substantial uncertainty. The interval for a risk difference helps show which values remain compatible with the data, including whether no difference is also plausible.

Third, the record presents a sponsor analysis that differs from simple recalculations. This illustrates why a reproducible, well-described statistical analysis plan matters. A headline estimate cannot be fully evaluated without knowing the comparison definition, analysis population, treatment of missing outcomes, and whether multiple comparisons were anticipated. The sponsor-reported result should take precedence, but the registry does not supply enough detail to explain the discrepancy.

Finally, sample-size planning depends on the effect a future study aims to detect. Planning around the full observed effect can produce different requirements than planning for a smaller effect, and an observed estimate is uncertain. The planning illustrations are not evidence of the completed study’s power. Together, these points show why transparent methods and uncertainty reporting are central to interpreting a clinical trial.

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 important trial-specific details unreported. It does not describe the randomization sequence or allocation concealment, and its masking field alone does not explain who was masked or how masking was maintained. The intervention arm descriptions are truncated, limiting interpretation of the full application procedures. The summary outlines daily temperature monitoring, preventive pack use three times weekly, and additional cooling for 5 consecutive days if temperature became elevated, but detailed adherence rules are not available.

The primary outcome description reports group counts and a completion figure, but does not specify how recurrence was defined and verified, how multiple recurrences were handled, or how missing outcome data were treated. The registry record does not identify the primary analysis population. The difference between the efficacy group counts and the serious-event at-risk counts is not explained, so the populations behind those summaries should not be presumed identical.

The sponsor’s reported result covers all four groups, while recalculated estimates use the designated reference group. The exact sponsor contrast is not sufficiently described to reconcile the discrepancy. The record also does not report an interaction analysis that could clarify whether pack comparisons differ between venous leg ulcer and diabetic foot ulcer participants.

Multiplicity adjustment, the original sample-size justification, interim analyses, and detailed statistical-plan specifications are not reported in the registry record. The posted results therefore do not establish how the study’s design handled multiple outcomes or comparisons. These limitations constrain interpretation of the statistical evidence; they do not, on their own, determine the direction of any treatment effect.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Cooling Leg and Foot Ulcer Skin Post Healing to Prevent Ulcer Recurrence — NCT02626156.
• Registry record last updated 2021-06-30; status last verified 2021-06.
• Results first posted 2021-06-29.
• 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

MUSTCOOL is a completed, phase 2, randomized, double-masked, parallel-group study sponsored by the Medical University of South Carolina. The registry lists enrollment of 140 participants and describes a home-based cooling and self-monitoring intervention for people with recently healed venous leg or diabetic foot ulcers. The primary outcome is the number of participants with ulcer recurrence through 6 months from baseline.

The sponsor-reported analysis across four groups gives a risk difference of 0.13, a 95% confidence interval from -0.02 to 0.3, and a p-value of 0.091. The registry flags a discrepancy with simple recalculations, so the sponsor’s analysis takes precedence. The record does not report sufficient detail about the analysis population, missing data, or multiplicity to resolve all interpretive questions.