Efficacy, Safety and Economic Benefits of Topical Wound Oxygen Therapy in the Treatment of Chronic Diabetic Foot Ulcers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety and Economic Benefits of Topical Wound Oxygen Therapy in the Treatment of Chronic Diabetic Foot Ulcers (NCT02326337), a randomized na study. The primary outcome is Wound Closure Within 12 Weeks With the Use of Topical Wound Oxygen Therapy (TWO2).

2. Clinical Question

3. Trial Design

This was a prospective, randomized, placebo-controlled trial described in its official title as multi-national and multi-center. The registry record identifies a parallel-group model and quadruple masking; the official title also calls the trial double blinded. The registry does not identify which specific roles were masked, so the masking label alone does not establish who knew each participant’s assignment.

The intervention was topical wound oxygen therapy delivered by the TWO2 device. The placebo device was described as not supplying cyclical oxygen pressure. Both groups were to use AMWT dressings and a standardized off-loading device. Participants first completed a 2 week run-in period with standardized care, and randomization followed eligibility confirmation. The record says half the subjects would use each device.

The registry lists 73 enrolled participants: 36 in the TWO2 group and 37 in the placebo group. The primary endpoint was complete closure within 12 weeks. The record lists a completed study and gives the primary completion date as 2018-02-05. It also lists secondary outcomes covering ulcer area, recurrence, amputation events, adverse events, quality of life, economic analysis, and time to closure. Results are posted for two secondary outcomes, while further outcome details are not reported in the registry record.

Further information about the randomization procedure, allocation concealment, sites, countries, participant flow, adherence, and analysis populations is not reported in the registry record. The trial’s own sample-size justification and original design assumptions are also 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: Patients with diabetic foot ulcers

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 Within 12 Weeks With the Use of Topical Wound Oxygen Therapy (TWO2), measured over 12 weeks.

The primary endpoint counts participants whose wounds achieved complete closure within 12 weeks. The registry defines complete closure as 100% skin re-epithelialization without dressing requirements, confirmed at 2 consecutive study visits 2 weeks apart. This is a binary outcome for each participant: the wound either met the stated closure definition within the specified timeframe or it did not.

A closure endpoint gives a clinically interpretable summary of whether healing reached a defined state, rather than measuring only a change in wound size. Requiring confirmation at consecutive visits makes the endpoint more specific than a single observation of closure. Those are general reasons such endpoints are used; they do not establish how the endpoint was selected for this trial. The protocol rationale for choosing this outcome is not reported in the registry record.

The posted count is 15 participants with closure among 36 assigned to the TWO2 device and 5 among 37 assigned to placebo. The comparison therefore describes the proportion reaching the specified endpoint in each group. It does not by itself describe the timing of closure for every participant, ulcer recurrence after closure, or changes in wound area. Those are distinct outcomes listed separately in the registry record.

7. Results Posted in the Registry

• Topical Wound Oxygen Device: 41.7% (15/36) versus 13.5% (5/37) on control; risk difference 28.2 percentage points (95% CI 8.6 to 47.7), risk ratio 3.08 (1.25–7.60); unadjusted two-proportion z-test p = 0.007.

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.

Absolute Change in Ulcer Area

• 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:
  • Topical Wound Oxygen Device: mean 1.97 versus 0.40 on control; difference 1.57 (95% CI 0.88 to 2.26), standardized effect d = 1.05; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Topical Wound Oxygen Device than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time to Complete Wound Closure in Weeks

• 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:
  • Topical Wound Oxygen Device: mean 8.20 versus 6.30 on control; difference 1.90 (95% CI 0.41 to 3.39), standardized effect d = 0.58; z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Topical Wound Oxygen Device than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists several secondary domains, including ulcer area, wound-closure timing, recurrence, amputation events, adverse events, quality of life, and economic analysis. Numerical results are posted for absolute change in ulcer area and mean time to complete wound closure. The other listed secondary outcomes do not have numerical results described in the posted summaries, so their results are not reported in the registry record.

The two available secondary comparisons do not all represent the same construct as the primary endpoint. Ulcer-area change concerns wound size, whereas the primary outcome is whether complete closure was achieved by a specified time. The mean time-to-closure outcome concerns timing, but its summary does not show whether it was calculated only among participants with closure or how participants without closure were handled. The registry record does not report those details. These outcomes can inform related questions, but they do not replace the primary endpoint.

The numerical secondary findings should be read as exploratory context rather than as independent confirmation of the primary result. Their p values are unadjusted, and the registry does not report a multiplicity plan. When multiple outcomes are examined, the chance of at least one apparently notable result can increase; adjustment or a prespecified hierarchy can address that concern, but neither is documented in the record. The registry also lists no reported analyses, leaving no posted detail about adjusted comparisons or the role of each secondary outcome.

Accordingly, the overall secondary evidence is incomplete in the registry record: two outcomes have numerical summaries, while several other outcome areas are named without results. This limits any broad conclusion about consistency across wound healing, safety, patient experience, and economic outcomes. No conclusion about the unreported outcomes can be drawn from their inclusion in the registry list alone.

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

• Absolute Change in Ulcer Area
• Ulcer Recurrence
• Number of Amputation Events
• Incidence of Adverse Events
• Quality of Life Assessment
• Economic Analysis
• Time to Complete Wound Closure in Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison measure?

The primary outcome is a count of participants who met the wound-closure definition within 12 weeks. For this kind of binary outcome, each group’s count can be expressed as a proportion of its participants. The posted proportions are 0.417 for the TWO2 group and 0.135 for placebo. The risk difference subtracts one group’s proportion from the other; the posted difference is 0.281. In this comparison, positive values correspond to a greater observed proportion in the TWO2 group.

A risk ratio expresses the proportion in one group relative to the proportion in the comparison group. The posted risk ratio is 3.083. An odds ratio instead compares the odds of the outcome across groups; the posted odds ratio is 4.571. Both are relative measures, and neither should be interpreted as a percentage-point difference. For outcomes that are not rare, an odds ratio can differ notably from a risk ratio. The registry reports both measures, but the risk difference is often easier to translate into an absolute group contrast.

How should the p value be read?

The posted primary p value is 0.007 and is labeled unadjusted. In general, a p value describes how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it indicate the size or clinical importance of an effect. The specific test and its assumptions are not reported in the registry record. Because no reported analyses are listed, further details about the sponsor’s statistical analysis are not available in this record.

What do the intervals contribute?

An interval around an estimate conveys its uncertainty: narrower intervals indicate greater precision under the method used, while wider intervals indicate less precision. The risk-difference interval runs from 0.086 to 0.477; the confidence level and the method used to calculate the interval are not reported in the registry record. The risk-ratio and odds-ratio intervals are also posted, but their methods and confidence level are not specified. General interpretation should therefore distinguish the numerical intervals from unreported details of how they were constructed.

How do the continuous outcomes differ?

For absolute change in ulcer area and time to complete wound closure, the registry reports group means and standard deviations, along with unadjusted mean differences. A mean summarizes the average value, while a standard deviation describes the spread of individual values around that mean. The mean difference compares group averages. Its sign depends on the order of subtraction and on how the outcome is coded; the record does not explain the sign convention for absolute ulcer-area change. A mean time is also not the same as a time-to-event analysis that accounts for participants who have not experienced the event by the end of follow-up.

The ulcer-area comparison reports means of 1.97 cm2 and 0.4 cm2, and a mean difference of 1.57 with an interval from 0.877 to 2.263. Its unadjusted p value is < 0.001. The closure-time comparison reports means of 8.2 and 6.3 weeks, and a mean difference of 1.9 with an interval from 0.411 to 3.389. Its unadjusted p value is 0.012. The record provides standard deviations for both groups, but does not report the precise analysis population or the handling of missing values for these outcomes.

General caution is needed when reading mean comparisons: the mean can be affected by skewed data or extreme observations. The posted summaries do not show individual-level distributions, so those features cannot be assessed from the registry record. Nor does the posted mean difference alone explain the clinical meaning of the direction of change when the outcome’s coding convention is not stated.

What do the planning calculations represent?

The sample-size illustrations use the observed effect and specify a two-sided significance level of 0.05, equal allocation, and a normal approximation. They consider effects set to 100%, 75%, and 50% of the observed effect. These are planning calculations, not the trial’s original design justification, which is not reported in the registry record. The calculations illustrate how a future study’s required group size changes under those assumptions. General statistical planning depends on assumptions about the target effect and analysis; changing those assumptions changes the resulting sample-size estimate.

The posted comparisons are simple unadjusted re-calculations from summary statistics. The registry discrepancy indicator is false. The record does not list sponsor-reported analyses, so there is no posted sponsor analysis to compare with these estimates. The calculations do not substitute for a full analysis plan or participant-level analysis.

11. Confidence Intervals and Precision

The primary risk difference is 0.281, with a reported interval from 0.086 to 0.477. This interval indicates uncertainty about the magnitude of the group contrast: values across a noticeable range remain compatible with the estimate under the interval method. Its lower endpoint is above zero, but the interval is not so narrow that the size of the difference is precisely pinned down. The confidence level and interval method are not reported in the registry record.

The relative measures are also imprecise. The risk ratio is 3.083, with an interval from 1.251 to 7.6; the odds ratio is 4.571, with an interval from 1.444 to 14.47. The breadth of these intervals means that the relative size of the group contrast remains uncertain. Relative measures can look more pronounced than absolute differences, so both scales are useful for understanding the posted result.

Only 73 participants were enrolled, with 36 in the TWO2 group and 37 in the placebo group. With a limited number of observations, estimates can be sensitive to the outcomes of a relatively small number of participants. This is a general precision consideration, not evidence that the posted results are incorrect.

The available intervals support a range of plausible effect sizes rather than a single exact effect. Their interpretation is also constrained by the absence of reported details about the interval calculation, missing-data handling, and analysis population. The reported p value addresses compatibility with a null model under an analysis, but it does not remove the uncertainty reflected in the intervals or resolve those reporting gaps.

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. They are not total event counts. For the primary binary outcome and the posted continuous outcomes, the registry’s planning description gives participant counts per arm. The record’s general note says time-to-event tables would instead give total events using the Schoenfeld method, but the posted time-to-closure outcome is presented as a mean comparison, not as that type of event-total calculation.

In plain language, 80% power describes a planning target under which a study would have an 80% chance of detecting the specified effect at the stated significance level if that effect were the true one and the assumptions held. The 90% column uses a higher target chance of detection under the same kind of planning framework. These are design concepts, not guarantees about a future result.

The listed calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set in turn to 100%, 75%, or 50% of the observed effect. Smaller effects require more participants per arm in the listed illustrations. The assumptions used in the trial’s original design and its own sample-size justification are not reported in the registry record. This is not observed power: it is a planning illustration based on the observed effect, not a retrospective measure of how well the completed trial could detect an effect.

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 = 0.135; treatment proportion p₁ = 0.417; average p̄ = 0.276.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6321 = 1.2389.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5999 = 0.5049.
4. n = (1.2389 + 0.5049)² / (0.2815)² = 38.4, rounded up to 39 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 <- 0.135135135135135                          # control proportion
p1 <- 0.416666666666667                          # 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(2326337)
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 = 39 (80% power), 51 (90% power)
 75% of observed effect: n per arm = 64 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 129 (80% power), 172 (90% power)
power.prop.test: 38.4 
Simulated power at n = 39 per arm: 0.825 (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

Multiplicity arises when a study evaluates more than one endpoint, comparison, subgroup, or time point. If each is tested separately without adjustment, the chance of at least one result appearing statistically notable can rise. This is a general statistical concern. The registry lists one primary endpoint and multiple secondary outcomes, but a prespecified hierarchy, multiplicity adjustment, or other control strategy is not reported in the registry record. The posted secondary p values are unadjusted.

The registry record lists no reported analyses. It therefore does not describe whether additional outcomes, subgroups, adjusted models, or interim analyses were planned or conducted. Interim analyses and stopping rules are not reported in the registry record; their absence from the record should not be taken as evidence that they did or did not occur.

Missing-data handling is also not reported. The record does not state how participants with missing 12-week assessments were classified, whether observations were imputed, or whether a sensitivity analysis was conducted. It does not identify the primary analysis population, such as whether the posted counts include all randomized participants or only those with available endpoint assessments. The enrollment and arm counts alone do not resolve these questions.

These omissions matter because outcome availability and analysis choices can affect an estimate. For example, a binary endpoint needs a stated approach for participants whose closure status is unknown; continuous outcomes need a stated approach for missing measurements. This is a general explanation of why missing-data methods matter, not a claim about what happened in this trial. Without those details, the posted results can be described, but their robustness to alternative handling of missing data cannot be evaluated from the registry record.

The registry also does not report the statistical analysis plan, the trial’s original sample-size justification, or the procedures used to implement masking and randomization. These are distinct reporting gaps and should not be filled by assumptions based on the trial’s title or design labels.

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: osteomyelitis (13.5%), wound infection (8.3%), urinary tract infection (5.6%), cardiovascular event (2.8%), utc grade ii ulceration (2.8%).

The registry reports serious adverse events in 6 of 36 participants at risk in the TWO2 group and 7 of 37 participants at risk in the placebo group. It reports other adverse events in 6 of 36 and 7 of 37, respectively. Deaths are listed as 2 in each group. These are counts in the registry record; they do not by themselves establish whether an event was caused by a device or by another factor.

The record lists Osteomyelitis (13.5%), Wound Infection (8.3%), Urinary Tract Infection (5.6%), Cardiovascular Event (2.8%), UTC Grade II Ulceration (2.8%), and Pneumonia (2.8%) among the serious-event terms. The record does not specify an arm for these term percentages in the posted information, so they should not be assigned to either group based on the overall group counts.

These summaries do not provide event timing, recurrence, severity detail beyond the serious-event classification, or a causal assessment. The registry record does not report those details. Group counts can describe what was recorded, but the available information is not enough to characterize individual risk or establish a treatment-related safety effect.

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

The primary result describes a greater observed proportion of participants meeting the registry’s wound-closure definition in the TWO2 group than in the placebo group. The estimate is based on 15 closures among 36 participants compared with 5 among 37. The risk difference and relative measures quantify that observed contrast, while their intervals indicate uncertainty about its size.

The result does not mean that every participant in the TWO2 group experienced closure, or that a particular participant’s outcome can be predicted from the group average. It also does not establish what would happen in a different population, care setting, or follow-up period. The randomized, masked, placebo-controlled design is relevant to comparative interpretation, but the registry record does not contain every detail needed to assess implementation and analysis.

The primary endpoint is a defined outcome at 12 weeks, not a complete account of healing over time. Separate outcomes address ulcer-area change and time to closure, while recurrence, amputation events, quality of life, and economic analysis are also listed. Results for some of these domains are not reported in the registry record. The primary result therefore should not be treated as a summary of every benefit, risk, or patient experience measured in the study.

The posted p value does not quantify the probability that the result is true, and statistical evidence does not by itself determine clinical importance. The intervals show that the estimated contrast is uncertain even though the reported risk-difference interval lies above zero. The interpretation is further limited by unreported analysis-population and missing-data methods, and by the absence of a reported multiplicity plan.

In short, the registry records a group difference on its stated primary endpoint. It does not, on its own, settle questions about the size and reliability of that difference, unreported secondary outcomes, or the broader implications of the treatment comparison.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares a defined wound-closure outcome between randomized device and placebo groups, with masking reported in the registry. Its endpoint has a specific threshold and confirmation rule, making the result interpretable as a count of participants who reached a stated closure condition within the follow-up window.

The example also shows why effect measures should be read on both absolute and relative scales. The risk difference describes the group contrast in proportions, while the risk ratio and odds ratio express relative contrasts. Their estimates and intervals tell related but different parts of the statistical story. Reporting the counts alongside the estimates helps readers see the scale of the underlying data.

Precision remains important. The posted interval for the risk difference spans a range of possible magnitudes, and the relative-effect intervals are broad. A p value alone would not convey that uncertainty. The small overall enrollment also makes transparent reporting of the analysis population, missing outcomes, and methods particularly useful for assessing how much confidence to place in the estimate.

The record illustrates the distinction between a trial’s design assumptions and retrospective planning illustrations. The listed planning calculations apply stated assumptions to observed effects; they do not document how the completed trial was originally sized. It also demonstrates why secondary outcomes and multiplicity matter: related outcomes may provide context, but unadjusted analyses across several outcomes carry less weight than a clearly specified primary analysis.

Finally, transparent registry reporting supports careful interpretation without turning a statistical result into a blanket treatment conclusion. The posted data describe a particular trial comparison and leave several analytic and outcome-reporting questions unresolved.

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.

Several trial-specific limitations in the registry record constrain interpretation. Although the study is described as multi-national and multi-center, the countries, sites, and distribution of participants are not reported in the registry record. Baseline characteristics and details of ulcer severity or duration are also not reported, limiting assessment of how similar the groups were on clinically relevant features.

The record gives arm counts and outcome summaries but does not describe participant flow, withdrawals, adherence to device use, or use of other care during follow-up. It does not state whether every enrolled participant contributed to each outcome. Missing-data methods, the primary analysis population, and sensitivity analyses are not reported in the registry record. These details would help readers assess the extent to which incomplete follow-up could affect the comparisons.

The endpoint definition is described, but the record does not report how closure assessments were adjudicated or whether assessors remained masked. It also does not provide the statistical analysis plan, interval methods, or the confidence level associated with the reported intervals. The trial’s own sample-size justification and its original design assumptions are not reported in the registry record.

Secondary results are incomplete: numerical summaries are posted for two outcomes, while other listed secondary domains have no results in the posted summaries. The treatment of multiple outcomes is not described, and the available secondary p values are unadjusted. Safety summaries provide counts but not event timing, causality assessment, or arm-specific attribution for the listed serious-event term percentages. These limitations relate to reporting available in the registry and do not establish that any particular procedure was absent from the conduct of the trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy, Safety and Economic Benefits of Topical Wound Oxygen Therapy in the Treatment of Chronic Diabetic Foot Ulcers — NCT02326337.
• Registry record last updated 2025-10-27; status last verified 2025-10.
• Results first posted 2025-04-20.
• 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

The registry record describes a completed, randomized, parallel-group, placebo-controlled trial of topical wound oxygen therapy for chronic diabetic foot ulcers. It lists 73 participants, with 36 assigned to the TWO2 device and 37 to the placebo device. Participants used standardized off-loading and AMWT dressings after a 2 week run-in period.

The primary endpoint was complete wound closure within 12 weeks, defined as 100% skin re-epithelialization without dressing requirements and confirmation at 2 consecutive study visits 2 weeks apart. The record reports 15 participants meeting this endpoint in the TWO2 group and 5 in the placebo group, with an unadjusted risk difference of 0.281 and a reported interval from 0.086 to 0.477.

Two secondary outcomes have numerical results in the posted summaries. Other listed outcomes, analysis details, missing-data methods, and the trial’s original sample-size justification are not reported in the registry record.