A Safety and Efficacy Study of INTEGRA® Dermal Regeneration Template for the Treatment of Diabetic Foot Ulcers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety and Efficacy Study of INTEGRA® Dermal Regeneration Template for the Treatment of Diabetic Foot Ulcers (NCT01060670), a randomized na study. The primary outcome is Incidence of Complete Wound Closure.

2. Clinical Question

3. Trial Design

This was a randomized, controlled, parallel-group clinical trial with no masking. Its official title describes a multi-center study evaluating the safety and effectiveness of INTEGRA® Dermal Regeneration Template for neuropathic diabetic foot ulcers. The registry lists the phase as NA and the status as completed. Enrollment is recorded as 545. The study start is listed as 2010-04 and primary completion as 2014-06.

The interventions were INTEGRA® Dermal Regeneration Template and conventional wound therapy. The arm descriptions identify the active group as receiving the device and the control group as receiving 0.9% Saline gel. The primary outcome was incidence of complete wound closure at 16 weeks. The registry describes the assessment as 100% closure, judged by the Investigator and confirmed at 2 consecutive treatment phase visits. The primary results are based on the Investigator assessment and ITT population.

The posted primary outcome includes results for 154 participants in the active-treatment group and 153 in the control group. These outcome denominators are not the same thing as the registry’s overall enrollment figure; the record does not explain the relationship between enrollment and the analyzed outcome groups. The registry does not report the trial’s original sample-size assumptions, detailed allocation procedures, or protocol deviations. It also does not report masking, which is recorded as none, or a phase category beyond NA.

Several secondary outcomes are listed, including wound closure, time and rate of closure, ulcer recurrence, and change in Short Form Health Survey (SF-36) quality-of-life metrics. Results are posted for only some of the listed outcomes. The registry record reports no analyses in its analysis listings. That absence does not establish which analyses may have been conducted outside the posted 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: Participants participated in a Run-In phase that must last a minimum of 14 days, but may have been extended up to 17 days to allow for scheduling of the randomization visit.

Run In

Reasons for not completing this period:

Treatment Phase

Follow up Phase

Analysis population for the primary outcome, as defined in the registry: The results were based on the Investigator assessment and ITT population.

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 Incidence of Complete Wound Closure, measured over 16 weeks.

The primary endpoint was incidence of complete wound closure, measured as participants with an event. The registry defines complete closure as 100% closure assessed by the Investigator and confirmed at 2 consecutive treatment phase visits. The timeframe was 16 weeks. The results were based on the Investigator assessment and ITT population.

A binary endpoint records whether each participant met a defined condition by the stated assessment period. It is useful for a clinical question framed as whether complete closure occurred, rather than how much an ulcer changed on a continuous scale. The proportion with closure describes the observed frequency in each group, while a between-group contrast describes how those frequencies differ. The risk difference is an absolute contrast: it expresses the difference between the two group probabilities on the probability scale. Its confidence interval conveys uncertainty around that estimated contrast.

The confirmation requirement is important to the meaning of the endpoint: a single assessment of closure was not sufficient under the registry definition. The outcome is therefore a specific, time-bounded event rather than a general measure of improvement. The record does not report further details about how the endpoint was adjudicated or how assessments were handled when observations were missing. The endpoint alone does not describe other aspects of wound healing, recurrence, quality of life, or safety.

7. Results Posted in the Registry

• Active Treatment: 51.3% (79/154) versus 32.0% (49/153) on control; risk difference 19.3 percentage points (95% CI 8.5 to 30.1), risk ratio 1.60 (1.21–2.11); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Incidence of Complete Wound Closure

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Active Treatment: 50.0% (77/154) versus 30.7% (47/153) on control; risk difference 19.3 percentage points (95% CI 8.5 to 30.0), risk ratio 1.63 (1.22–2.17); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Active Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time to Complete Wound 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:
  • Active Treatment: mean 52.61 versus 69.78 on control; difference -17.17 (95% CI -27.89 to -6.45), standardized effect d = -0.59; z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Active Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Rate of Wound 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:
  • Active Treatment: mean 7.15 versus 4.81 on control; difference 2.34 (95% CI 0.57 to 4.11), standardized effect d = 0.30; z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Active Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary closure question in several directions: they include another incidence measure of complete closure, time to closure, rate of closure, ulcer recurrence, and change in SF-36 quality-of-life metrics. The registry lists six secondary outcomes, but results are posted for only some of them. The overall direction of the posted closure-related comparisons is broadly consistent with the primary comparison. The time and rate measures provide different perspectives on healing than the binary endpoint, so agreement across them can be supportive without making them equivalent measures.

These outcomes should not be treated as independent confirmations of the primary result. They may be related to one another, and they address distinct features of wound outcomes. The registry record does not report a hierarchy or multiplicity adjustment for secondary testing. When several outcomes are examined, unadjusted p-values do not account for the broader set of comparisons and can overstate the strength of evidence if each is read in isolation. For that reason, secondary findings carry less weight than the prespecified primary question unless a clear testing strategy is documented.

The registry’s list includes ulcer recurrence and SF-36 quality-of-life change, but it does not post results for those measures in the record used for this analysis. Their inclusion as planned or listed outcomes should not be mistaken for evidence about their observed values. The record also lists time to complete wound closure twice among the secondary outcomes, while posted results do not provide registry-reported analyses. The available estimates can be described as posted summaries, but the registry does not explain the relationship between the repeated listing and analysis.

Thus, the secondary information adds breadth but has limitations in completeness and inferential context. It can help readers see whether different measurements tell a broadly similar story, while the absence of results for some outcomes and of a reported multiplicity plan argues for caution. The primary endpoint remains the central registered comparison.

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

• Incidence of Complete Wound Closure
• Time to Complete Wound Closure
• Time to Complete Wound Closure
• Rate of Wound Closure
• Incidence of Ulcer Recurrence
• Change in Short Form Health Survey (SF-36) Quality of Life Metrics

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant either met the registry definition of complete wound closure by the stated assessment period or did not. General statistical explanation: a binary outcome can be summarized by the proportion of participants with the event in each group. The primary comparison uses the risk difference, which subtracts the control-group probability from the active-group probability. A risk difference of zero corresponds to equal probabilities on this scale. The posted estimate is 0.193, and its confidence interval extends from 0.085 to 0.301.

What does the risk difference tell us?

The risk difference communicates an absolute contrast in event probabilities. It is often easier to connect to the observed frequency of an event than a relative measure, because its scale is the probability scale itself. Its interpretation depends on the event definition and timeframe: here, the event is Investigator-assessed complete wound closure confirmed at 2 consecutive treatment phase visits by 16 weeks. The risk difference does not by itself explain why groups differed or establish whether the same contrast would occur in a different population.

The registry also posts a risk ratio and an odds ratio. General statistical explanation: the risk ratio compares the event probability in one group with the probability in another, while the odds ratio compares their odds. Both are relative measures. The same underlying data can produce values that look different across these scales, particularly when an event is not rare. These measures answer different mathematical questions, so their numerical values should not be interpreted as if they were on the risk-difference scale.

How should the confidence interval and p-value be read?

A confidence interval gives a range of effect values compatible with the data under the method’s assumptions and conveys uncertainty in the estimate. It is not a guarantee that the true effect lies within the observed interval, and it does not incorporate every possible source of bias. The primary interval is entirely on the positive side of zero. The reported p-value is p < 0.001. General statistical explanation: a p-value evaluates how unusual data at least as discrepant as those observed would be under a specified null model. It is not the probability that the treatment effect is zero, and it does not measure clinical importance.

The primary estimate and confidence interval are unadjusted re-calculations from posted summary statistics. The registry record does not provide a separate adjusted analysis to compare with them. The discrepancy indicator is false, so no discrepancy between a sponsor analysis and the recalculated comparison is flagged. The posted results remain the basis for describing what the registry reports.

Why do the continuous secondary outcomes use different summaries?

Time to complete wound closure and rate of wound closure are posted as means with standard deviations. A mean summarizes the arithmetic average, while a standard deviation describes spread among observations around that average. The registry reports a mean difference for each of these outcomes, with a confidence interval and an unadjusted p-value. General statistical explanation: a mean difference retains the measurement scale of the outcome, so interpretation depends on the unit. The time outcome is measured in days and the rate outcome in percentage wound closure per week.

Standard deviations describe variation among observations; they are not confidence intervals around the mean. A standard error, by contrast, describes uncertainty in an estimated quantity. The posted secondary results include standard deviations and standard errors, but the record does not list reported analyses for these outcomes. The displayed comparison estimates are therefore best understood as unadjusted summaries rather than as documented results from a registry-reported modeling plan.

General statistical explanation: continuous-outcome methods can be sensitive to distributional features, including skewness and unequal variability. The registry does not report diagnostic checks or alternative analyses for these features. It would be inappropriate to infer that a particular model or assumption was used beyond what is recorded.

Why does multiplicity matter?

The record lists multiple secondary outcomes, including repeated descriptions of time to complete wound closure, and posts several outcome comparisons. When many hypotheses are examined, the chance of at least one apparently noteworthy result can increase if each is interpreted at the same unadjusted threshold. General statistical explanation: multiplicity procedures can control or otherwise address this issue, but the registry record does not report a procedure. That missing information lowers the evidential weight of secondary p-values; it does not change the definition of the primary endpoint.

The registry reports the primary results as based on an ITT population. General statistical explanation: an intention-to-treat approach aims to preserve randomized group assignment in the analysis. The record does not provide further details about the exact analysis population construction, missing observations, or handling of participants without an endpoint assessment. Accordingly, the ITT label should be reported as recorded, without inferring unreported implementation details.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.193, and its 95% confidence interval ranges from 0.085 to 0.301. The interval does not include zero, indicating that the posted estimate is separated from no difference on the risk-difference scale under the interval method’s assumptions. Its width also shows that uncertainty remains around the size of the contrast: the data are compatible with a range of positive effects, not one exact value.

Precision is distinct from statistical significance. A p-value below a conventional threshold can coexist with uncertainty about the magnitude of an effect. The confidence interval is useful because it conveys both the direction and range of values compatible with the data. It does not account for possible bias from missing outcome data, measurement, or other design and conduct issues not described in the registry record.

The posted relative estimates have their own intervals: the risk ratio is 1.602 with an interval from 1.214 to 2.114, and the odds ratio is 2.236 with an interval from 1.406 to 3.555. Each interval belongs to its own effect scale. Their values should not be compared directly with the risk-difference interval as though all three described the same quantity.

For the secondary continuous outcomes, the intervals are also informative about precision. The time-to-closure mean difference is -17.17 days, with an interval from -27.89 to -6.448. The rate-of-closure mean difference is 2.34 percentage wound closure per week, with an interval from 0.569 to 4.112. These are unadjusted comparisons and should be read with the multiplicity and reporting limitations in mind. Confidence intervals quantify sampling uncertainty under a statistical method; they do not resolve limitations in the registry’s descriptions of missing data or analysis procedures.

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 illustrations based on the observed effects, not the trial’s original design calculations. For the binary outcomes, the entries are participants per arm. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario targets a stated fraction of the observed effect. The record does not report the trial’s own original sample-size assumptions.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect is real. The 90% power column uses a higher target chance of detection and therefore generally requires a larger planned group. These are design-planning quantities, not a measure of what happened in this completed trial. This is not observed power.

The rows represent planning for 100%, 75%, and 50% of the observed effect. A smaller assumed effect is harder to distinguish from random variation, so the planning illustration requires more participants per arm. The calculation uses the observed effect as its starting point; it does not establish that the same effect will occur in a future study.

For the continuous outcomes, the same general planning assumptions are listed, with a normal approximation and equal allocation. The registry’s sample-size-assumptions description distinguishes time-to-event calculations, which would report total events, from other calculations, which report participants per arm. The posted planning figures associated with these outcomes should be read according to that distinction and their outcome type, rather than as observed enrollment or observed outcomes. These illustrations do not reveal the original trial’s rationale, which is not reported in the registry record.

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 = 0.320; treatment proportion p₁ = 0.513; average p̄ = 0.417.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6972 = 1.3665.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6838 = 0.5755.
4. n = (1.3665 + 0.5755)² / (0.1927)² = 101.5, rounded up to 102 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 <- 0.320261437908497                          # control proportion
p1 <- 0.512987012987013                          # 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(1060670)
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 = 102 (80% power), 136 (90% power)
 75% of observed effect: n per arm = 178 (80% power), 238 (90% power)
 50% of observed effect: n per arm = 393 (80% power), 525 (90% power)
power.prop.test: 101.5 
Simulated power at n = 102 per arm: 0.812 (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 lists multiple secondary outcomes and reports results for several comparisons. It does not report a multiplicity adjustment, a prespecified hierarchy for testing outcomes, or an analysis plan explaining how inferential claims across outcomes were controlled. The registry’s analysis listings report no analyses. This does not show that no analysis was conducted; it means the registry record does not document those analyses there.

Multiplicity matters because each additional hypothesis test creates another opportunity for a result to appear unusual by chance. General statistical explanation: when a family of tests is interpreted together, a prespecified adjustment or hierarchy can help define how much weight to give the collection of results. Without such information, the unadjusted secondary p-values should be treated as less conclusive than a single primary comparison. This limitation does not automatically invalidate the primary result, but it affects how confidently the secondary findings can be used to reinforce it.

The primary outcome description identifies the Investigator assessment and ITT population. The record does not report an analysis plan with details on missing observations, imputation, endpoint assessment availability, or sensitivity analyses. It therefore is not possible from the registry record to determine how participants without a recorded primary assessment were handled, or whether the conclusions were tested under alternative missing-data assumptions.

The registry reports randomized allocation and no masking. It does not report the details of sequence generation, concealment, or assessment safeguards. Because the endpoint involved Investigator assessment, the absence of masking is relevant context when considering possible measurement influences; the record does not quantify or establish that such influences occurred. These omissions limit independent appraisal of the statistical methods, even though the primary endpoint and population are described.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: osteomyelitis (9.8%), diabetic foot infection (5.2%), cellulitis (4.5%), condition aggravated (3.9%), abcess limb (2.0%).

The registry reports serious adverse events affecting 38 participants in the active-treatment group and 55 in the control group. The corresponding groups at risk are 154 and 153. These are group-level counts in the record; they do not by themselves establish that treatment caused or prevented an event. The registry also reports zero other adverse events for each group. Death counts are not reported in the registry record.

The listed serious adverse-event terms and reported percentages include osteomyelitis at 9.8%, diabetic foot infection at 5.2%, cellulitis at 4.5%, condition aggravated at 3.9%, abcess limb at 2.0%, and gangrene at 2.0%. The registry does not provide enough detail in this summary to determine whether participants could contribute to more than one term or how the listed percentages were calculated. The percentages should therefore be read as reported term frequencies, not added together or treated as a single overall rate.

Serious-event counts are descriptive safety information. Interpretation requires attention to event definitions, follow-up, exposure, and the possibility of multiple events per participant, details not fully reported in the registry record. The counts alone are not a complete assessment of comparative safety.

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

The primary result describes a difference in the observed incidence of complete wound closure by 16 weeks between the randomized groups. The active-treatment group had more participants recorded as meeting the endpoint, and the unadjusted risk-difference interval is entirely above zero. This is evidence about the defined endpoint in the enrolled trial population, as represented in the registry record.

It does not establish that every participant will experience the same outcome, that the result applies to all people with diabetic foot ulcers, or that the observed contrast will recur in another study. The registry’s population description is specific: participants had neuropathy and ulcers distal to the malleolus, without significantly compromised arterial circulation. Generalizing beyond that description requires evidence not contained in this record.

The result also does not answer every question about wound care. Complete closure is one endpoint with a specified confirmation rule and assessment period. It does not alone describe ulcer recurrence, longer-term outcomes, quality of life, or all dimensions of safety. Although the registry lists some of these as secondary outcomes, results are not posted for all of them. The available secondary findings have no reported multiplicity strategy and should not be given the same inferential weight as the primary comparison.

A statistically clear estimate does not by itself establish clinical importance, mechanism, or causality beyond the design and measurement limitations. Randomization is an important feature of comparative trials, but the registry does not report all details needed to assess allocation procedures, missing data, or endpoint analysis. The findings should therefore be understood as a comparative registry result, with the endpoint definition, follow-up period, and reporting limits kept in view.

17. Why This Trial Matters Statistically

This trial illustrates how the interpretation of a clinical outcome depends on its operational definition. Complete wound closure was not simply a general impression of improvement: the registry specified 100% closure, Investigator assessment, confirmation at 2 consecutive treatment phase visits, and a 16-week timeframe. Clear endpoint definition is essential when interpreting an event count or comparing rates between randomized groups.

It also demonstrates why effect measures should be read on their own scales. The risk difference gives an absolute comparison in event probabilities; the risk ratio and odds ratio give relative comparisons. Confidence intervals add information about precision that a p-value alone cannot convey. Together, these measures describe different aspects of the posted result, while none removes uncertainty arising from design or reporting limitations.

The record provides a useful contrast between a registered primary endpoint and a broader set of secondary outcomes. Multiple secondary comparisons can offer complementary perspectives, but without a reported hierarchy or multiplicity strategy their p-values warrant restraint. The fact that some listed outcomes have no posted results also illustrates that a registry’s outcome list and its available results are not always equally complete.

Finally, planning illustrations based on observed effects are not a substitute for original design assumptions. They can show how sample-size needs change when a hypothetical target effect is reduced, but they do not reveal why the trial enrolled as it did or how likely it was to detect its actual effect. Keeping planning calculations separate from trial results is an important part of sound statistical interpretation.

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 does not report the original sample-size justification or the assumptions used to plan enrollment. The posted sample-size illustrations are based on observed effects and cannot be used to reconstruct the original design rationale. Detailed allocation procedures are not reported, beyond randomized allocation, and masking is recorded as none.

The primary outcome is based on Investigator assessment. The endpoint definition is stated, but the record does not report further details about assessor training, adjudication, or procedures to maintain consistent assessment. The absence of masking is relevant when evaluating an assessor-measured endpoint, although the record does not establish that assessments were biased.

The registry identifies an ITT population but does not describe missing outcome data, the handling of participants without an assessment, or sensitivity analyses. Enrollment is recorded as 545, while primary outcome group denominators are reported separately; the record does not explain the relationship between those figures. This limits assessment of the completeness and construction of the analyzed population.

Secondary outcome reporting is incomplete: the registry lists recurrence and SF-36 change but does not post results for them. The analysis listings report no analyses, and no multiplicity strategy is described. Consequently, the secondary results have limited inferential context. Serious adverse-event counts are reported, but details about event ascertainment, multiple events, and the basis of term percentages are not fully described in the registry record.

These limitations concern what can be evaluated from the registry record. They do not establish that unreported procedures were absent, but they restrict independent appraisal of the trial’s analysis and reporting.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Safety and Efficacy Study of INTEGRA® Dermal Regeneration Template for the Treatment of Diabetic Foot Ulcers — NCT01060670.
• Registry record last updated 2016-09-22; status last verified 2016-07.
• Results first posted 2016-09-22.
• 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

NCT01060670 is a completed randomized, controlled, parallel-group trial with no masking, evaluating INTEGRA® Dermal Regeneration Template against conventional wound therapy for neuropathic diabetic foot ulcers. The registry reports enrollment of 545 and lists the study start as 2010-04 and primary completion as 2014-06.

The primary endpoint was Investigator-assessed complete wound closure, defined as 100% closure confirmed at 2 consecutive treatment phase visits by 16 weeks. The reported primary results use the ITT population. The unadjusted comparison favors a higher observed incidence of closure in the active-treatment group, with a risk-difference confidence interval above zero.

Some secondary outcomes and serious adverse-event summaries are posted, but results are not reported for every listed secondary outcome. The registry does not document a multiplicity strategy, detailed missing-data handling, or the original sample-size assumptions. These reporting limits should inform interpretation of the primary and secondary findings.