Prineo (Dermabond Protape) Versus Sutures for Full-thickness Surgical Incisions: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prineo (Dermabond Protape) Versus Sutures for Full-thickness Surgical Incisions (NCT00557947), a randomized phase 4 study. The primary outcome is Continuous Apposition of the Skin Edges Without Wound Dehiscence or Re-closure as Measured by the Upper Limit of 95% Confidence Interval in Proportion of Successes for Each Groups..

2. Clinical Question

3. Trial Design

The registry classifies this as a Phase 4, randomized, multicenter, prospective, controlled study. It lists no masking and a parallel model. Separately, the brief summary describes each incision as divided into two halves and the halves randomized to the two closure approaches; the arm descriptions say that the participant was their own control. These details mean the reported treatment comparison is paired within the participant or incision, rather than a conventional comparison of two wholly separate participant groups. The registry does not explain how its parallel-model classification relates to that paired description.

The study title frames the objective as showing equivalence of Dermabond Protape to intradermal sutures for skin closure of full-thickness surgical incisions. The registry reports enrollment of 83, while its brief summary describes a study of up to 80 subjects. It does not explain this difference or report the number included in each analysis beyond the posted group counts of 83 for each closure approach.

The described follow-up visits were at 24 hours (± 6 hours), 7 days (± 1 day), 12 - 25 days, and 90 days (± 10 days). The primary endpoint was assessed at 12-25 days post-operation. The registry lists Dermabond Protape and suture as device interventions. It reports study start as 2007-08, primary completion as 2008-04, and status as completed. It does not report the original sample-size justification, detailed site information, or further operational details of randomization.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: The primary analysis is based upon intent to treat 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 Continuous Apposition of the Skin Edges Without Wound Dehiscence or Re-closure as Measured by the Upper Limit of 95% Confidence Interval in Proportion of Successes for Each Groups., measured over 12-25 days post-operation.

The primary endpoint was the number of participants with continuous apposition of the skin edges, without wound dehiscence or re-closure, assessed 12-25 days post-operation. The registry describes the primary analysis as intent to treat. The outcome is binary: each participant’s result is classified as a success or not a success under the endpoint definition. The posted arm counts are 74 successes among 83 for Dermabond Protape and 78 among 83 for suture.

The registry’s equivalence rule uses the difference between the success proportions, with the suture proportion minus the Dermabond Protape proportion. It states that equivalence is demonstrated if the upper limit of the 95% confidence interval does not exceed 12%. This margin gives the comparison a prespecified interpretation: the question is not simply whether the observed proportions are identical, but whether the interval’s upper limit stays within the stated tolerance. The endpoint is therefore tied to a particular clinical feature and follow-up window, not to every possible measure of wound healing, appearance, or later outcome.

General: A confidence interval communicates the range of values reasonably compatible with the data and the analysis method. For an equivalence question, the interval must be considered against the stated margin; a nonsignificant test of difference alone does not establish equivalence.

7. Results Posted in the Registry

• Suture: 94.0% (78/83) versus 89.2% (74/83) on control; risk difference 4.8 percentage points (95% CI -3.6 to 13.2), risk ratio 1.05 (0.96–1.16); unadjusted two-proportion z-test p = 0.264.

8. Secondary Efficacy Endpoints

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

Time Required to Close the Final Skin Layer

• 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:
  • Suture: mean 6.65 versus 1.46 on control; difference 5.19 (95% CI 4.30 to 6.08), standardized effect d = 1.78; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Suture than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists four secondary outcomes: time required to close the final skin layer and three cosmetic outcome entries. A numerical result is posted for the closure-time outcome. Numerical results for the cosmetic outcomes are not reported in the registry record, so the overall secondary evidence is incomplete. The reported time comparison concerns the speed of completing the final skin layer, whereas the primary endpoint concerns skin-edge apposition without dehiscence or re-closure. They address different aspects of the procedure and should be interpreted separately.

The posted closure-time analysis indicates a difference between the approaches in the recorded time measure, with a small p-value in both the sponsor analysis and the unadjusted recalculation. That statistical signal does not establish that the primary wound outcome differs, nor does it answer the cosmetic questions. Conversely, the primary result does not resolve the procedure-time or cosmetic outcomes. Each endpoint has its own definition, analysis, and uncertainty.

Secondary results generally carry less confirmatory weight when many outcomes are considered, especially when the registry does not report a plan for controlling multiplicity. Testing multiple endpoints creates more opportunities for apparently notable results by chance. The record does not state whether any adjustment or hierarchy was used, so the secondary findings should be treated as supportive or exploratory rather than as independent confirmation of the primary comparison. The unavailable cosmetic results further constrain any summary of the secondary-outcome pattern.

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

• Time Required to Close the Final Skin Layer
• Cosmetic Outcome
• Cosmetic Outcome
• Cosmetic Outcome

9. Statistical Interpretation

10. Statistical Methods Explained

How should the primary analysis be understood?

The primary endpoint records success or non-success for each participant, so it is a binary outcome. The registry says that the primary analysis was based on the intent-to-treat population, which generally means participants are analyzed according to the assigned treatment approach, rather than being reclassified according to later events. The record does not describe how missing outcomes, protocol deviations, or incomplete follow-up were handled, so the practical details of the intent-to-treat analysis are not reported in the registry record.

The study description says that each incision was split into two halves, with one half randomized to Dermabond Protape and the other to intradermal suture, and that each participant was their own control. Thus, outcomes under the two closure approaches are paired. In general, a paired analysis uses the fact that two observations come from the same participant or unit. It focuses on within-pair differences, rather than assuming that observations in the treatment groups are unrelated.

Why does McNemar’s method fit this structure?

The sponsor reports McNemar’s method for the difference in proportions of successes. In general, McNemar’s test is designed for paired binary outcomes. The paired results include whether both halves succeed, whether both do not succeed, and which half alone meets the success definition. The discordant pairs—those with different outcomes between the two halves—are especially important to the method. The marginal success counts alone do not show how many pairs were concordant or discordant, so a reader cannot recreate the McNemar result from the two marginal counts alone.

The registry also lists a simple unadjusted recalculation based on posted summary statistics. That calculation gives a risk difference of 0.048, a confidence interval from -0.036 to 0.132, and p = 0.264. It does not reproduce the sponsor’s paired analysis, which reports 4.8 percentage points, a confidence interval from -0.0 to 10.9, and p = 0.219. These are not interchangeable analyses: the recalculation does not use the within-participant pairing. Because the study description identifies paired assignment and the registry reports McNemar’s method, the sponsor’s result is the relevant reported primary analysis.

What does the equivalence margin do?

The registry defines the difference as the suture success proportion minus the Dermabond Protape success proportion. Its criterion says equivalence is demonstrated if the upper limit of the 95% confidence interval for that difference does not exceed 12%. In general, an equivalence margin defines the largest difference that the study’s rule treats as acceptable for the comparison. The interval, not merely the point estimate, is compared with the margin. A point estimate within the margin is not sufficient if the interval extends beyond it.

The sponsor-reported upper limit is 10.9, below the stated margin of 12%. The reported p-value is not, by itself, the criterion described in the registry. For equivalence interpretation, the direction of the difference and the prespecified margin matter. The registry does not report the full statistical analysis plan or additional details about how the confidence interval was constructed, beyond naming McNemar’s method in the reported analysis.

Why might a different analysis give a different interval?

General: Standard errors and confidence intervals depend on both the outcome data and the assumptions of the analysis. An unpaired calculation treats the groups as independent; a paired method incorporates the relationship between outcomes within the same participant. When paired observations are related, ignoring that relationship can alter the estimated uncertainty. The direction and size of that change depend on the pattern of paired outcomes. Since the paired cross-tabulation is not reported in the registry record, the recalculation cannot recover that information.

How should the secondary time outcome be analyzed conceptually?

Time required to close the final skin layer is a continuous measurement, reported as a mean and standard deviation. The registry reports a two-sided t-test for the sponsor’s comparison. In general, a t-test evaluates evidence about a difference in group means under its statistical assumptions. The analysis reports p < 0.001. The unadjusted recalculation reports a mean difference of 5.19 minutes, a confidence interval from 4.301 to 6.079, and p < 0.001. This endpoint measures procedure time, a different construct from the primary binary wound-apposition outcome, and should not be substituted for it.

General: Standard deviations describe variation among individual measurements, whereas a confidence interval for a mean difference describes uncertainty about the estimated contrast. They answer different questions. If a continuous outcome has strongly skewed values or influential outliers, a mean-based method can be less representative or its assumptions may be less suitable. The registry does not report distributional checks or alternative analyses.

What is not specified?

The registry does not report the original sample-size justification, the full protocol or statistical analysis plan, an interim-analysis plan, or details of missing-data methods. It does not report the paired outcome table needed to independently reproduce the McNemar analysis. It also does not explain how the listed parallel model relates to the split-incision, participant-as-own-control description. These omissions limit independent reconstruction of the sponsor’s analysis, but do not change the results that the registry reports.

11. Confidence Intervals and Precision

Precision is reflected in the width of a confidence interval: narrower intervals indicate a more tightly estimated contrast under the analysis assumptions, while wider intervals leave more plausible values compatible with the data. The sponsor’s primary analysis reports a 95% confidence interval from -0.0 to 10.9 percentage points for the difference in success proportions. Its upper limit is below the registry’s 12% equivalence margin, but the interval still spans a range of possible differences rather than identifying a single exact value.

The simple unadjusted recalculation reports a confidence interval from -0.036 to 0.132 for the risk difference. Its upper limit is above 12% when expressed as a proportion, so it does not give the same margin-based result as the sponsor’s paired analysis. The methods differ: the sponsor reports McNemar’s paired approach, while the recalculation uses unadjusted summary statistics. The recalculated interval should not be used as if it were the sponsor’s primary estimate.

The arm counts—74 successes among 83 for Dermabond Protape and 78 among 83 for suture—offer useful context, but the precision of the paired contrast also depends on how outcomes align within participants. The record does not report that paired pattern. The posted confidence interval and method therefore provide the principal account of precision for the primary comparison.

General: Confidence intervals are not guarantees that the true value lies within the specific interval, nor do they measure the probability that one treatment is better. They summarize uncertainty under a statistical model and analysis procedure. A confidence interval should be interpreted in relation to the research question, outcome definition, and equivalence margin. Here, the interval applies to early skin-edge apposition under the study’s stated definition; it does not quantify precision for cosmetic outcomes or other unreported measures.

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, not total events. The study’s sample-size assumptions state a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning illustrations use the observed effect or a stated fraction of that observed effect. The registry’s original design assumptions and sample-size justification are not reported in the registry record. No time-to-event planning figures apply to the posted primary endpoint; the stated convention for time-to-event analyses is total events, while other planning figures are participants per arm.

The 80% power column gives the estimated participants per arm under the listed assumptions for a design with an 80% chance of detecting the assumed effect if that effect were present. The 90% power column gives the corresponding per-arm planning figure for a 90% chance under those assumptions. These are planning probabilities attached to hypothetical designs, not probabilities that the treatment effect is real and not a measure of the completed trial’s result.

The illustrations consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For the primary comparison, the per-arm figures are 521 and 697 for planning at 100% of the observed effect; 987 and 1,321 for planning at 75%; and 2,354 and 3,151 for planning at 50%, for 80% and 90% power respectively. The progressively larger figures illustrate the general principle that smaller effects are harder to distinguish from random variation and therefore require more participants under otherwise comparable assumptions.

These are planning illustrations calculated from the observed effect, not the trial’s own design calculation. This is not observed power. The registry does not report whether the original study was designed around these assumptions or what effect and margin informed its original target.

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 = 0.892; treatment proportion p₁ = 0.940; average p̄ = 0.916.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3930 = 0.7703.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3915 = 0.3295.
4. n = (0.7703 + 0.3295)² / (0.0482)² = 520.8, rounded up to 521 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 <- 0.891566265060241                          # control proportion
p1 <- 0.939759036144578                          # 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(557947)
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 = 521 (80% power), 697 (90% power)
 75% of observed effect: n per arm = 987 (80% power), 1,321 (90% power)
 50% of observed effect: n per arm = 2,354 (80% power), 3,151 (90% power)
power.prop.test: 520.8 
Simulated power at n = 521 per arm: 0.807 (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. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis uses McNemar’s method, appropriate to the registry’s description of paired incision segments and each participant serving as their own control. It reports a 4.8 percentage-point difference in success proportions, with a 95% confidence interval from -0.0 to 10.9 and p = 0.219. The interval’s upper limit is below the registry’s stated equivalence threshold of 12%. The sponsor’s result is the primary analysis posted in the record and should be used to describe the reported study finding.

The unadjusted recalculation uses the posted summary statistics and gives a risk difference of 0.048, with a confidence interval from -0.036 to 0.132 and p = 0.264. It does not incorporate the paired outcome structure in the way McNemar’s method does. The difference between the results is therefore a reminder that analysis choices matter, not evidence that one set of numbers can simply replace the other.

The registry marks no discrepancy between the reported analysis and its records. Even so, the posted marginal counts are insufficient to independently reproduce the paired analysis, because the paired outcome pattern is not reported. The sponsor’s analysis gives the relevant reported confidence interval for applying the registry’s stated margin; the recalculation is a separate, simpler illustration rather than an alternative sponsor result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists five outcome measures and five analyses, and names several secondary outcomes, including three cosmetic outcome entries. It does not report a multiplicity adjustment, a hierarchy among secondary endpoints, or a plan for interpreting multiple statistical tests. General: when several outcomes are tested, the chance of at least one apparently unusual result can increase unless the analysis plan addresses that issue. This is why secondary p-values, particularly when unadjusted, warrant more caution than a prespecified primary analysis.

The primary analysis population is described as intent to treat. However, the registry does not report the number of participants with missing primary outcome data, how missing outcomes were handled, whether any participants were excluded from analysis, or whether a sensitivity analysis was conducted. The arm counts are 83 for each approach, but these counts alone do not establish that all scheduled assessments were complete or that all randomized participants contributed an observed outcome.

The study description indicates paired closure segments within participants. The registry does not report the paired success/non-success cross-tabulation, so the McNemar calculation cannot be independently reconstructed from the posted marginal counts. It also lists a parallel model without explaining how that classification relates to the paired description. The registry does not report details of allocation concealment, protocol deviations, interim analyses, or the original statistical analysis plan. These details should not be inferred from the reported results.

The endpoint was assessed at 12-25 days post-operation, and the brief summary lists follow-up visits through 90 days (± 10 days). The registry does not report how later follow-up contributes to the primary analysis. Such omissions do not establish that data were missing or that analyses were inappropriate; they mean those aspects are not reported in the registry record and cannot be evaluated from the posted information.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: wound dehiscence (1.2%), infection (1.2%), seroma (1.2%), wound necrosis (1.2%), chest pain (1.2%).

The registry reports serious adverse events in 3 of 83 at risk for Dermabond Protape and 3 of 83 at risk for suture. It reports other adverse events in 16 of 83 at risk for each of those groups. The procedure category has 11 serious and 24 other adverse events among 83 at risk; the unrelated category has 3 serious and 7 other adverse events among 83 at risk. These are the posted category counts, and the categories should not be added together because the registry does not explain whether an event or participant could appear in more than one category.

The serious adverse-event terms listed with their reported percentages are Wound Dehiscence, Infection, Seroma, Wound Necrosis, Chest Pain, and Metastic Breast Cancer, each at 1.2%. The registry does not provide further event-level detail in this record. Death counts are not reported in the registry record.

These figures describe recorded events and at-risk counts; they do not establish that an event was caused by a closure approach. Equal group counts do not prove equal safety, particularly without detail on event definitions, timing, severity grading, and attribution. The safety information should be read as descriptive registry reporting, not as a complete comparative safety assessment.

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

The posted primary analysis describes early success in maintaining continuous skin-edge apposition without dehiscence or re-closure. The sponsor-reported paired estimate has a 95% confidence interval whose upper limit is below the 12% margin specified in the registry’s equivalence rule. Thus, the reported interval meets that stated numerical criterion for this endpoint and follow-up window. The result remains an estimate with uncertainty, not proof that the approaches have exactly equal outcomes.

The finding applies to the participants and incision segments included in this study and to the primary outcome as defined. It does not automatically extend to cosmetic appearance, other wound outcomes, later follow-up, other surgical settings, or other closure materials. The registry lists cosmetic secondary outcomes but does not report their numerical results. It also does not provide enough paired outcome detail to independently reconstruct the sponsor’s McNemar analysis.

The simple unadjusted recalculation gives a different interval because it does not account for the paired structure described for the study. It is useful as a demonstration that method and design structure affect uncertainty, but it is not a substitute for the sponsor’s reported primary analysis. The sponsor’s interval is the one that directly corresponds to the registry’s reported McNemar method and stated decision rule.

The secondary closure-time result addresses a distinct procedural measure and should not be conflated with the primary wound-apposition result. Likewise, the reported adverse-event counts are descriptive and do not establish attribution or comparative safety. Missing-data methods, multiplicity handling, and the original sample-size justification are not reported in the registry record, limiting evaluation of those aspects of the evidence.

Overall, the registry supports a narrow statistical reading: the reported primary confidence interval satisfies the stated upper-limit criterion, while the interval and the available secondary and safety information do not answer every broader question about the closure approaches. No clinical recommendation follows from these statistics alone.

18. Why This Trial Matters Statistically

This study illustrates why a clinical comparison must be read in light of its design. The registry describes a split incision and each participant serving as their own control. That paired structure affects how uncertainty should be calculated. The sponsor’s McNemar analysis reflects paired binary outcomes, whereas a simple recalculation from the marginal group summaries does not. The resulting intervals differ, showing why matching the statistical method to the design is important.

It also demonstrates the distinction between a test for a difference and a margin-based equivalence question. The primary result is interpreted against a stated 12% upper-limit criterion. A p-value alone does not answer that question; the confidence interval and its direction relative to the margin are central. The reported upper bound falls below the stated limit, while the interval still expresses uncertainty about the underlying difference.

The record also shows the importance of transparent reporting. The paired outcome table, original sample-size justification, missing-data handling, and multiplicity plan are not reported in the registry record. Those details would help readers evaluate reproducibility and the strength of conclusions beyond the main endpoint. Secondary measures can address different questions, but their evidential weight depends on prespecification and interpretation across multiple outcomes.

Finally, the planning illustrations derived from the observed effect are distinct from the trial’s actual design assumptions and from observed power. Keeping those concepts separate prevents a retrospective calculation from being mistaken for the rationale or performance of the completed study. These statistical distinctions matter whenever a trial reports an equivalence-style conclusion from a modest sample and a paired outcome design.

19. Limitations

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

The registry reports enrollment of 83, while the brief summary describes a study of up to 80 subjects; the reason for this difference is not reported in the registry record. The posted counts show 83 in each treatment group, but the record does not explain participant flow, exclusions, or completeness of outcome assessment. The primary analysis is described as intent to treat, yet the handling of missing data is not reported.

The design description has both a parallel-model classification and a split-incision, participant-as-own-control description. The record does not explain how these labels relate. The paired outcome cross-tabulation is not posted, limiting independent reproduction of the McNemar result. Allocation concealment and detailed randomization procedures are also not reported. Masking is listed as none, so the study was unmasked according to the registry; the record does not describe whether this could affect outcome assessment.

The primary endpoint is limited to early wound apposition at 12-25 days post-operation. Although follow-up visits are listed through 90 days (± 10 days), results for later outcomes are not described as part of the primary analysis. Three cosmetic outcome entries are listed, but their numerical results are not reported in the registry record. The original sample-size justification, multiplicity plan, interim-analysis plan, and complete statistical analysis plan are also not reported.

The trial is multicenter, but the registry does not report the number or characteristics of centers, participant characteristics, or further clinical context. The safety summaries give category counts but not detailed attribution or event-level information. These are limits on interpretation of the registry record; they do not, by themselves, establish that the trial was conducted incorrectly or that unreported procedures were absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Prineo (Dermabond Protape) Versus Sutures for Full-thickness Surgical Incisions — NCT00557947.
• Registry record last updated 2012-07-19; status last verified 2012-06.
• Results first posted 2012-07-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT00557947 is a completed randomized Phase 4 study of Dermabond Protape (Prineo) versus intradermal sutures for full-thickness surgical incision closure. The registry reports enrollment of 83, no masking, and a multicenter study. Its description states that incision halves were randomized to the two approaches and that each participant was their own control.

The primary outcome was continuous skin-edge apposition without wound dehiscence or re-closure at 12-25 days post-operation. The sponsor reports a paired McNemar analysis with a 4.8 percentage-point difference, a 95% confidence interval from -0.0 to 10.9, and p = 0.219. The upper confidence limit is below the registry’s stated 12% equivalence margin. A separate unadjusted recalculation gives different results and does not account for pairing.

The record also reports closure-time results and adverse-event counts. Cosmetic outcome results, the original sample-size justification, missing-data methods, and multiplicity handling are not reported in the registry record.