Study Looking at the Effect of Silverlon on Post Operative Wound Infections: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Looking at the Effect of Silverlon on Post Operative Wound Infections (NCT01143883), a randomized na study. The primary outcome is Surgical Site Infection.

2. Clinical Question

This is a question about an infection outcome during a defined postoperative follow-up period, not a comparison of wound healing at later times or of other surgical outcomes. The registry describes monitoring the incision to determine whether antibiotics were needed. It does not give a more detailed diagnostic definition of surgical site infection or report a separate breakdown by infection type.

3. Trial Design

The registry describes a prospective, randomized, controlled, parallel-group trial. Participants were assigned to Silverlon® or standard postoperative dressing with a stated 1:1 allocation ratio. The study was open label: neither investigators nor participants were blinded to the assigned dressing after randomization. The registry lists an enrollment of 110 and a completed study.

The study began in 2009-06, and primary completion is listed as 2010-09. Its stated clinical setting was elective colorectal surgery with an abdominal incision of at least 6 cm. The primary outcome timeframe ran from the day of surgery through 30 days postoperatively. The intervention description specifies that Silverlon® was applied to the surgical wound after surgery; the comparator was plain gauze dressing.

The primary outcome results report 13.0% for the Silverlon Dressing group, with 55 participants, and 33.0% for the Standard of Care Dressing group, with 54 participants. The comparison statistics use 7 events among 55 participants for Silverlon and 18 among 54 for standard dressing. The registry's description of the analysis population says participants were analyzed according to the randomized group in which they received treatment and were treated according to study protocol. The reason the outcome group sizes do not match the registry enrollment is not reported in the registry record.

The record does not report the method used to generate the random sequence, allocation concealment procedures, the number of study sites, or the trial's original statistical analysis plan. It also does not report the original sample-size justification or whether interim analyses were planned.

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 number of participants analyzed was based on the number who received treatment according to their randomized group and were treated according to study protocol

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 Surgical Site Infection, measured over Day of surgery up to 30 days post operatively.

The primary endpoint is the percentage of participants with a surgical site infection, assessed from the day of surgery through postoperative day 30. The registry description says the incision was monitored to determine whether antibiotics were needed. This makes the endpoint a binary participant-level outcome for the stated follow-up period: a participant either met the recorded infection outcome or did not.

An infection endpoint is relevant to this trial because the comparison concerns postoperative dressings intended for surgical wounds, and the stated clinical objective was to compare infection incidence between dressing groups. Reporting a percentage makes the outcome interpretable as the share of participants in each group who experienced the recorded event. The registry does not report a fuller case definition, the diagnostic criteria used, or whether the decision to give antibiotics was the sole criterion for classifying an infection. Those details would help readers assess how consistently the outcome was determined.

The endpoint is limited to the specified postoperative period. It does not describe infections occurring after the follow-up window, infection severity, treatment burden, or other outcomes such as wound healing. Those additional endpoints are not reported in the registry record.

7. Results Posted in the Registry

• Silverlon Dressing: 12.7% (7/55) versus 33.3% (18/54) on control; risk difference -20.6 percentage points (95% CI -36.0 to -5.3), risk ratio 0.38 (0.17–0.84); unadjusted two-proportion z-test p = 0.011.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is classified according to whether a surgical site infection was recorded during the follow-up period. For this type of endpoint, group results are commonly expressed as event counts and proportions. The posted infection counts are 7 among 55 participants assigned to Silverlon and 18 among 54 assigned to standard dressing. The registry also reports percentages of 13.0% and 33.0%, respectively.

What does the risk difference describe?

The risk difference is the Silverlon group event proportion minus the standard-dressing group event proportion, following the comparison direction used in the posted results. Its estimate is -0.206, with a 95% confidence interval from -0.360 to -0.052. A negative estimate indicates a lower observed event proportion in the first-named group. The risk difference is an absolute measure, on the proportion scale. It is useful because it describes the size of the observed separation between group event proportions without expressing that separation relative to the comparator.

In general, an estimated risk difference is subject to sampling uncertainty because the observed participants are not the only possible sample from the target population. A confidence interval conveys a range of estimates compatible with the data and the statistical procedure. Its width reflects how precisely the difference is estimated. A narrow interval conveys more precision than a wide interval, though neither guarantees that the study population or outcome definition is appropriate for every application.

How do the relative measures differ?

The registry reports a risk ratio of 0.382, with a confidence interval from 0.174 to 0.840. A risk ratio expresses the event proportion in one group relative to the other group. A value below one indicates a lower observed proportion in the first group under this comparison. The odds ratio is 0.292, with a confidence interval from 0.110 to 0.773. Odds are the ratio of the chance of an event to the chance of no event; an odds ratio compares those odds between groups. Risk ratios and odds ratios answer related but distinct questions. When events are not rare, the odds ratio can be farther from one than the corresponding risk ratio, so it should not be described as if it were a risk ratio.

What does the p-value contribute?

The unadjusted p-value is 0.011. In general, a p-value measures how compatible the observed data are with a specified null hypothesis, under the assumptions of the test. A smaller p-value indicates that the observed data would be less typical if the null model held. It is not a measure of the size or clinical importance of the difference, and it is not the chance that the result occurred by chance. The posted p-value is unadjusted; the registry record does not report a multiplicity plan for interpreting several outcomes or comparisons.

The registry labels the difference and relative measures as comparisons, but does not report details of the statistical test or interval construction. The exact analysis method, including any continuity correction or alternative handling of small counts, is not reported in the registry record. Therefore, the posted estimates and intervals should be read as the registry's stated results rather than as a basis for attributing a particular unreported calculation method.

Why can event counts matter?

For binary outcomes, uncertainty depends in part on the number of participants and the number of events. General statistical methods that assume a simple binomial model can be unreliable when event counts are sparse or when the data depart from their assumptions. Over-dispersion is a general term for variability greater than a model expects; it can make standard errors too small if not handled appropriately. The registry does not report an assessment of over-dispersion, and this trial's binary endpoint is not a repeated count outcome for which over-dispersion would ordinarily be the central modeling issue.

Random allocation is intended, in general, to support a fair comparison by making assigned groups comparable on average. It does not guarantee exact balance in every characteristic, especially in a trial with limited event counts. The record does not report baseline characteristics or adjusted estimates, so the degree of balance and the effect of any prognostic factors cannot be assessed from the posted outcome results alone.

What can be inferred from the posted analysis?

The reported statistics describe the unadjusted difference in recorded infections between the randomized groups during the stated follow-up. They do not establish that the dressing alone produced the difference, rule out chance variation, or show whether the result would be replicated. The interpretation also depends on the consistency of outcome assessment. Because the study was open label and the record does not report blinded outcome assessment, diagnostic criteria, or adjudication procedures, the possibility of outcome-classification differences cannot be evaluated.

10. Confidence Intervals and Precision

The registry reports a risk difference of -0.206, with a 95% confidence interval from -0.360 to -0.052. In general, a confidence interval describes a range of values for the population contrast that are reasonably compatible with the observed sample and the method's assumptions. It is not a range containing a fixed proportion of individual outcomes, nor does it mean that the true effect has a 95% probability of lying inside this particular interval.

The interval is entirely below zero, matching the direction of the reported estimate. Its width also matters: values across the interval represent materially different possible magnitudes of the absolute contrast. The interval therefore supports a direction for the estimated group difference while leaving uncertainty about its precise size. The observed event counts—7 among 55 for Silverlon and 18 among 54 for standard dressing—are limited, and the interval reflects the resulting uncertainty rather than a single exact population value.

The relative-effect intervals are also reported: the risk ratio is 0.382, with a confidence interval from 0.174 to 0.840, and the odds ratio is 0.292, with a confidence interval from 0.110 to 0.773. These intervals likewise express uncertainty in relative terms. Their interpretation depends on the chosen measure, and the odds ratio should not be read as a direct percentage reduction in risk.

Confidence intervals account for sampling uncertainty under their statistical assumptions, but they do not account automatically for every limitation. They cannot correct for differences in outcome classification, departures from the planned analysis population, missing outcome data, or limited generalizability. The statistical method used to construct the posted intervals is not reported in the registry record.

11. Planning a Similar Trial: Sample Size

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

The planning figures describe participants per arm for 80% power and participants per arm for 90% power. They are shown for planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For 100% of the observed effect, the figures are 65 participants per arm for 80% power and 86 participants per arm for 90% power. For 75% of the observed effect, they are 125 participants per arm for 80% power and 166 participants per arm for 90% power. For 50% of the observed effect, they are 299 participants per arm for 80% power and 399 participants per arm for 90% power.

These planning calculations assume a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The accompanying curve represents the same planning relationship: as the effect being targeted becomes smaller, more participants are needed to distinguish it from no difference with the stated power. The 80% and 90% columns describe the probability, under the planning assumptions and a specified true effect, of detecting that effect at the stated significance level; 90% power requires more participants than 80% power for each effect scenario.

The sample-size figures are planning illustrations based on the observed effect, not observed power. The registry record does not report the trial's original design assumptions or sample-size justification, so these calculations should not be treated as the basis on which the trial was originally planned.

12. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.333; treatment proportion p₁ = 0.127; average p̄ = 0.230.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5954 = 1.1670.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5773 = 0.4859.
4. n = (1.1670 + 0.4859)² / (-0.2061)² = 64.3, rounded up to 65 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 <- 0.333333333333333                          # control proportion
p1 <- 0.127272727272727                          # 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(1143883)
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 = 65 (80% power), 86 (90% power)
 75% of observed effect: n per arm = 125 (80% power), 166 (90% power)
 50% of observed effect: n per arm = 299 (80% power), 399 (90% power)
power.prop.test: 64.3 
Simulated power at n = 65 per arm: 0.819 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

The registry posts one primary outcome: surgical site infection during the period from the day of surgery through postoperative day 30. It does not post secondary outcome results. The comparison includes an unadjusted p-value, but the registry record does not report a prespecified plan for controlling multiplicity across outcomes, analyses, or possible subgroup comparisons. Without that plan, the p-value should be read as an unadjusted result rather than as an adjustment for a family of tests.

The record describes the analysis population as participants who received treatment according to their randomized group and were treated according to study protocol. This is not a full intention-to-treat description of all randomized participants. The outcome group sizes are 55 for Silverlon and 54 for standard dressing, while enrollment is listed as 110. The reason for the difference between enrollment and analyzed group sizes, including whether any participants were excluded or lacked outcome data, is not reported in the registry record. No missing-data method, imputation procedure, or sensitivity analysis is reported.

The registry record also does not report protocol deviations, participant flow, reasons for withdrawal, or whether any participants crossed between treatment groups. These omissions make it difficult to assess how the stated analysis population was formed or whether the outcome results could be sensitive to exclusions. The outcome counts and group sizes remain interpretable as the posted analysis, but the missing information limits assessment of the analysis population's relationship to all randomized participants.

No adjusted analysis or subgroup analysis is posted. The record does not report which covariates, if any, were intended for adjustment, or whether analyses beyond the primary comparison were planned. These matters are distinct from the displayed unadjusted comparison and cannot be inferred from its estimates.

14. 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 1.82% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event record lists no serious adverse events in either group: 0 among 55 at risk in the Silverlon Dressing group and 0 among 55 at risk in the Standard of Care Dressing group. For other adverse events, it lists 1 among 55 at risk in the Silverlon group and 0 among 55 at risk in the standard-dressing group. These are the registry's posted counts; they should be read separately from the primary infection outcome.

The adverse-event denominators differ in presentation from the primary outcome analysis, where the standard-dressing group includes 54 participants. The reason is not reported in the registry record. The record does not identify the nature of the other adverse event, provide a severity breakdown for non-serious events, or give a narrative account of event assessment. Death counts are not reported in the registry record.

Zero recorded serious adverse events in these groups does not establish that serious events cannot occur, and the counts do not by themselves permit a broad safety conclusion. The registry's adverse-event information is limited to the listed counts and at-risk group sizes.

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

The posted results show fewer recorded surgical site infections in the Silverlon group than in the standard-dressing group during the stated postoperative follow-up: 13.0% versus 33.0%. The unadjusted risk difference is -0.206, with a 95% confidence interval from -0.360 to -0.052, and the unadjusted p-value is 0.011. These statistics describe the observed comparison and its sampling uncertainty in the analyzed groups.

The finding does not by itself prove that the dressing caused the difference. Randomization strengthens the basis for comparing groups, but the open-label design and the absence of reported details about infection criteria or blinded assessment leave questions about how outcomes were classified. The registry record also does not explain the difference between enrollment and the primary outcome group sizes, or report missing-data handling and sensitivity analyses.

The estimates apply to the study population described in the registry: patients undergoing elective colorectal procedures with an abdominal incision of at least 6 cm. They concern the recorded infection outcome from surgery through postoperative day 30. They do not establish results for other procedures, incision types, follow-up periods, or patient populations. Nor do they describe infection severity, long-term outcomes, or broader measures of postoperative recovery.

The relative measures and confidence intervals provide additional ways to describe the same comparison, but they do not remove uncertainty about its magnitude or transportability. The posted result is evidence about this trial's observed groups, not a guarantee of the result in another setting. The registry does not report an adjusted analysis, a multiplicity strategy, or the original design assumptions. Those limitations should remain part of any interpretation of the numerical finding.

16. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can be expressed using both absolute and relative measures for a binary clinical outcome. The risk difference of -0.206 describes the absolute contrast between the observed infection proportions, while the risk ratio of 0.382 and odds ratio of 0.292 express relative contrasts. Each measure answers a different statistical question. Reporting more than one can help readers distinguish the absolute scale of the observed difference from its relative scale.

It also demonstrates why precision matters alongside the point estimate. The risk-difference confidence interval, from -0.360 to -0.052, spans a range of plausible contrast magnitudes. The event counts of 7 and 18 are important context for understanding why the estimate should not be treated as exact. A p-value of 0.011 conveys information about compatibility with a null model under test assumptions, but it does not describe the effect's size or establish its cause.

The design raises questions that are common in clinical-trial interpretation. Randomization and a clearly stated follow-up period support a structured comparison, while open-label treatment and unreported details of outcome assessment affect how confidently the infection classification can be interpreted. Reporting the analysis population, missing-data procedures, and original sample-size rationale would further help readers evaluate the strength and limits of the result.

Finally, the planning illustrations show how assumptions about the effect to detect influence participant requirements. Smaller target effects require larger planned groups under the stated assumptions. Such planning calculations are conceptually different from the observed trial result and from a retrospective claim about the trial's power.

17. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record identifies a narrowly defined surgical context: elective colorectal surgery with an abdominal skin incision of at least 6 cm. The findings therefore should not automatically be generalized to other surgical procedures or wound settings. The outcome follow-up is limited to postoperative day 30, and results beyond that period are not reported.

The trial was open label, with neither investigators nor participants blinded after randomization. The registry does not report whether infection assessors were blinded, how surgical site infection was defined beyond monitoring whether antibiotics were needed, or whether outcome decisions were independently adjudicated. These omissions matter because the primary outcome involves clinical assessment.

The analysis population is described as participants treated according to their randomized group and according to protocol. The registry does not explain why the analyzed group sizes differ from the stated enrollment, report participant flow, describe missing outcomes, or specify how protocol deviations were handled. It also does not provide baseline characteristics, adjusted comparisons, or sensitivity analyses.

The record does not report the original sample-size rationale, trial-specific statistical plan, random-sequence method, allocation concealment, site count, or multiplicity strategy. Its planning illustrations are based on the observed effect and should not be confused with the original design. Adverse-event reporting is also limited: the nature of the single other adverse event is not stated, and death counts are not reported in the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Study Looking at the Effect of Silverlon on Post Operative Wound Infections — NCT01143883.
• Registry record last updated 2013-06-13; status last verified 2013-06.
• Results first posted 2013-06-13.
• 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.

21. Record Summary

This completed randomized, controlled, parallel-group trial evaluated Silverlon® versus standard postoperative gauze dressing after elective colorectal surgery. The registry lists enrollment of 110 and primary completion in 2010-09. Neither investigators nor participants were blinded after randomization.

The primary endpoint was surgical site infection from the day of surgery through postoperative day 30. Reported infection percentages were 13.0% for Silverlon and 33.0% for standard dressing. The unadjusted risk difference was -0.206, with a 95% confidence interval from -0.360 to -0.052 and p = 0.011. Serious adverse events were listed as 0 in each group.

Details of the original sample-size rationale, missing-data handling, infection classification, and multiplicity plan are not reported in the registry record.