Role of Vacuum Assisted Closure (VAC) Device in Postoperative Management of Pelvic and Acetabular Fractures: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Role of Vacuum Assisted Closure (VAC) Device in Postoperative Management of Pelvic and Acetabular Fractures (NCT00635479), a randomized na study. The primary outcome is Number of Participants With Wound Infections.

2. Clinical Question

This is a comparison of postoperative wound-management strategies, not a comparison of fracture treatments. The registry describes randomized allocation to parallel groups and reports no masking. The primary outcome is a participant count: it records whether participants were reported as having wound infections, rather than the number of separate infection episodes or the time until an infection occurred.

The posted outcome counts are 5 participants among 49 in the VAC Device group and 2 among 42 in the Gauze Dressing group. Those counts describe the observed groups; by themselves, they do not establish that the dressing strategy caused a difference. The comparison also needs to be read alongside its uncertainty, the registry’s reporting gaps, and the way the groups were followed.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. The comparison is between a VAC device and traditional gauze dressing in postoperative management of pelvic and acetabular fractures. The gauze group is described as receiving daily dressing changes. The registry lists University of Missouri-Columbia as the sponsor.

The record gives an enrollment of 115 and marks the study as completed. The recorded study start is 2008-03, and primary completion is listed as 2013-09. These dates describe the registry record; they do not give the timing of each participant’s follow-up or explain the overall course of recruitment.

The primary outcome is the number of participants with wound infections, with a timeframe of until wound healed, up to 1 year. Outcome counts are reported for 49 participants in the VAC Device group and 42 in the Gauze Dressing group. The registry does not explain how those outcome counts relate to the enrollment figure, or report participant flow, withdrawals, or the number assessed at each follow-up point. Those details are not reported in the registry record.

Random assignment is intended, in general, to make groups comparable at the start of a trial, including for factors that are not measured. It does not guarantee that all prognostic factors will be balanced in a particular trial, especially when group sizes are limited. With no masking reported, participants and care teams may have known the assigned wound-management strategy; the registry does not specify which people, if any, were masked to outcome assessment.

The registry’s stated purpose includes comparing surgical wound drainage, infections, hospital stay, and cost effectiveness. It posts one primary outcome measure, wound infections, and does not post secondary outcome results. Hospital-stay and cost-effectiveness findings are not reported in the registry record. The original sample-size rationale, details of the randomization process, and full trial protocol are also not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Wound Infections, measured over Until wound healed, up to 1 year.

The primary endpoint is the number of participants with wound infections. It is a binary outcome at the participant level: a participant is counted as having an event or not, rather than contributing a count of every infection episode. The registry defines the observation period as until the wound healed, up to 1 year.

In general, a participant-level infection outcome is useful because infection is a clinically relevant postoperative event and can be compared across assigned groups. Counting participants rather than episodes also avoids treating repeated episodes in one person as if they came from different people. The outcome does not, by itself, describe infection severity, duration, treatment, or the timing of infection.

The registry reports 5 participants with wound infections in the VAC Device group, with 49 in that group, and 2 in the Gauze Dressing group, with 42 in that group. It does not provide an outcome definition, diagnostic criteria, adjudication process, or separate follow-up duration for each participant. Those details are not reported in the registry record, so the endpoint’s operational definition cannot be assessed from the posted information.

Although the registry’s stated study purpose also refers to surgical wound drainage, hospital stay, and cost effectiveness, no results for those outcomes are posted. The infection count therefore addresses only one part of the broader stated purpose.

7. Results Posted in the Registry

• Gauze Dressing: 4.8% (2/42) versus 10.2% (5/49) on control; risk difference -5.4 percentage points (95% CI -16.1 to 5.2), risk ratio 0.47 (0.10–2.28); unadjusted two-proportion z-test p = 0.331.

8. Statistical Interpretation

9. Statistical Methods Explained

The registry presents a binary primary outcome: the number of participants with wound infections. In general, a binary outcome classifies each participant into an event or no-event category for the outcome being assessed. The event counts and group sizes are the ingredients for comparing the observed frequency of events between groups. The registry reports 5 events among 49 participants assigned to VAC Device and 2 among 42 assigned to Gauze Dressing.

What does randomization contribute?

Randomization assigns participants to groups using a chance process. In general, this can reduce systematic differences in baseline factors between groups and makes a causal interpretation more credible than an uncontrolled comparison. Randomization does not ensure that groups will be identical, and it cannot correct for biased outcome measurement, incomplete follow-up, or analyses that exclude participants in a way related to their outcomes. The record says allocation was randomized but does not report the sequence-generation method, concealment procedures, or implementation details.

What does an unadjusted comparison mean?

The registry reports an unadjusted comparison, meaning the reported comparison is not described as adjusted for other participant characteristics or prognostic factors. An unadjusted comparison is often straightforward to interpret, but any chance imbalance in important factors can affect a result. The posted p-value is 0.331. The registry does not report a separate adjusted model or analysis details beyond the posted summary statistics.

In general, a p-value evaluates how unusual data at least as inconsistent with a specified null model would be if that model and the analysis assumptions held. It is not a measure of effect size, a probability that the result occurred by chance, or proof of no effect. The estimate and interval convey information about the range of effects compatible with the data, while the p-value addresses compatibility with a particular null value. Both depend on the quality and completeness of the underlying data.

How should risk differences and relative measures be understood?

A risk difference expresses the contrast between the groups’ event frequencies on an absolute scale. A relative risk compares those frequencies as a ratio, while an odds ratio compares event odds. These measures answer related but different questions: absolute differences describe how far apart the group frequencies are, and relative measures describe their proportional contrast. The registry reports all three kinds of comparison. For the risk difference, the interval includes zero; for the relative measures, the reported intervals include one, their no-difference value. These features indicate that the data do not pin down a single direction of effect with precision.

The registry does not specify the confidence level attached to the posted intervals, so no confidence level is assigned. In general, a confidence interval is a range constructed by a statistical procedure that, under its assumptions and repeated use, has a stated coverage property. It is not a range that guarantees the true effect lies within its endpoints. Its width reflects statistical uncertainty, which can be substantial when event counts are limited.

What is not described about the analysis?

The record does not report the analysis population, the handling of missing outcomes, a prespecified statistical plan, an analysis adjusted for other variables, or whether any interim analyses were planned or performed. It also does not describe the method used to calculate the posted interval or p-value. These details are not reported in the registry record. They matter because different analysis choices can lead to different estimates or uncertainty assessments, particularly if participants are omitted or outcome information is incomplete.

The trial is described as unmasked. In general, knowledge of treatment assignment can influence care, reporting, or outcome assessment, depending on the outcome and safeguards. The registry does not say whether wound infections were assessed using standardized criteria or independently adjudicated, nor whether outcome assessors were masked. The absence of those details does not demonstrate that assessment was biased; it limits the ability to evaluate that possibility.

The posted data support a descriptive comparison of the recorded group counts and the registry’s unadjusted statistical summary. They do not allow an independent reconstruction of the full analysis or assessment of its prespecified status. The original statistical analysis plan and the trial’s original sample-size assumptions are not reported in the registry record.

10. Confidence Intervals and Precision

The primary comparison is imprecise. The posted risk-difference interval includes zero, while the reported relative-risk and odds-ratio intervals include one. Those are the respective values representing no group difference. Because the intervals extend to values on either side of those reference points, the data are compatible with effects in either direction rather than establishing a single direction.

In general, a confidence interval describes uncertainty around an estimate under the statistical method used. A narrower interval indicates greater precision for that method; a wider interval indicates that a broader range of effects remains compatible with the data. Intervals do not account automatically for limitations such as incomplete follow-up, outcome misclassification, or bias in who was included in an analysis.

Here, the observed event counts are small: 5 participants in the VAC Device group and 2 in the Gauze Dressing group. With limited event information, estimates can be sensitive to a small number of outcome classifications. The registry does not report the confidence level or calculation method for the intervals, so their construction cannot be independently assessed from the record.

The unadjusted p-value is 0.331. It should not be read as proof that there is no difference, nor as proof that one approach is preferable. The interval and counts communicate the central statistical limitation: the posted comparison does not estimate the group contrast precisely enough to rule out meaningful differences in either direction. The registry does not specify what magnitude of difference would be clinically important.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They illustrate how many participants per arm a future study might plan for under the listed assumptions and effect scenarios; they are not a description of the number enrolled in this trial. The planning calculation uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect.

For planning at 100% of the observed effect, the figures are 366 participants per arm for 80% power and 490 participants per arm for 90% power. At 75% of the observed effect, the corresponding figures are 706 participants per arm for 80% power and 944 participants per arm for 90% power. At 50% of the observed effect, the figures are 1,708 participants per arm for 80% power and 2,286 participants per arm for 90% power.

In plain terms, the 80% power column gives the planning size associated with an 80% chance of detecting the specified effect under the calculation’s assumptions, if that effect is real and the model applies. The 90% power column uses a higher target chance of detecting that specified effect. These are planning illustrations computed from the observed effect, not observed power from the completed trial.

The figures increase as the assumed effect becomes smaller. In general, smaller differences are harder to distinguish from random variation, so detecting them with the same power and significance threshold requires more participants. These figures should not be treated as the trial’s original design target: the original sample-size assumptions and justification are not reported in the registry record.

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 = 0.102; treatment proportion p₁ = 0.048; average p̄ = 0.075.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3721 = 0.7293.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3701 = 0.3115.
4. n = (0.7293 + 0.3115)² / (-0.0544)² = 365.8, rounded up to 366 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 <- 0.102040816326531                          # control proportion
p1 <- 0.0476190476190476                          # 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(635479)
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 = 366 (80% power), 490 (90% power)
 75% of observed effect: n per arm = 706 (80% power), 944 (90% power)
 50% of observed effect: n per arm = 1,708 (80% power), 2,286 (90% power)
power.prop.test: 365.8 
Simulated power at n = 366 per arm: 0.811 (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 measure, wound infections, and reports no secondary outcome results. Its broader stated purpose includes surgical wound drainage, hospital stay, and cost effectiveness, but results for those outcomes are not reported in the registry record. The record does not identify additional prespecified outcomes beyond the single posted primary measure.

Multiplicity arises in general when multiple outcomes, comparisons, time points, or analyses are tested. Considering many tests can increase the chance of at least one apparently notable finding, unless the analysis plan accounts for that multiplicity or clearly distinguishes confirmatory from exploratory analyses. The registry does not report whether additional tests were conducted, whether a multiplicity adjustment was planned, or how the primary outcome was selected. No adjustment should be assumed from the posted information.

Missing-data handling is also not described. The primary outcome groups include 49 participants for VAC Device and 42 for Gauze Dressing, while enrollment is listed as 115. The record does not provide participant flow or reconcile these figures. It does not state how many participants had complete outcome information, whether any outcomes were missing, how missingness was defined, or whether imputation or another method was used. Those details are not reported in the registry record.

The analysis population is not described. In general, an intention-to-treat analysis compares participants according to their randomized assignment, regardless of subsequent treatment changes, while other analysis populations may apply different inclusion rules. The registry does not say which population produced the posted comparison, whether participants crossed between groups, or whether all randomized participants were analyzed. It is therefore not possible to identify the analysis approach from the posted record.

The record does not report a statistical analysis plan, interim-analysis procedures, or prespecified rules for stopping or interpreting results. These omissions do not establish that such procedures were absent; they mean they are not reported in the registry record. They limit assessment of whether the posted analysis follows decisions made before outcomes were known.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: infection (20.4%), implant failure (4.1%), pneumonia (2.4%), cva (2.4%), dvt (2.4%).

The registry reports serious adverse events affecting 15 participants among 49 in the VAC Device group and 9 among 42 in the Gauze Dressing group. It also reports other adverse events affecting 3 participants among 49 in the VAC Device group and 5 among 42 in the Gauze Dressing group. These are adverse-event summaries, distinct from the primary wound-infection endpoint.

The listed serious-event terms include infection at 20.4%, implant failure at 4.1%, and Pneumonia, CVA, DVT, and PE at 2.4% each. The registry does not clarify in this summary whether these term percentages are calculated across all participants, whether categories can overlap, or how the terms map to the treatment groups. They should not be interpreted as group-specific comparisons or as evidence that a particular event was caused by an assigned dressing strategy.

In general, adverse-event counts describe events recorded during the study period; they do not by themselves establish causation. The record does not report death counts, so deaths are not reported in the registry record. It also does not provide event timing, severity beyond the serious classification, relatedness assessments, or detailed safety-analysis methods.

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

The registry reports wound infections in 5 participants among 49 in the VAC Device group and 2 among 42 in the Gauze Dressing group. The unadjusted comparison has p = 0.331, and the reported intervals include the no-difference values for the absolute and relative comparisons. Taken together, the posted data describe fewer observed infections in the gauze group, but leave substantial uncertainty about the size and direction of the underlying difference.

This result does not establish that either dressing strategy causes more or fewer infections. It also does not establish equivalence. A non-significant p-value is not proof that groups are the same, and an interval that crosses the no-difference value can still include potentially important differences in either direction. The registry does not state what difference would be clinically meaningful.

The result concerns only the posted infection endpoint, measured as the number of participants with wound infections until healing, up to 1 year. It does not answer the broader questions about drainage, hospital stay, or cost effectiveness mentioned in the registry’s purpose, because results for those outcomes are not reported in the registry record. It also does not describe infection severity, number of episodes, or time to infection.

Interpretation is constrained by reporting gaps. The record does not reconcile the enrollment figure of 115 with the outcome group counts, describe missing-data handling or the analysis population, or provide the endpoint’s diagnostic criteria. It reports no masking and does not say whether infection assessment was blinded. These limits affect how confidently the comparison can be interpreted, without showing that the result is biased in a particular direction.

The safety summary records serious and other adverse events, but the registry’s aggregate term percentages do not permit a clear treatment-specific safety comparison. The available information is therefore best read as an uncertain, descriptive account of the posted infection outcome and adverse-event counts, rather than a definitive conclusion about comparative effectiveness or safety.

16. Why This Trial Matters Statistically

This trial raises several statistical issues that are common in clinical research. A randomized comparison can support causal inference, but the interpretation depends on transparent reporting of allocation, follow-up, outcome definitions, and analysis populations. The registry identifies randomization and the assigned wound-management strategies, yet does not report the randomization procedures or participant flow.

The primary endpoint is a binary participant-level outcome. That makes the comparison understandable, but the observed event counts are limited and the estimates are imprecise. The interval’s inclusion of the no-difference value is a reminder that an estimate’s direction alone does not settle the question. Precision and uncertainty matter alongside the event counts and p-value.

Reporting of denominators is especially important. The registry gives an enrollment figure and separate outcome-group counts, but does not explain their relationship. Without participant disposition and missing-data details, readers cannot determine how completely the randomized groups are represented in the analysis or assess whether missing outcomes might affect the result.

The registry’s stated purpose is broader than its posted results. It mentions drainage, hospital stay, and cost effectiveness, while posting one primary infection measure and no secondary results. This distinction matters: a statistical conclusion should remain tied to the outcome actually reported, rather than being extended to other clinical or economic questions.

Finally, the safety summary illustrates why event counts require context. Serious-event totals and aggregate event terms are useful descriptive information, but without attribution, timing, group-specific term details, and assessment methods, they do not support strong causal comparisons. Clearer reporting of these elements would make the findings easier to interpret and independently assess.

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.

The primary outcome is reported as a count of participants with wound infections, but the registry does not provide diagnostic criteria, severity definitions, or an adjudication method. It also does not state whether outcome assessors were masked. Since the trial is listed as having no masking, the lack of detail about outcome assessment is relevant when interpreting a potentially judgment-dependent endpoint.

The outcome timeframe is described as until wound healed, up to 1 year, but individual follow-up duration and the handling of participants whose wounds had not healed by the end of observation are not reported. The record also does not provide participant flow, withdrawals, crossovers, or reasons for missing outcome information. The enrollment figure of 115 is not reconciled with the outcome group counts of 49 and 42.

The registry lists hip fractures among the conditions, while the intervention and arm descriptions focus on pelvic and acetabular fractures. It does not clarify whether participants with hip fractures were included in the treatment comparison or how the condition listing relates to eligibility.

The trial’s stated purpose includes wound drainage, hospital stay, and cost effectiveness, but those results are not reported in the registry record. The record does not state the original sample-size rationale, prespecified statistical plan, analysis population, or whether the posted analysis was planned before results were known. It also does not report detailed safety-event attribution or group-specific serious-event terms. These limitations restrict interpretation of the posted comparison and its relevance beyond the recorded infection counts.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Role of Vacuum Assisted Closure (VAC) Device in Postoperative Management of Pelvic and Acetabular Fractures — NCT00635479.
• Registry record last updated 2017-12-11; status last verified 2017-11.
• Results first posted 2014-02-14.
• 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

The registry describes a completed randomized, parallel-group, unmasked trial sponsored by University of Missouri-Columbia. It compares postoperative VAC-device management with traditional gauze dressing for pelvic and acetabular fractures, and lists pelvic, acetabular, and hip fractures as conditions. Enrollment is recorded as 115.

The primary outcome is the number of participants with wound infections until healing, up to 1 year. The registry reports 5 participants with infections in the VAC Device group, among 49, and 2 in the Gauze Dressing group, among 42. The unadjusted comparison reports p = 0.331, with intervals that include the no-difference values.

The record posts no secondary outcome results. Participant flow, missing-data handling, analysis population, infection criteria, and the original design assumptions are not reported in the registry record. The posted infection comparison is therefore uncertain and does not resolve the broader questions about drainage, hospital stay, or cost effectiveness named in the study purpose.