Pre-operative Alcohol Skin Solutions in Fractured Extremities: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pre-operative Alcohol Skin Solutions in Fractured Extremities (NCT03523962), a randomized phase 4 study. The primary outcome is Number of Participants With a Superficial Incisional Surgical Site Infection (SSI).

2. Clinical Question

The clinical question is framed around prevention of surgical site infection after operative care of extremity fractures. The registry describes both open and closed fracture populations, and presents their outcome counts separately. The primary outcome is a count of participants meeting the registry definition, rather than a measure of infection severity or time to infection. An unplanned fracture-related reoperation within 12 months is also posted as a secondary outcome.

The randomized crossover design is relevant to how the comparison should be understood: sites changed from one solution to the other after the first intervention phase. The registry record does not provide a full account of the analysis used to account for that site-level changeover. The posted summaries therefore need to be read in light of the population labels and comparison definitions attached to each estimate, rather than assumed to represent a single pooled contrast.

3. Trial Design

PREPARE is a completed, Phase 4, randomized trial with a crossover model and single masking, sponsored by the University of Maryland, Baltimore. The registry lists enrollment of 8485. The study began on 2018-08-21, and primary completion was recorded as 2023-03-15. The study compares pre-operative alcohol-based antiseptic skin solutions used in extremity fracture surgery.

The registry describes the site process as beginning with sites using their assigned solution for eligible fracture surgeries. After the first intervention phase, each site crossed over to the opposite solution. The arm descriptions indicate that the second solution was used for a two-month period, but the description of the first phase is incomplete. The exact duration and operational details of that phase are not reported in the registry record. The registry also does not explain the masking procedures or identify who was masked.

The intervention list names DuraPrep and ChloraPrep. In contrast, the outcome groups are labeled iodine and chlorhexidine. Those labels are retained when describing the posted results; a product-to-label mapping is not reported in the registry record. The record lists 3 outcome measures, with a primary superficial incisional surgical site infection endpoint and a posted secondary endpoint for unplanned fracture-related reoperation. Analyses for the primary outcome are not listed in the registry's analysis record, and the posted secondary outcome has no reported analyses.

The posted outcome counts are divided into closed-fracture and open-fracture populations and into iodine and chlorhexidine groups. These counts are useful descriptions of the observed data, but the registry's stated comparison definitions matter: the posted risk-difference comparisons use the closed-fracture iodine group as the reference, including comparisons labeled as open-fracture groups. Consequently, the open-fracture comparisons should not be read as direct randomized comparisons between the two solutions within the open-fracture population.

The record gives no further details about the randomization sequence, allocation concealment, cluster structure, analysis population, or methods used to account for sites and crossover periods. Those aspects of the trial's design and analysis are 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.

Before assignment: To ensure wide generalizability to routine practice, the protocol allowed prewashing of the operative extremity with alcohol or other antiseptics before performing the final skin antisepsis with the study solution. In addition to ensuring trial feasibility and protocol adherence, this decision pragmatically allowed the intact skin to receive mechanical scrubbing or partial alcohol antisepsis at the treating surgeon's discretion.

Closed Fractures

Reasons for not completing this period:

Open Fractures

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Outcome data for surgical-site infection were missing for 4.5% of the patients in the closed-fracture population and for 2.8% of those in the open-fracture 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 Number of Participants With a Superficial Incisional Surgical Site Infection (SSI), measured over Within 30 days of the patient's last planned fracture management surgery.

The primary endpoint counts participants with a superficial incisional surgical site infection. The registry sets the observation window as within 30 days of the patient's last planned fracture management surgery. Its stated criteria follow the CDC National Healthcare Safety Network reporting criteria from 2017. The event must involve only skin and subcutaneous tissue of the incision, and it may be identified through purulent drainage, a positive microbiologic test from an appropriate specimen, an incision deliberately opened by a surgeon with specified signs or symptoms, or a surgeon's diagnosis of superficial incisional infection.

This endpoint is used because infection of the incision is a relevant postoperative outcome and can be defined using clinical and laboratory findings. The criteria combine several ways an event may be recognized, rather than requiring one single test. That makes the case definition dependent on the clinical documentation and assessments used at participating sites, as well as on the registry's stated criteria.

The endpoint is a count of participants who met the definition, not a measure of infection duration, treatment burden, or severity. Its timeframe is anchored to the last planned fracture management surgery, so it does not describe an unrestricted period of follow-up. The registry reports that outcome data were missing for 4.5% of patients in the closed-fracture population and 2.8% of those in the open-fracture population. How missing outcome observations were handled in the trial's own analysis is not reported in the registry record.

7. Results Posted in the Registry

• Closed-Fracture Population Chlorhexidine Group: 0.8% (27/3272) versus 0.6% (20/3205) on control; risk difference 0.2 percentage points (95% CI -0.2 to 0.6), risk ratio 1.32 (0.74–2.35); unadjusted two-proportion z-test p = 0.340.
• Open-Fracture Population Iodine Group: 0.7% (6/825) versus 0.6% (20/3205) on control; risk difference 0.1 percentage points (95% CI -0.5 to 0.7), risk ratio 1.17 (0.47–2.89); unadjusted two-proportion z-test p = 0.741.
• Open-Fracture Population Chlorhexidine Group: 1.1% (9/826) versus 0.6% (20/3205) on control; risk difference 0.5 percentage points (95% CI -0.3 to 1.2), risk ratio 1.75 (0.80–3.82); unadjusted two-proportion z-test p = 0.158.

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.

Number of Participants With an Unplanned Fracture-Related Reoperation

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Closed-Fracture Population Chlorhexidine Group: 5.9% (179/3047) versus 5.5% (164/2982) on control; risk difference 0.4 percentage points (95% CI -0.8 to 1.5), risk ratio 1.07 (0.87–1.31); unadjusted two-proportion z-test p = 0.530.
  • Open-Fracture Population Iodine Group: 16.1% (126/784) versus 5.5% (164/2982) on control; risk difference 10.6 percentage points (95% CI 7.9 to 13.3), risk ratio 2.92 (2.35–3.64); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Closed-Fracture Population Chlorhexidine Group and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Open-Fracture Population Iodine Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary endpoint concerns unplanned fracture-related reoperation within 12 months of the patient's last planned operation. Across its closed- and open-fracture groupings, the observed event pattern is not uniform. That pattern adds context about a different outcome, but it should not be treated as confirmation or contradiction of the primary infection result: reoperation and superficial incisional infection are distinct endpoints, measured over different follow-up windows.

The registry posts unadjusted comparisons for the secondary outcome, but it does not list trial analyses for it. As with the primary outcome, the comparison definitions require careful reading. The open-fracture iodine comparison uses the closed-fracture iodine group as the reference. It therefore does not estimate the solution contrast among open-fracture participants. The closed-fracture comparison is more directly aligned with a within-population contrast in the labels, but the registry still does not report an analysis accounting for the crossover design.

Unadjusted secondary results generally carry less inferential weight than a prespecified, fully described analysis of the primary endpoint. Multiple outcome assessments increase the opportunity for chance findings, and no multiplicity adjustment or hierarchy for interpreting secondary outcomes is reported in the registry record. The secondary endpoint can be informative as a descriptive outcome, but its p-value should not be read in isolation or used to settle the primary question.

The displayed secondary data therefore broaden the outcome picture without resolving the uncertainty in the primary comparison. The registry does not provide enough information to assess whether reoperation was analyzed according to a prespecified plan, how missing follow-up was treated, or how site and period structure were handled. Those gaps limit the strength of any conclusion drawn from the secondary summaries.

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

• Number of Participants With an Unplanned Fracture-Related Reoperation

9. Statistical Interpretation

10. Statistical Methods Explained

The outcomes are binary at the participant level: a participant either met the outcome definition during the specified follow-up window or did not. The counts and group sizes describe the number with an event and the number in each labeled group. For superficial incisional surgical site infection, the record also notes missing outcome data in both fracture populations, so the posted counts should be read alongside that missingness information.

What does a risk difference express?

A risk difference expresses the difference between the event proportions in two groups. A value of zero corresponds to equal proportions; positive and negative values indicate opposite directions according to the subtraction order used. It is an absolute contrast, rather than a relative measure. The posted primary closed-fracture risk difference is 0.002. Its confidence interval covers values on both sides of zero, so the data do not determine the direction of the contrast with precision.

Risk differences are often intuitive because they retain the event scale of the outcome. Their interpretation nevertheless depends on which groups are compared and in what order. Here, the comparison labels and reference groups are especially important. The posted open-fracture comparisons use the closed-fracture iodine group as the reference, rather than an iodine or chlorhexidine group from the open-fracture population. A contrast that mixes fracture populations cannot be treated as an isolated antiseptic comparison within one fracture stratum.

What do relative measures add?

The registry also posts relative risk and odds ratio summaries. A relative risk compares event proportions as a ratio, while an odds ratio compares the odds of the event. These relative measures can convey the size of an association on a different scale from the risk difference. When events are uncommon, the two relative measures may be numerically similar, but they remain distinct quantities. Their interpretation still depends on a valid and clearly defined comparison. They do not correct a comparison that mixes populations or account for the crossover design by themselves.

Confidence intervals describe the range of values compatible with the data under the statistical method used, subject to its assumptions. An interval that spans the null value—zero for a risk difference and one for a ratio measure—does not establish that the groups are equivalent. It indicates that the estimate has uncertainty that includes the null and other possible effects. The exact trial-analysis method behind the registry's posted intervals is not reported in the registry record.

What does an unadjusted p-value tell the reader?

A p-value evaluates how unusual data at least as inconsistent with a null hypothesis would be under that hypothesis and the statistical model used. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. The p-values posted for these contrasts are labeled unadjusted. They do not account for multiple comparisons unless a multiplicity procedure is separately stated, and no such procedure is reported in the registry record.

For the primary closed-fracture contrast, the unadjusted p-value is 0.34. This does not establish equality between groups. A result may be compatible with no difference while remaining compatible with effects in either direction, particularly when the interval is broad. Interpretation should therefore consider the estimate and interval, the comparison definition, outcome missingness, and the design—not a threshold alone.

Why does the crossover design matter?

In a crossover design, the same site or unit receives different interventions in successive periods. Outcomes may be affected by the intervention, the period, characteristics of the site, and changes over time. A suitable analysis may need to account for those features, depending on the randomization and data structure. The registry describes sites switching to the opposite solution but does not report the statistical model or whether period and site effects were addressed. General statistical considerations about crossover designs do not establish what the trial investigators actually did.

Likewise, the record does not state whether comparisons were adjusted for other factors, whether standard errors accounted for clustering, or how the analysis population was defined. The label “unadjusted” indicates that the posted recalculations are simple contrasts from the displayed summary statistics, not the trial's full adjusted analysis. No primary trial analysis is listed in the registry record, and the sponsor's own analysis cannot be compared with these calculations from the available information.

For uncommon binary outcomes, relatively small event counts can leave substantial uncertainty even when group sizes are large. General statistical reasoning explains why the confidence interval may be more informative than a simple significance label: it shows both the estimated direction and the range of effects that remain compatible with the data. This is particularly relevant for the open-fracture infection counts, where the number of recorded events is limited. The registry does not report a separate model for sparse data, so none should be assumed.

11. Confidence Intervals and Precision

Precision is conveyed primarily by the confidence intervals around the posted risk differences. The interval for the closed-fracture primary comparison extends across zero, from a small negative value to a small positive value. That means the posted data are compatible with no difference and with contrasts in either direction. The point estimate alone does not capture that uncertainty.

The open-fracture infection groups have fewer recorded events than the closed-fracture groups. With fewer events, estimates can be especially uncertain, even when the numbers of participants in the groups are substantial. The posted open-fracture intervals also span zero. However, because those comparisons use the closed-fracture iodine group as the reference, their width is not the only issue: the contrast itself does not isolate the solution difference within the open-fracture population.

Confidence intervals are not guarantees that the true effect lies within the interval, and they do not describe all sources of uncertainty. Their interpretation depends on the statistical model and the comparison being estimated. The registry does not report the method used for the trial's own analysis, so the precision of that analysis cannot be assessed from the record.

Missing primary outcome data are reported for 4.5% of patients in the closed-fracture population and 2.8% in the open-fracture population. The record does not describe the missing-data method or show how alternative assumptions about missing outcomes would affect the estimates. Thus, the intervals around the posted calculations should not be taken to address uncertainty arising from missingness or unreported design adjustments.

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 illustrative sample sizes for future studies based on the observed effect sizes in the posted results. For these binary participant-count outcomes, the numbers are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario asks how many participants per arm would be needed to detect a stated fraction of the observed effect.

The 80% power column describes a design that, under its assumptions and if the specified effect is real, would have an 80% chance of producing a statistically significant result. The 90% power column describes the corresponding design with a 90% chance. These are design probabilities for hypothetical future studies; they do not describe the probability that the current trial found a true effect. The figures are not observed power.

Rows that plan for 100% of the observed effect use the full observed contrast as the target. Rows that plan for 75% or 50% of that effect target smaller contrasts. Detecting a smaller effect generally requires more participants, which is why the figures increase as the target fraction decreases. This relationship is a general feature of study planning, not evidence that the smaller effects are present.

The registry record does not report the original trial's sample-size assumptions or justification. The posted planning figures are therefore not a reconstruction of the PREPARE trial's design target. They should be treated as illustrations, especially given that the underlying contrasts are unadjusted and the open-fracture comparisons do not represent a within-population solution contrast. For analyses of time-to-event outcomes, the planning convention would be total events, but the displayed outcomes are participant counts for binary events.

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 = 0.006; treatment proportion p₁ = 0.008; average p̄ = 0.007.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1199 = 0.2351.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1199 = 0.1009.
4. n = (0.2351 + 0.1009)² / (0.0020)² = 27,905.2, rounded up to 27,906 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 <- 0.0062402496099844                          # control proportion
p1 <- 0.0082518337408313                          # 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(3523962)
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 = 27,906 (80% power), 37,357 (90% power)
 75% of observed effect: n per arm = 47,901 (80% power), 64,125 (90% power)
 50% of observed effect: n per arm = 103,930 (80% power), 139,133 (90% power)
power.prop.test: 27905.2 
Simulated power at n = 27,906 per arm: 0.805 (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 3 outcome measures, but only the primary outcome and one secondary outcome have results described in the available record. The additional outcome details and its results are not reported in the registry record. The record also lists no trial analyses for the primary outcome and no reported analyses for the posted secondary outcome. Thus, it is not possible to determine from the registry whether the posted comparisons match a prespecified analysis plan.

Multiple statistical comparisons can increase the chance of at least one apparently notable result arising by chance. A prespecified hierarchy, adjustment procedure, or other strategy can guide interpretation when several outcomes or contrasts are examined. Such a strategy is not reported in the registry record. The posted p-values are unadjusted, so they should be treated as individual descriptive tests rather than as evidence that accounts for all outcomes and comparisons.

For the primary endpoint, the record states that outcome data were missing for 4.5% of patients in the closed-fracture population and 2.8% of those in the open-fracture population. The registry does not report whether missing outcomes were excluded, imputed, or handled in another way in the trial analysis. It also does not give reasons for missingness or an analysis of whether missingness differed by treatment group. Missing outcomes can affect both the event counts and the interpretation of comparisons, so the posted missingness percentages are relevant context.

The record does not specify the populations used for the primary and secondary analyses, including whether all randomized participants were retained in their assigned groups. The denominators differ between the infection and reoperation summaries, but the reasons for those differences are not reported. Nor does the record describe a protocol for handling crossover periods, site-level allocation, or departures from the assigned solution. These omissions prevent a detailed assessment of the analysis population and the relationship between the posted estimates and the randomized design.

These are reporting limitations: the absence of information in the registry does not prove that a method was not used. It does mean that the method cannot be evaluated from the registry record.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: study fracture related complication (23.2%), other (12.3%), non-study fracture related complication (4.7%), pulmonary (3.4%), cardiac (2.6%).

The serious adverse event summaries give the number at risk and the number affected in each of the four fracture-by-solution groups. For the closed-fracture groups, 1177 of 3360 in the iodine group and 1212 of 3425 in the chlorhexidine group were affected by a serious adverse event. For the open-fracture groups, the corresponding counts are 430 of 854 and 368 of 846. Death counts are also listed separately: 145 and 140 in the closed-fracture groups, and 13 and 13 in the open-fracture groups.

The registry lists no participants at risk and none affected in the other-adverse-event fields. This should be read as the content of those fields, not as proof that no non-serious events occurred. The record does not provide a causal assessment of the serious events or explain whether they were considered related to the skin-preparation solution.

The most frequently listed serious-event terms include Study Fracture Related Complication at 23.2% and Other at 12.3%, followed by Non-Study Fracture Related Complication at 4.7%, Pulmonary at 3.4%, Cardiac at 2.6%, and Renal at 2.6%. These are event-term summaries, not randomized treatment-effect estimates. The registry does not report an adjusted safety comparison or explain the denominator underlying each term percentage.

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

The posted results describe observed participant counts and unadjusted contrasts for superficial incisional surgical site infection and unplanned fracture-related reoperation. For the primary closed-fracture comparison, the estimate is close to zero on the risk-difference scale and its interval includes zero. This means the posted estimate is uncertain; it does not demonstrate that the solutions are equivalent or that there is no difference.

The open-fracture infection counts are small in relation to the group sizes, and the posted open-fracture contrasts use the closed-fracture iodine group as their reference. They therefore cannot be interpreted as direct randomized comparisons of iodine and chlorhexidine among open-fracture participants. The endpoint results also include missing observations, and the handling of those observations is not reported in the registry record.

The distinction between a result that is not statistically significant and a result showing no meaningful effect is important. A non-significant p-value can occur when the true difference is small, when the data are imprecise, or when the analysis does not fully reflect the design. The available record does not identify which explanation is most relevant. General statistical interpretation cannot replace information about the trial's planned analysis, which is not reported in the registry record.

The trial is described as randomized and crossover, but the posted summaries do not document how site and period structure were handled. Because the record does not report the trial's own analysis, the displayed unadjusted estimates should not be treated as definitive causal estimates. They are useful for describing the posted data and the uncertainty around selected contrasts, subject to the comparison definitions.

These findings do not establish that either solution works or does not work. They also do not support medical advice for an individual patient. They show what the registry reports for the specified populations and time windows, while leaving important questions about analysis, missing data, multiplicity, and the crossover design unresolved.

17. Why This Trial Matters Statistically

This trial raises statistical issues that commonly arise when a randomized clinical study has a crossover structure but the posted results are organized as group counts. The population labels, reference groups, and unit of randomization determine what a contrast means. In this record, comparisons labeled as open-fracture results use the closed-fracture iodine group as their reference. Recognizing that detail prevents those estimates from being mistaken for direct treatment comparisons within the open-fracture population.

The primary endpoint is clinically defined but depends on documented signs, laboratory findings, or a surgeon's diagnosis. The registry's definition sets a specific follow-up window and reports missing outcome data in both fracture populations. Those features matter when judging how complete and comparable outcome ascertainment was across groups.

Precision also matters. Event counts are modest for the infection outcome, and the posted primary interval spans zero. A single p-value cannot communicate the full uncertainty or establish equivalence. The planning illustrations further show how a future study's required participant numbers depend on the effect size it aims to detect, but they are not the original trial's design justification.

Finally, the registry record does not include the investigators' analysis for the outcomes discussed. Without details of the analysis population, crossover-period handling, site effects, and multiplicity strategy, readers cannot fully connect the simple posted contrasts to the randomized design. The statistical lesson is not that the trial has no value; it is that transparent reporting of estimands and analysis methods is essential for correctly interpreting trial results.

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 principal limitation is incomplete reporting of the analysis. The record describes randomized crossover allocation but does not report the trial's own outcome analyses, analysis populations, or methods for accounting for site and period. The posted comparisons are unadjusted, and their relationship to the trial's design is not fully documented.

Some comparison definitions also limit interpretation. The open-fracture comparisons use the closed-fracture iodine group as the reference, so they do not isolate the antiseptic contrast within the open-fracture population. The intervention list names DuraPrep and ChloraPrep, whereas the outcome groups use iodine and chlorhexidine; the mapping between those labels is not stated.

Primary outcome data were missing for 4.5% of the closed-fracture population and 2.8% of the open-fracture population. The registry does not report how missingness was handled, why observations were missing, or whether missing-data sensitivity analyses were performed. The reoperation denominators differ from the infection denominators, but the reasons are not reported.

The record does not report the original sample-size assumptions, the multiplicity strategy, details of masking, or a complete account of the crossover period schedule. The first-phase description is incomplete. These limitations do not establish that the trial investigators failed to address these issues; they mean that the registry record does not allow them to be evaluated.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pre-operative Alcohol Skin Solutions in Fractured Extremities — NCT03523962.
• Registry record last updated 2024-10-04; status last verified 2024-09.
• Results first posted 2024-10-04.
• 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

PREPARE is a completed, Phase 4 randomized crossover trial sponsored by the University of Maryland, Baltimore, with enrollment of 8485. It compared pre-operative antiseptic skin solutions in extremity fracture surgery, with sites switching to the opposite solution after the first intervention phase. The registry lists DuraPrep and ChloraPrep as interventions and labels the outcome groups iodine and chlorhexidine.

The primary outcome is the number of participants with superficial incisional surgical site infection within 30 days of the last planned fracture management surgery. A secondary outcome counts participants with unplanned fracture-related reoperation within 12 months of the last planned operation. The posted primary comparisons are unadjusted, and no trial analyses are listed for the outcomes discussed. Open-fracture comparisons use the closed-fracture iodine group as the reference, limiting their interpretation as solution contrasts within open fractures. Missing primary outcome data are reported, but their handling is not described. The registry record does not report the trial's original sample-size assumptions or detailed analysis plan.