Efficacy and Safety Study of Fibrin Sealant With 4 IU/mL Thrombin, Vapor Heated, Solvent Detergent Treated (FS VH S/D 4) in Face-Lift Procedures: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of Fibrin Sealant With 4 IU/mL Thrombin, Vapor Heated, Solvent Detergent Treated (FS VH S/D 4) in Face-Lift Procedures (NCT00708071), a randomized phase 2 study. The primary outcome is Visual Comparison of Ecchymosis at Postoperative Day 3.

2. Clinical Question

The question is comparative and specific to early postoperative bruising as assessed from photographs. It is not a general comparison of all aspects of recovery, nor does the primary outcome directly measure the amount of bruising with a physical instrument. The registry record identifies the study as exploratory Phase 2 and describes efficacy and safety as objectives. It does not report a separate clinical threshold for what would constitute an important difference in the visual assessment.

3. Trial Design

The registry record describes a randomized, single-masked, Phase 2 study with a single-group model and 45 participants enrolled. The intervention description specifies a within-person, split-face comparison: one side received FS VH S/D 4 and the other side received standard of care. This structure lets the comparison use observations from both sides of a participant, but the posted outcome counts alone do not show which individual participants had each side-specific outcome. Details of how treatment side was assigned are not reported in the registry record.

The study was sponsored by Baxter Healthcare Corporation and is listed as completed. The recorded start was 2008-06, and primary completion was 2008-09. The primary endpoint was a visual comparison of ecchymosis through postoperative day 3, based on standard digital photographs reviewed by five separate blinded reviewers. The primary analysis population is described as per protocol. If no majority of reviewers agreed on the comparison, that assessment did not contribute to the analysis.

Additional outcomes included visual comparisons at postoperative days 1, 5, 7, 10, and 14, as well as comparisons of modified Marchac ecchymosis grades assessed by five independent, blinded reviewers at days 1, 3, and 5. The registry lists 35 outcome measures and 26 analyses overall; 33 secondary outcomes are posted. The detailed analysis plan, original sample-size justification, and reasons for the difference between enrollment and the primary outcome count are not reported in the registry record.

Although the registry identifies randomization and single masking, it does not describe the sequence-generation procedure, concealment, or the identity of the masked parties. The reviewer blinding is explicitly described for the photographic primary assessment and some modified Marchac assessments. Broader masking details 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: 56 participants were enrolled and screened. 2 were screen failures. 9 were withdrawn prior to randomization (1 due to untoward medical occurrence, 2 due to study site over enrollment, 2 requested withdrawal, 2 had scheduling conflicts, 1 had surgery delayed, 1 missed deadline for enrollment. Therefore, 45 of the 56 enrolled were randomized.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Per Protocol. If there is no majority (i.e., 3 or more in agreement) in the outcomes of the visual comparison of both sides of the face from the 5 blinded reviewers then the assessment will not contribute to the analysis.

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 Visual Comparison of Ecchymosis at Postoperative Day 3, measured over Through Postoperative Day 3.

The primary endpoint is the number of participants whose photographs were judged to show less ecchymosis on one side of the face than on the other through postoperative day 3. Reviewers compared the FS VH S/D 4-treated side with the SoC-treated side using standard digital photographs. The registry says five separate blinded reviewers made the assessments. An assessment contributed to the per-protocol analysis only when at least three reviewers agreed; without that majority, it was excluded.

Ecchymosis is postoperative bruising. A side-to-side visual comparison is useful for this question because each participant serves as their own comparator: participant-level features shared by both sides cannot explain a within-person difference in the same way they could explain a difference between unrelated groups. That is a general design rationale, not evidence that all sources of side-to-side variation are controlled.

The endpoint records which side was judged to have less bruising, along with equal assessments and cases with no ecchymosis on either side. It does not quantify bruise area, color, duration, discomfort, or functional impact. Those measures are not reported as components of this primary outcome. The primary endpoint therefore captures a blinded visual judgment at a specified early time point, rather than a complete account of postoperative recovery.

7. Results Posted in the Registry

• Participants With Less Ecchymosis Treated With FS VH S/D 4: 17.9% (5/28) versus 42.9% (12/28) on control; risk difference -25.0 percentage points (95% CI -48.2 to -1.8), risk ratio 0.42 (0.17–1.03); unadjusted two-proportion z-test p = 0.042.
• Participants With Equal Ecchymosis On Both Sides: 39.3% (11/28) versus 42.9% (12/28) on control; risk difference -3.6 percentage points (95% CI -29.3 to 22.2), risk ratio 0.92 (0.49–1.72); unadjusted two-proportion z-test p = 0.786.
• Participants With No Ecchymosis on Either Side: 0.0% (0/28) versus 42.9% (12/28) on control; risk difference -42.9 percentage points (95% CI -61.2 to -24.5); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Visual Comparison of Ecchymosis at Day 1

• 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:
  • Participants With Less Ecchymosis Treated With FS VH S/D 4: 6.9% (2/29) versus 37.9% (11/29) on control; risk difference -31.0 percentage points (95% CI -51.0 to -11.1), risk ratio 0.18 (0.04–0.75); unadjusted two-proportion z-test p = 0.005.
  • Participants With Equal Ecchymosis On Both Sides: 55.2% (16/29) versus 37.9% (11/29) on control; risk difference 17.2 percentage points (95% CI -8.0 to 42.5), risk ratio 1.45 (0.82–2.57); unadjusted two-proportion z-test p = 0.188.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Participants With Less Ecchymosis Treated With FS VH S/D 4 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Participants With Equal Ecchymosis On Both Sides and the control. The interval gives the range of effects that remain compatible with the data.

Visual Comparison of Ecchymosis at Day 5

• 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:
  • Participants With Less Ecchymosis Treated With FS VH S/D 4: 18.5% (5/27) versus 29.6% (8/27) on control; risk difference -11.1 percentage points (95% CI -33.7 to 11.5), risk ratio 0.62 (0.23–1.67); unadjusted two-proportion z-test p = 0.340.
  • Participants With Equal Ecchymosis On Both Sides: 51.9% (14/27) versus 29.6% (8/27) on control; risk difference 22.2 percentage points (95% CI -3.3 to 47.8), risk ratio 1.75 (0.88–3.47); unadjusted two-proportion z-test p = 0.097.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Participants With Less Ecchymosis Treated With FS VH S/D 4 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Participants With Equal Ecchymosis On Both Sides and the control. The interval gives the range of effects that remain compatible with the data.

Visual Comparison of Ecchymosis at Day 7

• 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:
  • Participants With Less Ecchymosis Treated With FS VH S/D 4: 29.0% (9/31) versus 25.8% (8/31) on control; risk difference 3.2 percentage points (95% CI -19.0 to 25.4), risk ratio 1.12 (0.50–2.53); unadjusted two-proportion z-test p = 0.776.
  • Participants With Equal Ecchymosis On Both Sides: 45.2% (14/31) versus 25.8% (8/31) on control; risk difference 19.4 percentage points (95% CI -4.0 to 42.7), risk ratio 1.75 (0.86–3.57); unadjusted two-proportion z-test p = 0.111.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Participants With Less Ecchymosis Treated With FS VH S/D 4 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Participants With Equal Ecchymosis On Both Sides and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend visual comparisons beyond the primary day 3 assessment, including days 1, 5, 7, 10, and 14, and modified Marchac grade comparisons at days 1, 3, and 5. Across the posted day 1, day 5, and day 7 visual comparisons, the descriptive direction is not uniform: early counts more often favor the FS VH S/D 4 side for the category of less ecchymosis, while the day 7 comparison does not continue that pattern. Equal-ecchymosis classifications are also common. This broad pattern does not establish a consistent time course.

These later assessments provide context for the day 3 primary result, but they do not overturn or clarify the sponsor’s primary paired analysis. They are separate outcome assessments at different times, with denominators that vary across the posted results. The registry’s full numeric results for every listed secondary outcome are not reported in the registry record. A complete trajectory or consistent summary across all secondary measures therefore cannot be inferred from the available details.

Unadjusted secondary results carry less weight because several outcomes and time points are considered. In general, testing many outcomes increases the chance that at least one result will appear noteworthy by chance, even if no underlying effect is present. An adjustment strategy or prespecified hierarchy can address this concern, but a multiplicity procedure is not reported in the registry record. The registry also does not report whether all secondary analyses were prespecified or how missing assessments were handled across time points.

Accordingly, the secondary findings are best treated as exploratory descriptive evidence. They can indicate whether the primary pattern appears to persist or change across follow-up assessments, but the posted information does not support a firm overall conclusion about the course of ecchymosis or a definitive comparison across all measured outcomes.

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

• Visual Comparison of Ecchymosis at Day 1
• Visual Comparison of Ecchymosis at Day 5
• Visual Comparison of Ecchymosis at Day 7
• Visual Comparison of Ecchymosis at Day 10
• Visual Comparison of Ecchymosis at Day 14
• Difference in Marchac Grades Using A Modified Marchac Scale (MMS) of Ecchymosis Between Two Sides of Face Assessed by 5 Independent, Blinded Reviewers- Day 1
• Difference in Marchac Grades Using A Modified Marchac Scale (MMS) of Ecchymosis Between Two Sides of Face Assessed by 5 Independent, Blinded Reviewers- Day 3
• Difference in Marchac Grades Using A Modified Marchac Scale (MMS) of Ecchymosis Between Two Sides of Face Assessed by 5 Independent, Blinded Reviewers- Day 5

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help clarify what a side-to-side result can and cannot tell us. The registry reports a sponsor analysis using McNemar’s method for the primary comparison, while a simple recalculation from the posted summary counts gives a different inferential result. The distinction is especially important because treatment comparisons within the same participant are paired.

What does a paired comparison use?

In a paired design, the relevant information is not only how many participants fall into each category on each side. The analysis also depends on how the two side-specific observations line up within each participant. For example, a paired method distinguishes participants whose outcome favors the treated side from those whose outcome favors the comparator side. The number of participants with equal outcomes contributes differently. This is a general explanation of paired analysis.

McNemar’s method is designed for paired categorical outcomes. For a two-category paired comparison, its evidence is driven by the discordant pairs: participants whose classifications differ between the two conditions. In this study, the registry reports four outcome categories, including “less ecchymosis” on either side and equal ecchymosis. The posted aggregate counts do not include a full participant-level cross-classification of those categories. Therefore, the sponsor’s McNemar result cannot be reconstructed from the marginal counts alone.

What is the recalculated comparison?

The recalculated risk difference is a simple, unadjusted comparison of the proportion classified as having less ecchymosis on the FS VH S/D 4 side with the corresponding proportion classified as having less on the SoC side. It uses the posted counts and denominators, without the pairing information needed for the sponsor’s McNemar analysis. Its p-value and confidence interval are therefore not interchangeable with the sponsor’s paired result. The recalculation is useful as a transparent check on the displayed summary counts, but it is not a reconstruction of the prespecified or sponsor analysis.

In general, a p-value measures how compatible observed data are with a stated null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A smaller p-value is not automatically evidence of a more important effect. Here, the recalculated p-value is unadjusted and differs from the reported paired-analysis p-value; that discrepancy makes the sponsor’s analysis the primary inferential reference.

Why does the confidence interval matter?

A confidence interval expresses uncertainty around an estimated effect under the method used to calculate it. In general, a wider interval indicates less precision, while an interval spanning zero for a difference measure is compatible with effects in either direction as well as no difference under that method. The sponsor’s 95% interval for the difference in proportions runs from -0.04 to 0.49 and includes zero. Its interpretation belongs with the McNemar method and the sponsor’s contrast definition; it should not be combined with the recalculated risk difference as if both came from one analysis.

Confidence intervals also depend on analysis assumptions and data structure. A paired interval should reflect within-participant information. A simple interval based on marginal counts does not capture that structure in the same way. In general, when only aggregate summaries are available, the precision and inferential details of the original paired analysis may not be recoverable.

How does the reviewer rule affect the endpoint?

The primary outcome description sets a majority rule: at least three of the five reviewers must agree, otherwise the assessment does not contribute to the analysis. This produces an analysis based on classifiable reviewer judgments. The rule may help avoid treating a split panel as a decisive side preference, but it can also make the analyzed set differ from the enrolled set. The number excluded under this rule and how those cases were handled in any other analysis are not reported in the registry record.

More generally, blinded assessment can reduce the influence of knowledge about treatment when reviewers interpret images. It does not remove every possible source of measurement variation. Image quality, visible clues, the review procedure, and agreement among raters can affect visual outcomes. The registry specifies standard digital photographs and separate blinded reviewers, but details on image standardization, rater calibration, or reliability statistics are not reported in the registry record.

What should be made of the safety counts?

The registry separates serious adverse events from other adverse events and lists counts by location: localized to the SoC side, localized to the FS VH S/D 4 side, or non-localized. These are descriptive safety counts. In general, counts from a small study can identify events recorded during the study but cannot precisely characterize uncommon risks. The registry does not report enough detail to infer causation, timing, severity beyond the serious/non-serious classification, or a comparative risk estimate.

Finally, an analysis plan can specify endpoint hierarchy, model choice, handling of missing or indeterminate observations, and adjustment for multiple testing. Such details are important when many outcomes are considered. The registry record does not report the full statistical analysis plan, multiplicity adjustment, or original sample-size justification. Any explanation of those methods beyond the explicitly posted McNemar analysis is therefore general rather than a claim about this trial’s original protocol.

11. Confidence Intervals and Precision

The sponsor-reported primary result is a difference in proportions of 0.250, with a 95% confidence interval from -0.04 to 0.49 and p=0.143. The interval includes zero and extends in both directions, so the sponsor’s estimate is not highly precise about the direction or size of the paired difference. In general, a confidence interval gives a range of effects compatible with the data and method at the stated confidence level; it is not a guarantee that the true effect lies within the particular interval.

The posted aggregate counts are based on 28 participants in the primary per-protocol outcome. The sample is small, and the outcome is a categorical visual judgment. The registry does not provide the participant-level paired cross-classification, so the amount of information in discordant pairs cannot be independently assessed from the counts alone. This limits an external reader’s ability to verify the precision calculation for the sponsor’s paired method.

The simple recalculation yields an unadjusted risk difference of -0.25 and p=0.042, but it answers a marginal-count comparison rather than reproducing the sponsor’s paired analysis. Its apparent difference in statistical significance should not be read as greater precision or as stronger evidence than the sponsor’s result. The analysis structures differ, and the sponsor’s own analysis takes precedence.

In general, confidence intervals are more informative than a significance label because they show both the estimated effect and uncertainty. Here, the sponsor interval allows values below and above zero. The registry does not report a threshold for a clinically important difference, so the interval cannot be judged against a prespecified importance margin. Nor does it establish equivalence: that would require an appropriate design and a reported margin.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the original trial design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original design assumptions and sample-size justification are not reported in the registry record.

For the primary comparison, the planning figures are participants per arm. Under the illustration using 100% of the observed effect, the estimates are 52 participants per arm for 80% power and 69 participants per arm for 90% power. Planning for 75% of the observed effect gives 99 participants per arm for 80% power and 132 participants per arm for 90% power. Planning for 50% of the observed effect gives 232 participants per arm for 80% power and 311 participants per arm for 90% power.

In plain terms, the 80% power column is the estimated number of participants per arm under the stated assumptions for a design with an 80% chance of detecting the chosen effect if that effect is real. The 90% column applies the higher target chance under the same assumptions. Smaller effects need more participants to distinguish them from random variation, which is why the planning estimates rise as the fraction of the observed effect decreases.

These are planning illustrations, not observed power and not a description of the study’s original design. The illustration uses an equal-allocation two-arm framework, whereas this study’s outcome is a within-participant comparison of facial sides. It should therefore be read as a general planning aid rather than a direct reconstruction of the trial’s design requirements.

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 = 0.429; treatment proportion p₁ = 0.179; average p̄ = 0.304.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6503 = 1.2745.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6258 = 0.5267.
4. n = (1.2745 + 0.5267)² / (-0.2500)² = 51.9, rounded up to 52 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 <- 0.428571428571429                          # control proportion
p1 <- 0.178571428571429                          # 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(708071)
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 = 52 (80% power), 69 (90% power)
 75% of observed effect: n per arm = 99 (80% power), 132 (90% power)
 50% of observed effect: n per arm = 232 (80% power), 311 (90% power)
power.prop.test: 51.9 
Simulated power at n = 52 per arm: 0.813 (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 registry reports the sponsor’s primary analysis as McNemar’s test for a difference in proportions. It gives a value of 0.250, a 95% confidence interval from -0.04 to 0.49, and p=0.143. This paired analysis is the sponsor-reported result for the side-to-side comparison.

The simple recalculation from the posted marginal counts gives a risk difference of -0.25 and an unadjusted p-value of 0.042 for the count classified as having less ecchymosis on the treated side compared with the SoC side. The recalculation does not use the participant-level pairing needed for McNemar’s method. The aggregate counts do not show how each participant’s two side-specific assessments were paired, so the difference in results cannot be resolved from the posted summaries alone.

The recalculated result is a check based on a simpler, unadjusted comparison, not a replacement for the sponsor’s analysis. The sponsor’s own analysis takes precedence. Its confidence interval includes zero and its p-value is 0.143; those are the inferential figures to use when describing the registry-reported primary analysis. The discrepancy also means that the marginal-count recalculation should not be used to claim that the sponsor’s paired test reached a different conclusion.

The registry record does not provide the detailed analysis plan or a participant-level paired dataset that would allow independent reproduction of the sponsor’s calculation. It also does not report an explanation for the discrepancy between the sponsor analysis and the recalculation.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists many outcomes and analyses, including visual ecchymosis comparisons at several postoperative days and modified Marchac grade comparisons at multiple time points. When numerous outcomes are tested, the chance of at least one apparently unusual result can increase. In general, multiplicity methods may control that risk by adjusting significance thresholds, defining a hierarchy, or treating secondary comparisons as exploratory. The registry record does not report a multiplicity adjustment, endpoint hierarchy, or a rationale for interpreting the set of tests together.

The primary population is described as per protocol. Assessments without agreement by at least three of the five reviewers were not included in the primary analysis. The record does not state how many assessments failed to meet this criterion, whether those participants were excluded from other analyses, or what sensitivity analyses were used. Reasons for missing outcome observations and methods for handling missing data are not reported in the registry record.

Outcome denominators differ across the posted primary and secondary assessments. That may reflect availability or analysis eligibility at each time point, but the reason is not reported in the registry record and should not be inferred. No imputation method or missing-data assumption is reported.

The registry identifies randomization, single masking, and the sponsor’s McNemar analysis for the primary comparison, but a complete statistical analysis plan is not reported. Details about the randomization procedure, treatment-side assignment, prespecified handling of the four-category assessment, and any sensitivity analyses are not reported in the registry record. The original sample-size justification is also not reported. These omissions limit assessment of whether the posted analyses fully follow a prespecified plan and how robust the primary result is to alternative analysis choices.

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: basal cell carcinoma (2.2%).

The registry reports serious adverse events by location. Among 45 participants at risk for events localized to the SoC side, 1 serious adverse event was recorded; among 45 at risk for events localized to the FS VH S/D 4 side, 0 were recorded. For non-localized events, 45 were at risk and 0 serious events were recorded. The registry lists basal cell carcinoma at 2.2% among the top serious adverse event terms. The relationship between that term and the localized counts is not detailed in the posted information.

For other, non-serious adverse events, the record lists 10 localized to the SoC side, 3 localized to the FS VH S/D 4 side, and 0 non-localized, each with 45 at risk. These are descriptive counts. They should not be interpreted as proof that an event was caused by the treatment or that the sides have different underlying risks, particularly given the small study and the limited detail about event definitions and timing.

Death counts are not reported in the registry record. Further information on event severity, onset, duration, relatedness, and participant-level overlap is not reported in the registry record. The safety entries therefore describe recorded events, rather than a complete comparative safety assessment.

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

The registry record supports a limited description of how blinded reviewers classified early postoperative ecchymosis on opposite sides of the face. For the primary outcome, 5 participants were classified as having less ecchymosis on the FS VH S/D 4 side, 12 as having less on the SoC side, and 11 as having equal ecchymosis, among 28 assessed participants. The sponsor’s paired analysis reports a difference in proportions of 0.250, with a 95% confidence interval from -0.04 to 0.49 and p=0.143.

That result does not establish a statistically clear difference under the sponsor’s reported analysis. It also does not demonstrate equivalence or rule out differences that could matter. No equivalence margin or threshold for clinical importance is reported. The estimate concerns a visual comparison at one early postoperative time point, not every consequence of treatment or the full course of recovery.

The simple recalculation gives a different result because it compares marginal counts without the paired participant-level information used by McNemar’s method. It is not appropriate to treat that recalculation as overriding the sponsor-reported paired analysis. The posted aggregate data do not make it possible to reproduce the paired test independently.

The study is described as exploratory Phase 2 and includes 45 enrolled participants, with fewer represented in the primary per-protocol assessment. Its results are therefore best read as evidence from a small, specific comparison, not as a definitive answer applicable to all face-lift procedures or settings. The registry record does not provide information on broader recovery outcomes, a clinical importance threshold, or the original statistical design assumptions. The data describe observed classifications and their uncertainty; they do not by themselves establish a general treatment effect or a complete safety profile.

18. Why This Trial Matters Statistically

This trial illustrates how design and analysis details can change the interpretation of apparently simple counts. The intervention and comparator were applied to opposite sides of the same participant, so the primary comparison is paired. Marginal counts tell how many assessments favored each side, but they do not reveal the within-person pairings needed to reproduce a paired test. The sponsor’s McNemar result and a simple unadjusted recalculation consequently answer the data in different ways and yield different inferential results.

The example also shows why the endpoint definition matters. The primary outcome was a visual judgment based on photographs, with a majority agreement requirement among five blinded reviewers. This creates a defined classification rule, but it also means that assessments without agreement do not enter the per-protocol analysis. The registry does not report how many observations were excluded for that reason, making the analyzed population harder to relate to the enrollment total.

Precision is another important issue. The sponsor’s interval includes zero and covers effects in either direction, while the primary analysis includes 28 participants. Statistical interpretation should therefore consider the estimate and uncertainty, rather than relying only on a p-value or on a recalculation that does not preserve the paired structure.

Finally, the record includes multiple outcome times and measures, while the multiplicity strategy and full analysis plan are not reported. This makes the secondary findings appropriately exploratory. The study is a useful example of why paired-data structure, transparent analysis plans, reviewer rules, and complete reporting of missing observations matter when interpreting small clinical trials.

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.

Several limitations are specific to the posted record. First, the primary outcome is based on a visual judgment from photographs rather than an objective measurement of bruise extent. Although the reviewers are described as blinded, the registry does not report image standardization beyond the use of standard digital photographs, reviewer reliability, or whether raters were calibrated.

Second, assessments without agreement by at least three of five reviewers were excluded from the primary per-protocol analysis. The number excluded and their outcome characteristics are not reported. Because the primary analysis includes 28 participants while enrollment was 45, the record does not explain the relationship between the enrolled and analyzed populations or the reasons for non-inclusion.

Third, the posted aggregate counts do not provide the paired participant-level classifications. This prevents independent reproduction of the sponsor’s McNemar analysis and leaves the discrepancy with the simple recalculation unresolved. The registry also does not report the full statistical analysis plan, detailed handling of missing data, multiplicity approach, or original sample-size justification.

Fourth, the record includes several secondary time points and outcomes, but detailed numeric findings are not reported for every listed outcome. Follow-up denominators vary across posted assessments, and reasons for those variations are not provided. The small exploratory study and limited information on safety-event timing and relatedness also constrain interpretation. These limitations restrict precision, reproducibility, and the extent to which the findings can be generalized beyond the measured visual outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of Fibrin Sealant With 4 IU/mL Thrombin, Vapor Heated, Solvent Detergent Treated (FS VH S/D 4) in Face-Lift Procedures — NCT00708071.
• Registry record last updated 2012-10-23; status last verified 2012-10.
• Results first posted 2012-08-27.
• 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

NCT00708071 is a completed, randomized, single-masked Phase 2 study sponsored by Baxter Healthcare Corporation. It enrolled 45 participants undergoing rhytidectomy and compared FS VH S/D 4 on one side of the face with standard of care on the other. The primary outcome was a blinded visual comparison of ecchymosis through postoperative day 3.

The primary per-protocol counts were 5 favoring less ecchymosis on the treated side, 12 favoring less on the SoC side, and 11 equal, among 28 participants. The sponsor reported a McNemar difference in proportions of 0.250, a 95% confidence interval from -0.04 to 0.49, and p=0.143. A simple unadjusted recalculation differs, but the sponsor’s paired analysis takes precedence.

Secondary outcomes cover additional postoperative days and modified Marchac assessments. The record also lists adverse event counts by location. The full statistical analysis plan, original sample-size justification, multiplicity approach, and reasons for missing or excluded assessments are not reported in the registry record.