The EVARREST® Fibrin Sealant Patch Liver Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The EVARREST® Fibrin Sealant Patch Liver Study (NCT01993888), a randomized phase 3 study. The primary outcome is Hemostasis at the Target Bleeding Site (TBS) at 4-minutes Following Randomization.

2. Clinical Question

The clinical question is about control of bleeding at a specified site during hepatic surgery, rather than a general measure of surgical recovery. The primary outcome is an event count: participants who met the registry definition of hemostatic success. The comparison is randomized, which supports an evaluation of differences between the assigned groups, while the absence of masking is relevant when considering how procedures and assessments might be influenced. Further details about eligibility, the method used to assess bleeding, and who assessed the endpoint are not reported in the registry record.

3. Trial Design

The registry identifies NCT01993888 as a Phase III randomized, controlled, superiority study with a parallel-group model and no masking. It was sponsored by Ethicon, Inc. The recorded enrollment was 102 participants. The study status is completed; its recorded start was 2013-10 and its primary completion was 2014-07.

The two groups were EVARREST® Fibrin Sealant Patch and Standard of Care (SoC). The registry describes EVARREST as a sterile bio-absorbable combination product made up of a flexible matrix and a coating of Human Fibrinogen and Human Thrombin. SoC is described as a composite of approaches surgeons typically use to control bleeding after conventional methods, such as suture, ligation, or cautery, are ineffective or impractical. The registry description states that SoC was initiated with continuous firm manual compression, with or without gauze or sponge; further detail about the SoC procedure is not reported in the registry record.

The primary outcome was assessed in the ITT analysis set. The record does not report the allocation sequence generation method, concealment procedures, the timing or conduct of any interim analyses, or further details about the analysis population beyond its ITT designation. The original sample-size justification and the trial’s planned statistical analysis details are not reported in the registry record. The planning calculations associated with the posted outcomes are separate illustrations based on the observed effect, not evidence of the assumptions used to design this trial.

The registry lists six outcome measures. The primary measure concerns hemostasis at 4 minutes following randomization; a secondary measure concerns hemostasis at 10 minutes. Other secondary measures address time to hemostasis, re-bleeding, adverse events, and adverse events potentially related to thrombotic events. The numerical results available for these outcomes vary, so the primary comparison should not be treated as a complete account of every outcome listed.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary endpoint analysis was based on the Intent to Treat (ITT) analysis set.

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 Hemostasis at the Target Bleeding Site (TBS) at 4-minutes Following Randomization, measured over Intraoperative, 4 minutes following randomization.

The primary endpoint counts participants achieving hemostasis at the target bleeding site at 4 minutes following randomization. Hemostasis is defined as no detectable bleeding at the site at that time, with an additional requirement that no re-bleeding requiring treatment occur at the site before initiation of wound closure. The measure is recorded as a number of participants with hemostatic success, and the analysis population is the ITT set.

This endpoint is used to capture an immediate, site-specific outcome during surgery. Its fixed assessment time makes the outcome comparable across the randomized groups, while the no-re-bleeding condition extends the definition beyond a single observation at 4 minutes. It therefore combines the presence or absence of detectable bleeding at the assessment point with a subsequent treatment-related condition before wound closure.

As a binary outcome, each participant either meets the recorded success definition or does not. The count is straightforward to interpret, but it does not describe the amount of bleeding, the time course between assessments, or the clinical context of each event. Those details are not reported in the registry record. The endpoint also does not by itself describe later bleeding, overall surgical outcomes, or safety. The registry lists separate secondary measures for hemostasis at 10 minutes, absolute time to hemostasis, and re-bleeding during follow-up, but those questions should remain distinct from the primary endpoint.

7. Results Posted in the Registry

• EVARREST™ Fibrin Sealant Patch: 96.0% (48/50) versus 46.2% (24/52) on control; risk difference 49.8 percentage points (95% CI 35.2 to 64.4), risk ratio 2.08 (1.54–2.80); 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.

Hemostasis at the Target Bleeding Site (TBS) at 10-minutes Following Randomization

• 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:
  • EVARREST™ Fibrin Sealant Patch: 98.0% (49/50) versus 80.8% (42/52) on control; risk difference 17.2 percentage points (95% CI 5.8 to 28.6), risk ratio 1.21 (1.06–1.39); unadjusted two-proportion z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for EVARREST™ Fibrin Sealant Patch than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted numerical secondary comparison concerns hemostasis at the target bleeding site at 10 minutes following randomization. Its event counts and unadjusted comparison are displayed with the secondary results. The estimate is in the same direction as the primary comparison, but it addresses a different assessment time and should not be substituted for the primary endpoint.

The registry lists additional secondary measures covering absolute time to hemostasis, re-bleeding events during study follow-up, adverse events, and adverse events potentially related to thrombotic events. Numerical results for these measures are not reported in the registry record. Consequently, the record does not support a complete account of the secondary-outcome pattern, and no overall claim about consistency across all secondary endpoints can be made from the listed outcome names alone.

Secondary outcomes can provide context by asking related but distinct questions. A later hemostasis assessment may complement the primary time point; time-to-hemostasis and re-bleeding measures address other aspects of bleeding control; safety measures concern harms rather than hemostatic success. Their interpretation depends on their definitions, analysis populations, follow-up, and statistical methods, details that are not reported for all outcomes in the registry record.

Unadjusted secondary results generally carry less confirmatory weight when a study assesses multiple outcomes. The more outcomes examined, the greater the chance that at least one result may appear notable by chance if no multiplicity strategy is used. The registry record does not report whether the secondary analyses were adjusted, placed in a hierarchy, or intended as exploratory. The 10-minute result should therefore be viewed as additional context, not as an independent confirmation that resolves the limitations of the primary analysis or fills gaps in the other secondary results.

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

• Hemostasis at the Target Bleeding Site (TBS) at 10-minutes Following Randomization
• Absolute Time to Hemostasis
• Incidence of Re-bleeding Events From the TBS During the Study Follow-up
• Incidence of Adverse Events (AEs)
• Incidence of Adverse Events That Were Potentially Related to Thrombotic Events

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The primary outcome is binary: participants are counted as having either achieved hemostatic success or not, according to the registry definition. The posted re-calculation compares the proportions in the two randomized groups using a risk difference. This measure expresses the difference between the event proportions on the proportion scale. The estimated risk difference is 0.498, with a confidence interval from 0.352 to 0.644. The comparison is unadjusted, meaning it uses the posted group summary counts without adjustment for other variables.

Risk difference is one way to express a binary outcome contrast. Other measures, such as a risk ratio or odds ratio, describe the relationship on different scales and can have different numerical interpretations. Their values are reported with the primary comparison, but interpreting several measures at once can distract from the directly interpretable contrast in event proportions. None of these measures changes the endpoint definition or adds information about unreported participant-level characteristics.

What does a p-value tell the reader?

A p-value is a measure of how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not indicate the probability that the finding occurred by chance in an everyday sense. A smaller p-value indicates less compatibility with the null model under the test assumptions, but does not by itself quantify the effect size or its clinical importance.

The registry reports a Chi-squared analysis with p <.0001. The posted re-calculation reports p <0.001. The record does not report further details about the sponsor’s full statistical analysis plan or any adjustments beyond the identified Chi-squared method. The p-value should therefore be considered alongside the effect estimate and its interval, not as a replacement for them.

Why is a confidence interval useful?

A confidence interval gives a range of values compatible with the data under the interval method and its assumptions. It communicates uncertainty about an estimated quantity. The primary interval runs from 0.352 to 0.644 for the risk difference, and the estimate is 0.498. The interval is not a range containing a fixed proportion of individual participant outcomes; it is an interval for the group contrast. Its width reflects statistical precision, with narrower intervals generally indicating greater precision under comparable methods and data.

Confidence intervals are not guarantees that the true effect lies within the calculated range, nor do they account automatically for every source of uncertainty. In particular, they do not resolve questions about how the trial was conducted, outcome assessment, missing data, or selective reporting. Those aspects require design and reporting information that is not reported in the registry record.

Why does the analysis use binary-outcome methods?

The primary event is success under a defined rule, and the record gives counts of participants with that event and the group denominators. Methods for binary outcomes are therefore appropriate to the form of the posted data. A Chi-squared test evaluates whether the observed event distribution is compatible with equal proportions under its null model. A risk-difference estimate complements that test by expressing the contrast in the same outcome scale.

General statistical practice distinguishes a test of a null hypothesis from estimation. A test provides evidence against a specified null model, while an estimate and confidence interval describe the magnitude and uncertainty of the group contrast. The trial’s reported Chi-squared result and the unadjusted re-calculation serve these different roles when read alongside the group counts.

What can and cannot be inferred from the analysis?

Random assignment is intended to make the groups comparable in expectation, supporting a causal comparison of assigned strategies when the trial is conducted and analyzed appropriately. The registry identifies randomization, but does not report the sequence-generation or allocation-concealment methods. Masking is listed as none. These details matter because knowledge of treatment assignment can affect care, measurements, or outcome assessment; the registry record does not provide enough information to establish whether or how such influences were addressed.

The primary analysis population is ITT. As a general concept, an ITT analysis aims to analyze participants according to randomized assignment, preserving the randomized comparison. The registry does not report how missing outcomes or protocol deviations were handled, so the exact implementation cannot be assessed from the record. The group denominators posted for this endpoint are 50 and 52, but additional detail on participant flow and exclusions is not reported in the registry record.

The calculation is unadjusted and based on summary statistics. It does not incorporate covariates, participant-level data, or any adjustment for multiple outcomes. The registry reports one primary endpoint and lists five secondary outcomes. The analysis plan for multiplicity, including any hierarchy or adjustment, is not reported in the registry record. Accordingly, the secondary results should not be interpreted as if a formal multiplicity procedure had been applied.

Finally, general statistical interpretation separates evidence about an observed endpoint from broader claims about treatment effects. The primary estimate concerns hemostasis at the target bleeding site under the specified definition and time. It does not automatically establish effects on later bleeding, other surgical outcomes, or adverse events. Those require their own complete outcome results and appropriately described analyses. Results for several listed secondary measures and details of the original statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.498, and its confidence interval extends from 0.352 to 0.644. This interval communicates uncertainty in the estimated contrast between the randomized groups. Its endpoints remain on the positive side of zero, indicating that the interval associated with this re-calculation is compatible with a positive risk difference for EVARREST relative to SoC under the method’s assumptions. The interval does not indicate the probability that a particular participant will achieve hemostasis.

Confidence intervals are useful because they show both the direction and the range of effect sizes reasonably compatible with the observed data, rather than presenting only a single estimate. The range is not a guarantee about the true value, and its interpretation depends on the statistical method and assumptions. It also does not incorporate unreported uncertainties about trial conduct, endpoint measurement, missing data, or selective outcome reporting.

The primary estimate is based on 48 successes among 50 participants in the EVARREST group and 24 among 52 in the SoC group. The group counts give the context for the interval, while the risk difference expresses the comparison on the absolute proportion scale. Other reported measures, including the risk ratio and odds ratio, use different scales and should not be treated as interchangeable with the risk difference.

The registry’s Chi-squared result, p <.0001, and the unadjusted re-calculation, p <0.001, provide evidence against their respective null comparisons. A p-value does not express precision or effect magnitude, so it should be read with the interval and estimate. No confidence interval for the sponsor-reported Chi-squared analysis is posted in the registry record. The interval belongs to the unadjusted re-calculation from the summary statistics.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for this binary endpoint, 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. The effect to detect is set at the stated fraction of the observed effect. The original design assumptions and the trial’s own sample-size justification are not reported in the registry record; these calculations are planning illustrations based on the observed effect.

The 80% power column gives the planned number of participants per arm under the stated assumptions for a calculation designed to have 80% power to detect the specified effect. The 90% power column gives the corresponding per-arm number for 90% power. In general, power is the probability that a study will reject its null hypothesis under a specified alternative effect, assuming the planning model and its conditions hold. It is a design quantity, not a statement about what the completed trial achieved.

The entries are shown for planning at 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The smaller the effect targeted for detection, the more participants the calculation requires under otherwise unchanged assumptions. This pattern reflects that smaller group differences are harder to distinguish from sampling variation than larger differences.

These figures are not observed power. They do not recalculate the probability that the completed trial found a statistically significant result, nor do they validate the assumptions used in the original design. They are conditional illustrations to help readers understand how a future study’s planned size changes with the target effect and desired power.

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 = 0.462; treatment proportion p₁ = 0.960; average p̄ = 0.711.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6412 = 1.2568.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5356 = 0.4508.
4. n = (1.2568 + 0.4508)² / (0.4985)² = 11.7, rounded up to 12 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 <- 0.461538461538462                          # control proportion
p1 <- 0.96                          # 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(1993888)
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 = 12 (80% power), 16 (90% power)
 75% of observed effect: n per arm = 25 (80% power), 33 (90% power)
 50% of observed effect: n per arm = 61 (80% power), 80 (90% power)
power.prop.test: 11.7 
Simulated power at n = 12 per arm: 0.845 (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 comparison as a Chi-squared analysis, with p <.0001. The posted unadjusted re-calculation, based on the group summary counts, reports p <0.001 and estimates a risk difference of 0.498, with a confidence interval from 0.352 to 0.644. The registry’s reported analysis and the simple re-calculation are consistent in the broad direction of the evidence, while they are distinct analyses and their p-value formats should be quoted as reported.

The re-calculation provides an unadjusted estimate and interval from the posted counts. It is not a reconstruction of the sponsor’s complete analysis plan, and it does not include any possible adjustments or details not available in the registry record. The sponsor’s reported analysis is the trial’s registered analysis result; the re-calculation offers a transparent summary-statistic comparison that helps describe magnitude and precision.

The registry does not report additional details about the sponsor’s model, any covariate adjustment, or multiplicity handling. The record does not identify a discrepancy between the posted analysis and the re-calculation. Interpretation should therefore retain the distinction between the sponsor-reported test and the unadjusted estimate rather than treating one as a replacement for the other.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists five secondary outcomes. The primary endpoint is hemostasis at the target bleeding site at 4 minutes following randomization. The listed secondary outcomes address hemostasis at 10 minutes, absolute time to hemostasis, re-bleeding, adverse events, and adverse events potentially related to thrombotic events. The record does not report a multiplicity plan, such as an adjustment to significance thresholds or a hierarchy governing the interpretation of outcomes.

As a general statistical principle, testing multiple outcomes can increase the chance of at least one apparently significant result when all outcomes are treated as confirmatory and no multiplicity procedure is used. A prespecified hierarchy or adjustment can help control that concern, but neither should be assumed in the absence of reporting. The posted p-values should be interpreted as reported, without implying that they have been adjusted for the number of outcomes.

The primary analysis population is identified as ITT, but details about missing data are not reported in the registry record. In particular, the record does not describe the amount or handling of missing primary or secondary outcome data, imputation methods, sensitivity analyses, or how participants with incomplete follow-up were treated. The denominators posted for the primary endpoint are 50 and 52, but those values alone do not explain participant flow or missingness.

Further details about the trial’s statistical analysis plan, including model specifications, covariate adjustments, prespecified testing procedures, and interim analyses, are not reported in the registry record. This absence limits assessment of whether the posted analyses followed a fully prespecified plan and how much inferential weight to assign the secondary results. It does not, by itself, establish that a particular procedure was or was not used; it means the record does not provide the information needed to evaluate it.

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: haematoma infection (4.0%), pneumonia (4.0%), post-procedural bile leak (4.0%), sepsis (3.8%), renal failure acute (3.8%).

The registry reports serious adverse events affecting 12 of 50 participants in the EVARREST group and 16 of 52 participants in the SoC group. Other adverse events affected 45 of 50 and 50 of 52 participants, respectively. These are descriptive counts for the groups, not a reported adjusted comparison or a test of a safety difference.

The registry also lists serious-event terms with reported percentages: Haematoma Infection, Pneumonia, and Post-procedural Bile Leak at 4.0% each; Sepsis and Renal Failure Acute at 3.8% each; and Ileus at 2.0%. These listed terms do not replace the overall serious-event counts. The record does not provide enough detail to infer the timing, duration, severity distribution, or attribution of each event from those figures.

Deaths are not reported in the registry record. The adverse-event follow-up period, event definitions, collection procedures, and comparative safety analysis are also not reported. The counts should be read as a limited descriptive account and not as a complete evaluation of harms or evidence that either group had a safer profile.

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

The primary result describes hemostatic success at one target bleeding site and one specified time, using the registry definition that also requires no re-bleeding requiring treatment before wound closure. The posted counts and unadjusted estimate show a higher observed proportion of success in the EVARREST group than in the SoC group for that endpoint. The confidence interval provides a range of uncertainty around the estimated risk difference.

That result does not establish what would happen for every patient or every surgical setting. It does not by itself address bleeding at other sites, later bleeding beyond the endpoint definition, overall surgical recovery, or outcomes not numerically reported in the registry record. The listed measures of time to hemostasis, re-bleeding, and safety are distinct questions, and complete numerical results for them are not reported in the registry record.

The randomized design supports a comparison between assigned groups, but important implementation and analysis details are not reported. Masking is listed as none; allocation concealment, missing-data handling, and multiplicity procedures are not described. These omissions limit how fully the reported estimate can be assessed, but they do not justify assuming that any particular undocumented procedure was used or omitted.

The result is not a stand-alone conclusion about the balance of benefits and harms. Serious and other adverse-event counts are descriptive, while deaths and several details needed for a comparative safety interpretation are not reported. Statistical evidence for a primary endpoint is not equivalent to a complete clinical assessment, and the registry result should be understood within the specific population, endpoint, and analysis information it records.

18. Why This Trial Matters Statistically

This trial is statistically informative because it poses a focused randomized comparison for a binary, intraoperative outcome. The primary endpoint has a clear time point and a stated success definition, and the registry provides event counts for both groups. These features allow readers to examine an absolute risk-difference estimate and its confidence interval rather than relying on a significance test alone.

The comparison also illustrates why a result is best understood through several statistical components. The group counts describe the observed data, the risk difference expresses the estimated contrast, the confidence interval communicates uncertainty, and the p-value addresses compatibility with a null model. Each answers a different question. The registry’s Chi-squared result and the unadjusted recalculation point in a similar inferential direction, while the estimate and interval communicate the size and precision of the posted contrast.

The record also illustrates the limits of available outcome reporting. A result for the primary endpoint cannot stand in for unreported results on time to hemostasis, re-bleeding, or safety. Likewise, a statistically notable secondary result has less confirmatory force when the multiplicity plan is not reported. The planning illustrations further show, in general terms, that sample-size needs depend on the target effect and desired power; they are separate from the trial’s undocumented original design justification.

For clinical researchers and biostatisticians, the key lesson is to distinguish what the registry quantifies from what remains uncertain. Careful attention to endpoint definitions, analysis populations, interval estimates, and absent reporting helps prevent a single p-value or outcome from carrying more meaning than the recorded data support.

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 specific to this record affect interpretation. The primary endpoint is site-specific and intraoperative, with success assessed at 4 minutes and a further requirement related to re-bleeding before wound closure. It does not summarize every aspect of bleeding control. The assessment procedures, measurement reliability, and assessor roles are not reported in the registry record, and masking is listed as none.

The analysis population is described as ITT, but the registry does not report participant flow, the handling of missing outcomes, or sensitivity analyses. It also does not report allocation-sequence generation or concealment details. As a result, the degree to which all potential sources of bias were addressed cannot be evaluated from this record alone.

The registry provides numerical results for the primary outcome and the 10-minute hemostasis outcome, but not for the other listed secondary outcomes. This limits assessment of the broader pattern across bleeding and safety measures. A multiplicity strategy, full analysis plan, interim-analysis details, and the original sample-size rationale are not reported. The sample-size figures associated with the observed effect should not be mistaken for the trial’s design assumptions.

Safety reporting is also limited: adverse-event counts and selected serious-event terms are posted, but deaths, follow-up duration, event definitions, attribution, and a comparative safety analysis are not reported. The record therefore supports a focused interpretation of the primary endpoint, but not a comprehensive assessment of longer-term outcomes or the full benefit-harm profile.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The EVARREST® Fibrin Sealant Patch Liver Study — NCT01993888.
• Registry record last updated 2016-07-11; status last verified 2016-04.
• Results first posted 2016-07-11.
• 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

NCT01993888 is a completed, randomized, parallel-group Phase III superiority study with no masking, sponsored by Ethicon, Inc. It enrolled 102 participants and compared EVARREST® Fibrin Sealant Patch with Standard of Care for controlling parenchymal bleeding during hepatic surgery.

The primary endpoint was hemostatic success at the target bleeding site at 4 minutes following randomization, analyzed in the ITT set. The registry reports 48 successes among 50 participants assigned to EVARREST and 24 among 52 assigned to SoC. Its reported Chi-squared analysis gives p <.0001; the unadjusted re-calculation estimates a risk difference of 0.498, with a confidence interval from 0.352 to 0.644.

The record lists five secondary outcomes but provides numerical results for the 10-minute hemostasis comparison only. It reports descriptive adverse-event counts, while deaths and several analysis and follow-up details are not reported in the registry record. The primary result should be interpreted as evidence about the defined intraoperative endpoint, not as a complete account of all outcomes.