The Effect of Intravenous EACA on Blood Loss and Transfusion Requirements After Bilateral VRO: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effect of Intravenous EACA on Blood Loss and Transfusion Requirements After Bilateral VRO (NCT02257580), a randomized phase 4 study. The primary outcome is Intraoperative Calculated Total Blood Loss.

2. Clinical Question

3. Trial Design

The registry identifies NCT02257580 as a completed Phase 4 randomized trial sponsored by Hospital for Special Surgery, New York. The listed start date is 2015-04-01, and the primary completion date is 2020-10-26. Enrollment is recorded as 28. The posted primary-outcome groups contain 16 participants assigned to EACA and 12 assigned to placebo.

Allocation is recorded as randomized, and the control group received placebo. The summary characterizes the study as prospective, double-blind, and placebo-controlled. The registry masking field says quadruple, but the record does not identify which people or roles were masked. The model field says single-group, a description that sits uneasily alongside the two posted randomized arms; the record does not explain this mismatch. No explanation of the allocation sequence or concealment procedures is reported in the registry record.

The intervention description gives an EACA loading dose of 100 mg/kg, with a maximum of 4-5 grams, up to 1 hour before incision. An infusion of 33 mg/kg/hr, with a maximum of 1 gram/hr, was to continue during the case and end at its conclusion. The placebo was an equivalent volume of normal saline prepared by the pharmacy. These details describe the assigned regimens; adherence and deviations from the regimens are not reported in the registry record.

The primary outcome was intraoperative calculated total blood loss over the stated timeframe of 3-6 hours. Secondary outcomes listed in the record include cell saver use, postoperative allogeneic transfusion, postoperative blood loss, hospital length of stay, and complications. The registry lists six outcome measures, while only some secondary results have posted numerical group data. Protocol details, the original statistical plan, and the handling of missing data 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.

Overall Study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Intraoperative Calculated Total Blood Loss, measured over Intraoperative (3-6 hours).

The primary endpoint is intraoperative calculated total blood loss, measured in mL. Rather than recording blood loss as a direct volume, the registry description says it was estimated using estimated blood volume, the difference between preoperative and postoperative hemoglobin, and the Nadler equation for estimating blood volume. The calculation also adjusts for transfused hemoglobin to produce a single measure of calculated intraoperative blood loss.

This approach is intended to combine information about hemoglobin change and estimated blood volume into a measure of blood loss that can be compared between randomized groups. The method may be useful when direct measurement of total blood loss is difficult, but the resulting value remains an estimate dependent on the inputs and calculation procedure. The registry does not report additional validation details or the exact timing of the postoperative hemoglobin measurement.

The endpoint is summarized as a mean with a standard deviation for each group. The mean describes the group average; the standard deviation describes the spread of individual measurements around that average. The posted means are 535.7 mL in the EACA group and 628.0 mL in the placebo group. The unadjusted mean difference is -92.3 mL, with a confidence interval from -312.1 to 127.5 mL. This estimate is a comparison of the posted group summaries, not a separate adjusted treatment-effect analysis.

7. Results Posted in the Registry

• E-Aminocaproic Acid (EACA): mean 535.70 versus 628.00 on control; difference -92.30 (95% CI -312.14 to 127.54), standardized effect d = -0.30; z-test p = 0.411.

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.

Intraoperative Cell Saver Utilization

• 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:
  • E-Aminocaproic Acid (EACA): 43.8% (7/16) versus 58.3% (7/12) on control; risk difference -14.6 percentage points (95% CI -51.6 to 22.4), risk ratio 0.75 (0.36–1.56); unadjusted two-proportion z-test p = 0.445.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between E-Aminocaproic Acid (EACA) and the control. The interval gives the range of effects that remain compatible with the data.

Postoperative Allogeneic Blood Transfusion

• 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:
  • E-Aminocaproic Acid (EACA): 25.0% (4/16) versus 25.0% (3/12) on control; risk difference 0.0 percentage points (95% CI -32.4 to 32.4), risk ratio 1.00 (0.27–3.66); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between E-Aminocaproic Acid (EACA) and the control. The interval gives the range of effects that remain compatible with the data.

Post Operative Blood Loss

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • E-Aminocaproic Acid (EACA): mean 72.50 versus 103.30 on control; difference -30.80 (95% CI -92.80 to 31.20), standardized effect d = -0.39; z-test p = 0.330.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between E-Aminocaproic Acid (EACA) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several different aspects of the operation and recovery: use of cell saver, postoperative allogeneic transfusion, postoperative blood loss, length of stay, and complications. The posted numerical results include cell saver use, postoperative transfusion, and postoperative blood loss. The broader pattern does not provide a consistently precise signal across these outcomes. The available group comparisons are uncertain, and the registry does not post numerical results for every listed secondary outcome.

These outcomes are related to the primary question but are not interchangeable with calculated intraoperative blood loss. Cell saver use and transfusion are clinical decisions or events that may reflect blood loss alongside other influences. Postoperative blood loss describes a later period, while length of stay and complications concern other dimensions of recovery and safety. A difference in one measure would not automatically establish a corresponding difference in another. The primary endpoint remains the direct focus of the stated study aim.

Secondary comparisons carry less weight when they are unadjusted and multiple outcomes are examined. Each additional comparison creates more opportunity for an apparently unusual result to arise by chance, even when there is no true difference for any outcome. The registry does not report a multiplicity procedure, a hierarchy among secondary outcomes, or a prespecified plan for interpreting them. Accordingly, individual secondary p-values should be treated as exploratory rather than as independent confirmatory evidence.

The posted results can help describe the range of outcomes considered, but they do not resolve the primary estimate’s uncertainty. A broad pattern across endpoints is more informative than selecting an isolated favorable or unfavorable comparison, yet even a pattern must be interpreted in light of small group sizes, outcome variability, and incomplete reporting. The registry record does not provide detailed analyses for all the listed secondary measures, so conclusions about the overall recovery profile remain limited.

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

• Intraoperative Cell Saver Utilization
• Postoperative Allogeneic Blood Transfusion
• Post Operative Blood Loss
• Length of Hospital Stay
• Complications [VTE (Symptomatic of DVT or PE), Infection (Superficial, Deep), Hematoma, Seroma, Reoperation, and Death]

9. Statistical Interpretation

10. Statistical Methods Explained

The registry’s primary outcome is a continuous measurement reported as a mean and standard deviation. A mean is the arithmetic average of the recorded values in a group. It gives a compact description of the group’s central level, but it does not show how values are distributed or whether there are unusually high or low observations. A standard deviation describes how dispersed observations are around the mean. Larger spread generally makes a group mean, and a comparison between group means, less precise when group sizes are held fixed.

The reported effect measure is a mean difference. It compares the EACA group mean with the placebo group mean according to the ordering used in the registry results. The posted estimate is -92.3 mL. Its sign communicates direction under that ordering; its magnitude is expressed in the endpoint’s units. The mean difference is not a percentage change, and it does not account for other variables unless an adjusted analysis is explicitly reported. No adjusted primary analysis is listed in the registry record.

A confidence interval expresses uncertainty around an estimated effect under the assumptions of the calculation. The primary interval, -312.1 to 127.5 mL, is broad and includes zero. Values within the interval are not all equally likely, and the interval is not a range containing every plausible individual outcome. Rather, it describes the uncertainty associated with the group comparison. A wide interval indicates that the data do not pin down the size or direction of the difference closely.

The unadjusted p-value for the primary comparison is 0.411. A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result occurred by chance. The registry does not report an adjustment of this p-value for multiple outcome comparisons.

Why does outcome variability matter?

Blood loss estimates vary between participants. When the observations are dispersed, the group average is less precisely estimated than it would be with more consistent observations, all else equal. This is one reason the standard deviations belong alongside the means. The EACA standard deviation is 356.6 mL, and the placebo standard deviation is 235.8 mL. The record also gives standard errors of the group means, 89.15 mL and 68.07 mL, respectively. A standard error describes the estimated sampling uncertainty of a statistic, such as a mean; it is not the spread of individual outcomes.

The comparison’s pooled standard deviation is 311.3 mL. A pooled estimate combines within-group variation for purposes of a standardized comparison. The posted standardized effect, d = -0.296, expresses the mean difference relative to that pooled spread. Such a standardized measure can help compare effects measured on different scales, but it does not replace the mean difference in mL, which retains direct interpretation in the clinical endpoint’s units. Neither standardized effect nor mean difference establishes clinical importance without a prespecified threshold or clinical context.

What is the role of randomization?

Random allocation is intended to make treatment groups comparable, on average, with respect to measured and unmeasured factors. In a randomized study, a between-group contrast can support a causal interpretation when allocation, follow-up, outcome ascertainment, and analysis are appropriately conducted. The registry identifies randomized allocation, but it does not report the sequence-generation method, allocation concealment, adherence, participant flow, or analysis population. Those omissions limit assessment of how fully the intended design was carried through.

The study is described as double-blind in the summary, and the masking field says quadruple. Masking can reduce the opportunity for expectations to influence care or measurement, but the registry does not specify the masked roles or how masking was maintained. The outcome itself is calculated from laboratory and estimated-volume inputs, so the details of measurement and calculation remain important regardless of masking.

What does over-dispersion mean for binary outcomes?

For a binary endpoint, each participant either has or does not have the recorded event. With modest group sizes, the observed proportions can be unstable: a small change in event counts can materially change the estimated proportion. A simple binomial model assumes variation consistent with the event probability and the number of observations. Over-dispersion means the observed variability is greater than that model expects, which can make standard errors too small and confidence intervals too narrow if not addressed. The registry does not report an over-dispersion assessment or a model for the secondary binary outcomes.

The secondary binary comparisons include risk differences and, where posted, relative risks and odds ratios. A risk difference compares the event proportions directly, while a relative risk compares them as a ratio and an odds ratio compares event odds. These measures answer related but different questions. Their confidence intervals can be wide when event counts are limited; interpretation should rely on the interval and the underlying counts, not only on a p-value. These are unadjusted comparisons, and the registry record does not report a multiplicity correction.

The calculations labelled as recalculated are unadjusted comparisons derived from the posted group summaries. No discrepancy is flagged for the primary comparison. The registry lists no reported analyses for the secondary outcomes. The statistical model, handling of missing observations, and any planned covariate adjustment are not reported in the registry record, so conclusions should remain limited to the reported summaries and comparisons.

11. Confidence Intervals and Precision

The primary estimate is -92.3 mL, and its confidence interval extends from -312.1 to 127.5 mL. The interval spans zero, so it includes no mean difference as well as differences favoring either group under the comparison’s direction. Its width signals substantial uncertainty about the size and direction of the primary contrast. The estimate should therefore be read as a point within a broad range of values compatible with the data and calculation assumptions, not as a precise treatment effect.

The two group means are 535.7 mL for EACA and 628.0 mL for placebo. Their standard deviations are 356.6 mL and 235.8 mL. The variation in individual measurements, together with the group sizes of 16 and 12, helps explain why the confidence interval is broad. The record does not report a clinically important difference threshold. Without such a threshold, the interval cannot establish whether effects that might matter clinically have been ruled out.

Confidence intervals are useful because they show both the direction and the uncertainty of an estimate. They do not give the probability that the true effect lies within the particular interval, and they do not account for biases or limitations that are not represented in the calculation. In this trial, the interval is an unadjusted comparison based on posted summary statistics. It does not incorporate unreported covariates, missing-data procedures, or other analyses that may have been considered.

The unadjusted p-value of 0.411 is consistent with substantial uncertainty, but it should not be used alone to judge the estimate. A result that does not cross a conventional significance threshold is not proof of no effect, and a confidence interval containing zero is not proof of equivalence. The practical reading is that the registry result does not estimate the primary difference precisely enough to distinguish clearly among materially different possibilities.

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 expressed as participants per arm for the two-arm comparison, not as total events. They are illustrative calculations based on the observed effect, not the trial’s original design assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original sample-size justification and design assumptions are not reported in the registry record.

For the primary endpoint, the planning illustration using 100% of the observed effect gives 179 participants per arm for 80% power and 239 participants per arm for 90% power. Planning for 75% of the observed effect gives 318 participants per arm for 80% power and 425 participants per arm for 90% power. Planning for 50% of the observed effect gives 715 participants per arm for 80% power and 956 participants per arm for 90% power. The same planning logic is used for the secondary outcomes that have planning rows; no such calculation is posted for postoperative transfusion.

Power is the chance that a study would detect an effect of the specified size under the planning assumptions if that effect were present. The 80% and 90% columns represent different target probabilities of detection, not observed outcomes from this trial. The illustrations are not observed power. Smaller effects require more participants to detect reliably under the stated assumptions, which is why the calculated requirements rise as the target fraction of the observed effect falls. These figures do not show that the trial was designed with these assumptions or that its observed result has a particular probability of being correct.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -92.300; pooled standard deviation σ = 311.267.
2. n = 2 × (1.96 + 0.842)² × 311.267² / -92.300² = 178.5, rounded up to 179 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
delta <- -92.3                      # observed difference in means
sigma <- 311.267349840813                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2257580)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 179 (80% power), 239 (90% power)
 75% of observed effect: n per arm = 318 (80% power), 425 (90% power)
 50% of observed effect: n per arm = 715 (80% power), 956 (90% power)
power.t.test: 179.5 
Simulated power at n = 179 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 one primary outcome and several secondary outcomes. It does not report how the outcomes were prioritized for statistical testing beyond identifying the primary endpoint, whether the analyses followed a prespecified hierarchy, or whether any multiplicity adjustment was applied. The posted p-values are unadjusted. When many outcomes are examined, the chance of at least one apparently notable result can increase; adjustment or a clearly stated testing hierarchy can help address that issue. Without a reported plan, the secondary results should not be treated as confirmatory findings.

The record lists no reported analyses for the primary or secondary outcomes in its analysis fields, although it does post group summaries and comparison statistics. The comparison statistics discussed for the primary endpoint are unadjusted recalculations from the posted summaries. The registry does not identify an analysis population such as intention-to-treat or per-protocol, nor does it report whether participants were analyzed according to assigned group. This makes it difficult to assess the role of exclusions or treatment deviations.

Missing-data methods and the amount or pattern of missing outcome data are not reported in the registry record. It is therefore unknown whether all randomized participants contributed to each endpoint, whether missing values were imputed, or whether sensitivity analyses were undertaken. Missingness can affect estimates if the availability of measurements is related to group assignment or outcome status. No conclusion about those possibilities can be drawn from the posted summary alone.

The registry also does not report interim analyses, stopping rules, covariate adjustment, or a detailed statistical analysis plan. These are not details that can be inferred from the randomization or masking fields. Their absence does not demonstrate that such methods were not used; it means they are not documented in the registry record. The displayed comparisons should therefore be interpreted as limited summaries rather than a complete account of the trial’s analytical conduct.

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.

The adverse-event record reports 0 serious adverse events among 16 participants at risk in the EACA group and 0 among 12 participants at risk in the placebo group. It also records 0 other adverse events and 0 deaths in each group. These are counts recorded for the reported groups; they do not show that the risks of rare events are absent or equal.

The registry lists complications of interest including venous thromboembolism, infection, hematoma, seroma, reoperation, and death. The serious-event terms field contains no listed terms. Details about event definitions, ascertainment, follow-up completeness, and the timing of safety surveillance are not reported in the registry record. The record also does not provide confidence intervals for these safety counts.

With no recorded events in the posted groups, the data offer limited information about the frequency of uncommon harms. A zero count can occur even when an underlying risk is not zero, particularly when the groups are small. The safety figures should be read as the events reported in this trial record, not as proof that no adverse events could occur in other patients or settings.

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

The registry results show that the average calculated intraoperative blood loss was numerically lower in the EACA arm than in the placebo arm. The unadjusted mean difference is -92.3 mL, and the 95% confidence interval ranges from -312.1 to 127.5 mL. Because the interval includes zero and extends in both directions, the estimate does not distinguish clearly between lower, similar, or higher mean calculated blood loss under the comparison’s direction.

This is not evidence that the treatments are equivalent. Equivalence or non-inferiority requires a prespecified margin and an analysis designed to address that question; neither is reported in the registry record. Nor does the unadjusted p-value of 0.411 prove that an effect is absent. The posted estimate is uncertain, and the record does not provide a threshold for what size of difference would be clinically important.

The conclusion is restricted to the calculated intraoperative blood-loss measure for patients undergoing bilateral VRO in this trial. The measure is derived from hemoglobin and estimated blood-volume inputs with an adjustment for transfused hemoglobin, rather than being a direct observation of total blood loss. Results for that endpoint cannot be assumed to describe postoperative blood loss, transfusion, cell saver use, length of stay, or complications. The secondary findings require their own interpretation and are subject to the limitations of unadjusted multiple comparisons.

The record’s randomized allocation and placebo control are relevant strengths for a comparative question. However, interpretation is constrained by the limited group sizes, the wide primary confidence interval, incomplete reporting of analysis methods and missing data, and the discrepancy between the single-group model field and the two posted randomized arms. The summary describes double-blinding while the masking field says quadruple; the exact masked roles are not explained. These gaps prevent a full assessment of bias and analytical choices.

Accordingly, the most defensible reading is descriptive: the observed group means differ, but the registry result is too imprecise to establish the direction or size of a reliable difference. It does not support a definitive claim of benefit, lack of benefit, equivalence, or safety beyond the events recorded. Broader conclusions would require fuller reporting and evidence from studies designed and analyzed for those questions.

17. Why This Trial Matters Statistically

This trial addresses a statistical challenge common in surgical research: estimating a treatment effect when the outcome is variable and is itself calculated from several clinical measurements. Intraoperative blood loss is not reported as a direct volume; the registry describes a calculation based on estimated blood volume, hemoglobin change, and transfused hemoglobin. That construction makes clear measurement definitions and reproducible methods especially important when comparing groups.

The randomized, placebo-controlled design is suited to a comparative question, and the record identifies an outcome directly connected to its stated aim. Reporting group means, standard deviations, a mean difference, and a confidence interval gives readers more information than a p-value alone. In particular, the wide interval makes the uncertainty visible. It shows why a point estimate should not be interpreted as a precise or definitive answer.

The trial also illustrates the distinction between statistical significance and clinical importance. The p-value does not establish whether a difference matters to patients, while the confidence interval does not resolve that question without a prespecified clinical threshold. A carefully chosen meaningful-difference threshold, together with adequate planning and complete outcome reporting, would help connect statistical uncertainty to the clinical question.

Finally, the registry record demonstrates why transparent reporting matters. Details on the analysis population, missing data, multiplicity, masking roles, and original sample-size rationale would help readers assess the strength and scope of the evidence. The posted results offer a useful quantitative starting point, but the uncertainties and reporting gaps should remain part of any interpretation.

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 primary comparison is imprecise, with a confidence interval from -312.1 to 127.5 mL. The posted group sizes are 16 and 12, and the primary outcome has substantial within-group spread. These features limit how precisely the trial estimates the group difference. The record does not state a clinically important difference threshold, so it is not possible to determine from the confidence interval alone whether effects of practical importance have been excluded.

The endpoint is calculated rather than directly measured. Its value depends on estimated blood volume, hemoglobin measurements, the Nadler equation, and the adjustment for transfused hemoglobin. The registry does not report validation details, measurement timing beyond the stated intraoperative timeframe, or procedures for handling incomplete laboratory data. Differences in any of these inputs or procedures could affect the resulting endpoint, but their influence cannot be assessed from the record.

Analytical reporting is incomplete. The registry does not report the original sample-size justification, detailed statistical plan, analysis population, missing-data handling, multiplicity strategy, or interim analyses. It lists no reported analyses despite posting group summaries and comparisons. The record also says single-group in the model field even though allocation is randomized and results are posted for EACA and placebo; the reason is not given. The summary’s double-blind description and the quadruple masking field are not reconciled, and masked roles are unspecified.

Numerical secondary results are not posted for every outcome listed, and the available comparisons are unadjusted. The safety record contains zero events in the reported categories, but provides no confidence intervals or detailed ascertainment information. These limitations restrict conclusions about less common events and the overall recovery profile. The findings should therefore be interpreted as a limited registry record of a small randomized comparison, not as a comprehensive analysis of every trial outcome.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Effect of Intravenous EACA on Blood Loss and Transfusion Requirements After Bilateral VRO — NCT02257580.
• Registry record last updated 2022-11-23; status last verified 2022-11.
• Results first posted 2022-11-23.
• 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

NCT02257580 is recorded as a completed Phase 4 randomized, placebo-controlled trial sponsored by Hospital for Special Surgery, New York. The registry lists enrollment of 28, a start date of 2015-04-01, and a primary completion date of 2020-10-26. The intervention was intravenous EACA during bilateral VRO; the comparator was normal saline placebo.

The primary endpoint was calculated intraoperative total blood loss. The posted mean was 535.7 mL for EACA and 628.0 mL for placebo. The unadjusted mean difference was -92.3 mL, with a 95% confidence interval from -312.1 to 127.5 mL and an unadjusted p-value of 0.411. This interval indicates substantial uncertainty about the direction and size of the difference.

Secondary results and adverse-event counts are also posted, but the record does not report a complete analysis plan, missing-data procedures, or a multiplicity strategy. The interpretation is limited to the outcomes and summaries documented in the registry.