Topical Tranexamic Acid and Acute Blood Loss in Total Knee Arthroplasty: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Topical Tranexamic Acid and Acute Blood Loss in Total Knee Arthroplasty (NCT01370460), a randomized phase 2 study. The primary outcome is Blood Loss.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-masked, parallel Phase 2 trial sponsored by Henry Ford Health System. The study status is completed. Its recorded start was 2011-06, and primary completion was 2012-09. Enrollment was 101. The posted arm counts are 51 for placebo and 50 for tranexamic acid.

Participants were assigned to topical tranexamic acid or placebo during unilateral total knee arthroplasty. Tranexamic acid was described as 2g/100mL; the placebo was 100mL 0.9% NS. The parallel design means the two groups were followed as separate arms rather than participants crossing between treatments. The record states that the trial was randomized and triple masked, but does not report the randomization procedure, allocation concealment, the identities of the masked groups, or whether masking was maintained throughout the study.

The primary outcome timeframe was the duration of hospital stay, with an expected average of 3 days. The secondary outcome, postoperative transfusion rate, has the same recorded timeframe. The record does not provide a more detailed follow-up schedule or describe whether participants could be assessed after discharge.

The trial’s original sample-size justification and design assumptions are not reported in the registry record. Nor does the record describe a protocol-defined analysis population, planned interim analyses, or a prespecified statistical analysis plan. These absences limit the ability to judge how closely the posted analyses follow the original protocol. The planning illustrations associated with the posted effect are separate from the trial’s own design rationale.

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: We planned on 50 patients in one treatment arm and 51 in another, resulting in 101 overall patients.

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 Blood Loss, measured over participants will be followed for the duration of hospital stay, an expected average of 3 days.

The primary endpoint is blood loss, expressed as a mean in mL. The registry describes it as calculated from the difference between preoperative hemoglobin and the lowest postoperative hemoglobin. That change, recorded in g/dL, was converted to an estimated blood-loss volume using formulas cited in the registry description. The result is therefore a calculated measure, not a direct collection or measurement of all blood lost during surgery and recovery.

Using a continuous outcome allows the comparison to use each group’s mean blood-loss estimate, rather than reducing the result to a simple yes-or-no event. The standard deviation describes how much individual measurements vary around each group mean. This helps readers understand that a group average does not describe every participant’s outcome. The record does not provide a separate clinical threshold for interpreting the amount of blood loss.

Hemoglobin-based estimates can be useful for comparing groups when the same measurement and calculation approach is applied across arms. Their interpretation still depends on the validity of the conversion formulas and on how the measurements were obtained. The registry refers to cited formulas but does not give enough detail to evaluate their implementation or the handling of missing hemoglobin measurements. The outcome was assessed over the hospital stay, with an expected average of 3 days.

7. Results Posted in the Registry

• Tranexamic Acid: mean 940.20 versus 1,293 on control; difference -352.90 (95% CI -524.93 to -180.87), standardized effect d = -0.80; 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.

Postoperative Transfusion Rate

• 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:
  • Tranexamic Acid: 0.0% (0/50) versus 7.8% (4/51) on control; risk difference -7.8 percentage points (95% CI -15.2 to -0.5); unadjusted two-proportion z-test p = 0.043.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Tranexamic Acid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Postoperative transfusion rate is the single posted secondary outcome. It concerns a related but distinct aspect of postoperative blood loss: whether a transfusion was recorded during the hospital stay. The primary endpoint is a continuous calculated estimate, while this secondary measure is a binary event count. Considering both types of outcome can provide complementary descriptions, but they are not interchangeable and need not show the same degree of precision.

The secondary comparison points in the same direction as the primary comparison in the posted results. That directional consistency is useful descriptive context, but it does not make the outcomes independent confirmation of one another. Both were recorded in the same trial population and over the hospital stay, and the secondary event count is sparse. The registry does not report further secondary outcomes or adjusted analyses.

Unadjusted secondary results carry less weight because they may be exploratory and because multiple outcomes create opportunities for findings to appear noteworthy by chance. The registry record does not state whether the secondary outcome was prespecified in a formal analysis plan, whether any multiplicity adjustment was planned, or how the result should be ranked relative to other outcomes. No adjustment should be assumed.

For that reason, the secondary result is best interpreted as a supporting observation rather than as a stand-alone definitive test. Its meaning depends on the event definition, completeness of recording, and analysis choices, details that are not fully reported in the registry record. The pattern can be considered alongside the primary result, but it does not resolve uncertainty about the primary endpoint’s measurement or the broader limitations in reporting.

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

• Postoperative Transfusion Rate

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant has a calculated blood-loss value in mL, and the registry reports a mean and standard deviation for each arm. A mean summarizes the group’s average value. A standard deviation describes the spread of individual values around that mean; it is not the uncertainty in the mean itself. In general, a large spread means that individual outcomes vary more widely, even when the group mean is estimated with reasonable precision.

What does the mean difference represent?

The posted mean difference compares the tranexamic acid mean with the placebo mean. Its estimate is -352.9 mL. A negative value means the reported mean was lower in the tranexamic acid group under that subtraction order. The estimate is a difference between group summaries, not a statement that each participant’s blood loss changed by that amount. The confidence interval, -524.9 to -180.9 mL, expresses uncertainty about the group difference under the analysis method.

In general, a confidence interval combines an estimated effect with its sampling uncertainty. A narrower interval indicates greater precision than a wider interval, for the same type of estimate and method. It is not a range containing a fixed proportion of individual participant outcomes. Its conventional confidence interpretation depends on repeated use of the statistical procedure under the assumptions of the model. The registry does not report an adjusted primary analysis, so the posted comparison is an unadjusted group-level comparison.

How should the p-value be read?

The primary unadjusted p-value is <0.001. In general, a p-value is calculated by comparing the observed data with what would be expected under a specified null hypothesis and statistical model. It measures compatibility between the data and that null model; a small value indicates relatively low compatibility under the test assumptions. It is not the probability that the null hypothesis is true, and it does not indicate the probability that the result will be repeated. It also does not convey the practical importance of the estimate, which requires substantive context not reported in the registry record.

The secondary outcome is binary, recording whether a postoperative transfusion occurred. The posted group counts are 4 participants in the placebo arm and 0 in the tranexamic acid arm. The registry reports the risk difference for tranexamic acid relative to placebo as -0.078, with a confidence interval from -0.152 to -0.005. A risk difference expresses the difference between the two observed group proportions on the probability scale. The negative sign indicates a lower observed proportion in the tranexamic acid arm under the stated comparison order. The unadjusted p-value is 0.043.

In general, binary outcomes with few events can yield uncertain estimates: a small change in event counts can noticeably affect the group proportions and their difference. That is one reason to consider the confidence interval and the event counts alongside a p-value. The registry does not report an adjusted secondary analysis or additional details about the test used.

Why does over-dispersion matter?

In general, over-dispersion means that the observed variability is greater than a statistical model expects. When a model understates variability, standard errors may be too small and confidence intervals may be too narrow. This concept is especially relevant to count or clustered data, but the registry does not report that an over-dispersion model was used for these outcomes. The primary endpoint is reported as a continuous measure with standard deviations, and the secondary endpoint is a binary participant count. No extra model assumptions should be inferred from those summaries alone.

What is the role of the planning illustrations?

The planning illustrations use the observed primary effect as a starting point and show hypothetical participant requirements under stated assumptions. They are not a reconstruction of the trial’s original design calculation. In general, power is the probability that a specified statistical procedure will reject its null hypothesis when a particular effect is true, under the assumptions used for planning. The illustrations vary the effect to be detected and report participants per arm for 80% and 90% power. They do not show the probability that the observed result is correct, nor do they measure the power achieved by this completed trial.

The registry’s planning assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For the primary comparison, the effect to detect is expressed as a fraction of the observed effect. The registry does not report the original trial’s sample-size justification, nor does it state that these later planning assumptions were used to design the trial.

All reported inferences depend on the accuracy of the recorded outcomes, the analysis choices, and the assumptions behind the statistical methods. The registry record does not provide enough detail to independently verify those choices. Statistical significance should therefore be read together with the estimated magnitude, confidence interval, study design, and limitations in reporting.

11. Confidence Intervals and Precision

The primary mean difference is -352.9 mL, with a 95% confidence interval from -524.9 to -180.9 mL. The interval is entirely below zero, in the same direction as the observed lower mean in the tranexamic acid group. Its span indicates that the data are compatible with a range of group differences, rather than identifying one exact effect. The interval describes uncertainty in the estimated difference; it does not describe the spread of individual blood-loss values, which is reflected separately by the reported standard deviations.

The secondary risk difference is -0.078, with a confidence interval from -0.152 to -0.005. This interval also lies below zero, though the secondary event counts are sparse. In general, estimates based on few events can be sensitive to the event pattern, and interval width is important when considering how precisely a risk difference has been estimated. The registry’s unadjusted p-value for this comparison is 0.043; that value does not replace the interval’s information about uncertainty.

Confidence intervals do not account for every possible source of uncertainty. They do not, by themselves, address unreported missing observations, departures from the analysis plan, measurement error, or bias. The registry record does not provide enough information to evaluate these issues. Nor does it state a threshold for a clinically important difference, so statistical precision cannot be translated into a judgment about clinical importance from the record alone.

In general, a confidence interval is most informative when considered with the point estimate, the measurement scale, the design, and the assumptions of the analysis. The posted intervals quantify sampling uncertainty under the reported comparisons; they do not guarantee replication or establish that the estimated effects apply beyond the studied participants.

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.

Each planning figure represents participants per arm for the stated power level; these are not total event counts. 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 registry record does not report the assumptions or justification used for the trial’s original sample-size design.

For planning at 100% of the observed effect, the illustration gives 25 participants per arm for 80% power and 34 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 44 participants per arm for 80% power and 59 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 99 participants per arm for 80% power and 133 participants per arm for 90% power.

In plain terms, 80% power is the planned chance of detecting the specified effect under the assumptions if that effect is real; the 90% column uses a higher target chance. Neither is a probability that the study’s conclusion is correct. Smaller effects require more participants to detect under the same planning assumptions, which is why the participant requirements rise as the assumed fraction of the observed effect falls. These figures are planning illustrations based on the observed effect, not observed power.

The display’s curve should be read as a visual expression of that relationship between the assumed effect size and the required participants per arm. It does not add information about the trial’s actual randomization, missingness, or outcomes. Since the original design assumptions are not reported in the registry record, the planning illustration should not be mistaken for evidence about the choices made before enrollment.

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 = -352.900; pooled standard deviation σ = 443.029.
2. n = 2 × (1.96 + 0.842)² × 443.029² / -352.900² = 24.7, rounded up to 25 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 <- -352.9                      # observed difference in means
sigma <- 443.028952128687                     # 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(1370460)
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 = 25 (80% power), 34 (90% power)
 75% of observed effect: n per arm = 44 (80% power), 59 (90% power)
 50% of observed effect: n per arm = 99 (80% power), 133 (90% power)
power.t.test: 25.7 
Simulated power at n = 25 per arm: 0.791 (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 a primary outcome and one secondary outcome, but the analysis field lists no reported analyses. It does not report a statistical analysis plan or say whether additional outcomes were considered during the study. The record also does not state whether there was a prespecified hierarchy among outcomes or whether any correction for multiple testing was planned. Therefore, the posted unadjusted p-values should not be interpreted as accounting for multiplicity.

Multiplicity matters in general because examining multiple outcomes or analyses can increase the chance of observing a small p-value even when no true effect exists. The degree of that concern depends on the full set of analyses that were planned and performed. Since that full set and any adjustment procedure are not reported in the registry record, the extent of multiplicity cannot be assessed from the posted information. This does not invalidate the reported estimates, but it limits how strongly nominal p-values can be used as confirmatory evidence.

The record does not report how missing outcome measurements were handled, whether any participants were excluded from an analysis, or which analysis population was used. It also does not provide participant flow or reasons for missingness. These omissions prevent assessment of whether the posted group summaries include everyone assigned to the arms or only participants with available measurements. Missingness can affect interpretation if the availability of outcomes is related to group assignment or to the outcomes themselves.

Randomization can support a fair comparison when assignment and analysis are handled appropriately, but the registry does not provide enough information to assess allocation methods, adherence, or analysis population choices. No interim analyses are reported; whether any were planned or conducted is not reported in the registry record. The original sample-size justification and analysis plan are also not reported. These gaps make it difficult to distinguish confirmatory analyses from exploratory reporting.

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

The posted primary results describe lower mean calculated blood loss in the tranexamic acid arm than in the placebo arm during the recorded hospital-stay timeframe. The estimated mean difference is -352.9 mL, with a confidence interval from -524.9 to -180.9 mL. This is a summary of the comparison in this randomized trial, using the registry’s hemoglobin-based calculation; it is not a direct measure of every aspect of blood loss or recovery.

The result does not show that all participants in one group had lower blood loss than all participants in the other group. The reported standard deviations show variation within each arm, and group averages cannot describe individual outcomes. The posted statistics also do not determine whether the difference is clinically important. The registry does not report a threshold for clinical importance, so statistical evidence and clinical meaning cannot be equated from these data alone.

The secondary transfusion result is a separate outcome and should be interpreted with added caution because it is secondary and the event count is sparse. Its unadjusted statistical result does not establish a broad effect on all outcomes, and it does not compensate for missing detail about prespecification or multiplicity.

These findings do not establish how the comparison would apply outside the studied trial or in other clinical settings. The record gives limited information about participant eligibility and characteristics, the allocation procedure, missing data, and analysis populations. It also does not describe the detailed methods used to assess or record outcomes. Those unknowns restrict assessment of generalizability and robustness.

No medical advice follows from the registry summaries. The results are best understood as estimates from a completed Phase 2 randomized trial, together with uncertainty and reporting limitations. They neither prove that a treatment will produce the same result in every setting nor establish an outcome for an individual participant.

16. Why This Trial Matters Statistically

This trial offers a useful statistical example because it reports both a continuous primary outcome and a binary secondary outcome. The continuous measure uses a mean difference and standard deviations, while the transfusion outcome uses event counts and a risk difference. These measures answer related but distinct questions and illustrate why outcome type determines how a comparison is summarized.

The primary result also highlights the distinction between an estimated effect and its precision. A mean difference provides an interpretable group contrast on the blood-loss scale, while the confidence interval communicates uncertainty around that estimate. The standard deviations describe participant-level variation and should not be confused with uncertainty in the estimated contrast. Reading these summaries together is more informative than relying on a p-value alone.

The registry’s planning illustration is another useful statistical distinction. It shows how required participants per arm change when the assumed effect is smaller or the desired power is higher. Those calculations are based on the observed result and specified planning assumptions, not on the original design rationale. Keeping planning calculations separate from observed trial evidence avoids treating a retrospective illustration as the trial’s actual design basis.

Finally, the record demonstrates why statistical interpretation depends on reporting quality as well as numerical results. The absence of reported analysis details, missing-data handling, and multiplicity procedures leaves important uncertainty about how robust the posted comparisons are. Careful interpretation therefore considers the effect estimates, precision, study design, and limits of the registry record together.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry does not provide a detailed description of eligibility criteria or participant characteristics. This makes it difficult to determine how broadly the results might apply. The record identifies knee osteoarthritis and acute blood loss anemia among the listed conditions, but does not provide the clinical profile of the enrolled group or explain how participants were selected.

The primary outcome is a calculated blood-loss estimate based on preoperative and lowest postoperative hemoglobin, converted using cited formulas. The registry does not provide the measurements themselves, detailed calculation procedures, or information about the timing and completeness of hemoglobin assessment. The estimate therefore depends on both the recorded hemoglobin values and the conversion method.

Further design and analysis details are not reported in the registry record. These include the randomization method, allocation concealment, identities of those masked, analysis populations, missing-data handling, and detailed analysis plan. The record does not report whether outcome assessors or other roles remained masked. It also does not give the original sample-size justification or report whether interim analyses occurred.

The secondary transfusion outcome has few reported events, and no adjusted analysis is posted. The record does not state how transfusion decisions were made or whether the same criteria were applied across arms. Adverse events are marked as not collected, so the registry record cannot support an assessment of adverse-event incidence. These limitations do not change the reported summaries, but they constrain conclusions about completeness, precision, and broader interpretation.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Topical Tranexamic Acid and Acute Blood Loss in Total Knee Arthroplasty — NCT01370460.
• Registry record last updated 2023-04-25; status last verified 2023-03.
• Results first posted 2013-07-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT01370460 is a completed, randomized, triple-masked, parallel Phase 2 trial sponsored by Henry Ford Health System. It compared topical tranexamic acid with topical placebo during unilateral total knee arthroplasty. Enrollment was 101, and the study’s recorded dates were 2011-06 for start and 2012-09 for primary completion.

The primary endpoint was calculated blood loss in mL, based on preoperative and lowest postoperative hemoglobin. The posted unadjusted mean difference was -352.9 mL, with a confidence interval from -524.9 to -180.9 mL and p <0.001. The secondary outcome was postoperative transfusion rate. The registry record does not report a detailed analysis plan, handling of missing data, or adverse-event collection; it marks adverse events as not collected.