Bone Wax Use for Hemostasis During Primary Unilateral Total Knee Arthroplasty: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bone Wax Use for Hemostasis During Primary Unilateral Total Knee Arthroplasty (NCT04992052), a randomized na study. The primary outcome is Blood Loss.

2. Clinical Question

The study asks whether applying bone wax to exposed cancellous bone after cemented implants are in place is associated with less blood loss than not applying bone wax during primary unilateral total knee arthroplasty. The registry describes a prospective, randomized superiority study. The outcome used to address the question is blood loss, calculated using the Hb-balance formula and measured on the morning of postoperative day 1.

The word “superiority” in the official study title describes the trial’s stated aim, not a conclusion. The posted means are lower in the bone-wax arm, but the unadjusted interval estimate includes values on both sides of no difference. The registry record does not report an adjusted analysis or a conclusion from the investigators. The results therefore describe the observed summaries and their uncertainty; they do not, by themselves, establish that one approach is superior.

3. Trial Design

The registry record describes a prospective, randomized, parallel-group study of bone wax use during primary unilateral total knee arthroplasty. It lists 52 participants enrolled and identifies Northwell Health as the sponsor. The study began on 2021-07-27, reached primary completion on 2023-09-12, and is recorded as terminated. The reason for termination is not reported in the registry record.

The official title calls the study single-blinded, while the registry’s masking entry lists double masking. The record does not explain this difference or identify which trial participants or personnel were masked. Random allocation is listed; the allocation ratio and method used to generate or conceal assignments are not reported in the registry record. The study is listed as parallel-group, with one arm receiving bone wax and a control arm receiving no bone wax.

The primary outcome was blood loss, recorded in milliliters and measured on the morning of postoperative day 1. The registry describes calculation using the Hb-balance formula. The primary outcome population note says that one control participant did not have postoperative day 1 blood work, so blood loss could not be calculated for that participant. The posted primary outcome summaries include 29 participants in the treatment arm and 22 in the control arm.

The registry also lists the Knee Society Scoring System as a secondary outcome, collected before surgery and on postoperative day 56 within a stated collection window of +/- 2 weeks. The record lists no reported analyses. It does not report the trial’s original sample-size justification, its planned statistical analysis, or any interim analyses.

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

Analysis population for the primary outcome, as defined in the registry: One patient in the control arm did not have any blood work done on postoperative day 1, therefore, the blood loss analysis could not be calculated.

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 Blood loss is measured the morning of postoperative day 1..

The primary endpoint is blood loss measured on the morning of postoperative day 1. The registry describes calculating it with the Hb-balance formula, which uses hemoglobin information to estimate blood-volume loss. The outcome is continuous, and the posted summaries are means with standard deviations for each arm.

Blood loss is relevant to the study question because the intervention is intended to address hemostasis: the study asks whether applying bone wax to exposed cancellous bone is associated with a different amount of blood loss than leaving the bone untreated. A continuous measure retains information about the amount observed for each participant rather than reducing the outcome to a yes-or-no event. The mean describes the average in an arm, while the standard deviation describes how spread out individual observations are around that average.

The record notes that one control participant had no blood work on postoperative day 1, preventing calculation of the primary outcome for that participant. It does not report a detailed missing-data procedure, whether any other values were unavailable, or whether the analysis population was defined in advance. The endpoint summary should therefore be read in light of the recorded arm counts and the stated missing blood work.

7. Results Posted in the Registry

• Treatment Arm: mean 810.48 versus 905.36 on control; difference -94.88 (95% CI -294.10 to 104.34), standardized effect d = -0.27; z-test p = 0.351.

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.

Knee Society Scoring System

• 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:
  • Treatment Arm: mean 62.55 versus 56.32 on control; difference 6.23 (95% CI -4.43 to 16.89), standardized effect d = 0.35; z-test p = 0.252.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome, the Knee Society Scoring System. Its posted summaries give arm means and standard deviations, and the recalculated unadjusted comparison has a positive point estimate for the treatment arm. Its interval includes zero, and the unadjusted p-value is 0.252. The record lists no reported analyses, so these comparative statistics are recalculations from the posted summaries rather than investigator-reported tests.

The secondary result does not provide a clear independent confirmation of the primary result. It measures a different construct from blood loss and is collected on a different schedule: the score was collected within two months before surgery and on postoperative day 56 with a collection window of +/- 2 weeks. It may therefore add information about a patient-reported or functional dimension, but it cannot substitute for the primary blood-loss endpoint. The registry does not report an analysis of change from baseline or an adjusted comparison accounting for the preoperative score.

As a general statistical matter, secondary outcomes often support interpretation or generate questions rather than carry the same evidential weight as a prespecified primary outcome. If multiple outcomes are examined, the chance of finding at least one apparently notable result can increase unless the analysis plan addresses multiplicity. The record does not report whether the investigators planned a hierarchy of outcomes, an adjustment for multiple comparisons, or a separate confirmatory role for the Knee Society Scoring System.

For that reason, the secondary outcome should be viewed as supportive descriptive information with substantial limitations in interpretation. Its direction and uncertainty can be considered alongside the primary result, but it does not resolve the uncertainty around the blood-loss comparison. No conclusion about a broad treatment effect should be drawn by combining distinct outcomes without a prespecified method for doing so.

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

• Knee Society Scoring System

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure, summarized by an arithmetic mean and standard deviation in each arm. A mean is the sum of the observed values divided by the number of observations; it describes the center of the data on the outcome’s original scale. A standard deviation describes the typical spread of observations around the mean. It is not the uncertainty in the mean itself: uncertainty in a group mean also depends on the number of observations.

What does the mean difference represent?

The posted comparison is expressed as a mean difference, with the treatment arm contrasted against the control arm. A negative value means the treatment-arm mean is lower than the control-arm mean, while a positive value would mean it is higher. For the primary endpoint, the recalculated unadjusted difference is -94.88 milliliters. This is an absolute difference on the blood-loss scale, not a percentage change or a standardized effect.

The comparison is described as unadjusted because it is calculated from the posted group summaries without adjustment for other participant characteristics or covariates. The registry does not report an adjusted model or identify covariates used in an analysis. An unadjusted comparison can be useful for describing the arm summaries, but it does not account for possible baseline imbalances or other factors that might affect the outcome.

How should the interval be read?

An interval estimate communicates uncertainty around an estimated difference. In general, a wider interval indicates less precision, and an interval containing zero is compatible with no difference as well as with differences in either direction. The primary interval extends from -294.1 to 104.3 milliliters, so it includes zero and values on both sides. The confidence level for the posted interval is not reported in the registry record; it should not be assigned a level that the record does not specify.

The interval is not a range within which every participant’s blood loss fell, nor does it say that all values inside it are equally plausible. It is an estimate of uncertainty about the group-level mean difference under the assumptions used for its calculation. The registry record does not describe those assumptions in a reported analysis plan. Its absence means that readers cannot verify from the record whether the interval corresponds to a particular model, whether adjustments were intended, or how the investigators planned to handle departures from model assumptions.

Why do the standard deviations matter?

Standard deviations describe participant-to-participant variation. When outcomes vary substantially within each arm, it can be difficult to distinguish a true difference between arm means from random variation, especially with limited sample sizes. The primary arm standard deviations are 342.5 and 371.9 milliliters, while the mean difference is much smaller in magnitude than either arm’s spread. That contrast helps explain why the estimate is imprecise, but it does not by itself establish the cause of the uncertainty.

Many common methods for comparing means rely on assumptions about the distribution of observations or the behavior of the sampling distribution of the mean. General statistical practice is to consider whether the data contain strong skew, outliers, or unequal variability, and whether the chosen method is appropriate for the sample size and design. Those diagnostic checks and the analysis method are not reported in the registry record. It is therefore not possible to say which assumptions the investigators assessed or whether a different method was planned.

Over-dispersion is a general concern when observed variability is greater than a model expects. If a method assumes less variation than the data actually contain, standard errors can be underestimated and intervals can be too narrow. Conversely, an appropriate variance estimate can reflect the observed spread. The posted arm standard deviations describe variability, but the registry does not report a model-based over-dispersion assessment or an adjustment for it.

What do the p-value and analysis record say?

The p-value of 0.351 is an unadjusted recalculation based on the posted summaries. In general, a p-value measures how incompatible the observed data are with a specified null model, assuming the model and test assumptions hold. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry record lists zero reported analyses, so this p-value should not be mistaken for an investigator-reported primary analysis or for evidence that the study used a particular test.

The registry’s sample-size assumptions describe a separate planning illustration based on the observed effect, equal allocation, a two-sided significance level of 0.05, and a normal approximation. These are not identified as the original trial design assumptions. The original sample-size justification, planned test, analysis population, multiplicity strategy, and any interim-analysis plan are not reported in the registry record.

In general, random allocation aims to make treatment groups comparable on average, including for characteristics not measured. It does not guarantee identical groups in a particular trial, and the record does not provide enough baseline information to assess balance. Masking can reduce certain forms of bias, but the registry’s title and masking entry differ, and the record does not explain who was masked. These design details matter when interpreting an outcome, yet they cannot be resolved from the posted information.

11. Confidence Intervals and Precision

The primary mean difference is -94.88 milliliters, with an interval from -294.1 to 104.3. The estimate points toward lower mean blood loss in the bone-wax arm, but the interval is wide enough to include no difference and differences in either direction. The result is therefore not precise enough to support a narrow statement about the size or direction of the underlying arm difference.

In general, an interval estimate is a range of values compatible with the observed data under the method’s assumptions. Its width reflects sampling variability and the analysis method. It is not a guarantee that the true effect lies within the interval, and it does not describe the range of individual participant outcomes. The confidence level attached to this interval is not reported in the registry record, so its nominal coverage cannot be specified from the record.

The primary arm standard deviations, 342.5 and 371.9 milliliters, show notable spread in blood-loss values. The posted outcome counts are 29 in the treatment arm and 22 in the control arm. The control-arm note identifies one participant without postoperative day 1 blood work, for whom the endpoint could not be calculated. Missing outcome information and variation among observed values both matter to precision, but the record does not provide a fuller missing-data assessment or sensitivity analysis.

The interval should be read together with the point estimate and p-value, not in isolation. The p-value is 0.351, but the interval communicates more directly that the data do not narrowly locate the mean difference. A result that does not show a clear difference is not equivalent to a result demonstrating equivalence. No equivalence margin or non-inferiority margin is reported in the registry record.

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 estimates are participants per arm, not total events. They are illustrations calculated from the observed effect, with equal allocation between two arms, a two-sided significance level of 0.05, and a normal approximation. The scenarios use the full observed effect and smaller fractions of that effect. These assumptions describe the planning illustration; the trial’s original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a hypothetical study to have an 80% chance of detecting the stated effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column expresses the corresponding planning target for a 90% chance. Power is a design property under specified assumptions, not a guarantee that a study will produce a statistically significant result.

The rows that plan for 75% or 50% of the observed effect use smaller target differences than the full observed effect. Smaller effects are harder to distinguish from random variation, so those scenarios require more participants per arm. The values are planning illustrations rather than a reconstruction of the original trial design. They are not observed power; observed study results do not determine a retrospective probability that the trial had power.

The displayed estimates depend on the observed effect, which is uncertain and may differ from the effect in a future study. Equal allocation and the normal approximation are also assumptions of this calculation. The registry does not report whether the original trial used these assumptions, selected another target effect, allowed for missing outcomes, or planned a different sample-size method. The illustration is best used to understand how sample-size requirements change with the target effect and desired power, not as evidence of the investigators’ original planning.

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 = -94.880; pooled standard deviation σ = 355.390.
2. n = 2 × (1.96 + 0.842)² × 355.390² / -94.880² = 220.2, rounded up to 221 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 <- -94.88                      # observed difference in means
sigma <- 355.39038149216                     # 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(4992052)
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 = 221 (80% power), 295 (90% power)
 75% of observed effect: n per arm = 392 (80% power), 525 (90% power)
 50% of observed effect: n per arm = 881 (80% power), 1,180 (90% power)
power.t.test: 221.2 
Simulated power at n = 221 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 two outcome measures and identifies blood loss as the primary endpoint and the Knee Society Scoring System as a secondary outcome. It lists no reported analyses. The record does not describe a prespecified statistical analysis plan, a hierarchy among outcomes, or any adjustment for multiple comparisons. Consequently, it is not possible to determine whether the secondary outcome was intended to be confirmatory, exploratory, or interpreted under a multiplicity procedure.

Multiplicity matters because examining several outcomes or several analyses can increase the chance of an apparently notable result arising by chance. General approaches include prespecifying a primary comparison, adjusting significance thresholds, or interpreting secondary results as exploratory. The registry record does not say which, if any, approach was planned. The posted unadjusted recalculations should therefore not be treated as multiplicity-controlled evidence.

For the primary endpoint, the record explicitly notes that one control participant did not have postoperative day 1 blood work, so blood loss could not be calculated. The outcome summaries list 29 treatment participants and 22 control participants. The secondary outcome summaries include 22 treatment participants and 19 control participants. The record does not provide a full accounting of missing observations for the secondary outcome or explain why its analysis counts differ from those for blood loss.

The registry does not report whether the analysis followed intention-to-treat principles, used a per-protocol population, or applied another analysis-population definition. It also does not describe imputation, complete-case handling, sensitivity analyses, or assumptions about why values were missing. These omissions limit assessment of whether missing data could have affected the results. The record’s note about the control participant explains why that participant’s primary outcome could not be calculated, but it does not establish how all missingness was handled.

The original sample-size justification, planned interim analyses, stopping rules, and statistical decision criteria are not reported in the registry record. The terminated status is recorded, but the reason for termination and any effect of the termination on planned enrollment or analysis are not reported. These gaps prevent a full assessment of how the observed results relate to the original trial plan.

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 summaries list 29 participants at risk in the treatment arm and 23 in the control arm. No serious adverse events, other adverse events, or deaths are recorded in either group. No serious-event terms are listed.

These figures describe the events recorded in the registry summaries. They do not establish that no events occurred outside the recorded categories or observation period, and they do not provide information about event severity beyond the serious-versus-other classification. The record does not give a detailed safety follow-up period, event definitions, or a narrative explanation of how events were collected.

The adverse-event group counts differ from the primary blood-loss outcome counts, particularly in the control arm. The registry does not explain this difference, so the at-risk counts should not be assumed to be the analysis counts for blood loss. With no events recorded in the listed categories, a comparative safety effect cannot be estimated from these summaries. The figures should be read as registry-reported event counts, not as proof that the intervention has no risks.

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

The posted primary summaries show mean blood loss of 810.5 milliliters in the bone-wax arm and 905.4 milliliters in the control arm. The recalculated unadjusted mean difference is -94.88 milliliters. Its interval, from -294.1 to 104.3, includes zero and spans effects in either direction. The unadjusted p-value is 0.351. Together, these statistics describe an observed difference with substantial uncertainty; they do not establish that bone wax is superior or that the approaches are equivalent.

The study was designed with a superiority aim according to its official title, but the registry does not report the original statistical plan or an investigator-reported analysis. No significance threshold for the primary analysis is reported in the record, and the sample-size illustration is not evidence of the trial’s original design. The displayed recalculation is therefore a descriptive statistical comparison, not a substitute for the planned analysis.

The endpoint is a blood-loss measure calculated from hemoglobin information on postoperative day 1. Its relevance to hemostasis does not make it a complete measure of all outcomes that may matter. The registry also lists a secondary scoring outcome, but it does not report an adjusted analysis or a combined interpretation of outcomes. The available summaries cannot establish broader effects beyond the measured endpoints and timeframes.

Interpretation is further limited by the outcome counts and incomplete reporting. The record identifies missing postoperative blood work for one control participant, but does not provide a full account of missing data or analysis populations. The study is marked terminated, with the reason not reported in the registry record. These registry entries do not explain the observed result, but they constrain conclusions about the completeness and intended conduct of the trial.

In general, a trial result describes evidence in the studied participants under the methods used; it does not by itself guarantee the same pattern in other settings or populations. Here, details about eligibility, baseline characteristics, the original sample-size rationale, analysis assumptions, and the identities of masked groups are not reported in the registry record. Conclusions should remain limited to the posted summaries and their uncertainty.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should not be read alone. The primary mean difference points toward lower blood loss in the treatment arm, but the interval is broad and includes zero as well as values in the opposite direction. The unadjusted p-value also does not indicate a clear separation. Looking at the estimate, interval, and observed variation together gives a more informative account than treating the direction of the means as a conclusion.

It also highlights the distinction between a study’s stated aim and evidence that the aim was met. The official title describes a superiority study, yet the registry record does not report an investigator analysis or the planned decision criteria. A recalculated comparison from arm summaries can describe the observed data, but it cannot reconstruct the original inferential plan. Statistical interpretation depends on both the result and the method specified before observing it.

The record further shows how endpoint availability and reporting shape interpretation. A missing postoperative blood test prevented calculation of one control participant’s primary outcome, and the secondary outcome has different arm counts. Without a fuller accounting of missingness and analysis populations, readers cannot assess whether those differences are consequential or how the investigators handled them.

Finally, the sample-size illustration demonstrates the general relationship between effect size and required enrollment: planning to detect a smaller difference calls for more participants under the stated assumptions. That illustration is distinct from the original design rationale, which is not reported. Together, these features make the trial useful for learning how uncertainty, missing information, and analysis-plan transparency affect the strength of conclusions from randomized studies.

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 registry record has several trial-specific reporting limitations. It lists the study as terminated but does not report the reason. It also does not give a full participant disposition, explain the difference between enrollment and outcome counts, or provide baseline characteristics with which to assess balance between randomized groups.

The masking information is inconsistent across registry entries: the official title describes the study as single-blinded, while the masking field lists double masking. The record does not identify who was masked or clarify the difference. Allocation is listed as randomized, but the sequence-generation and concealment methods are not reported in the registry record.

The primary outcome note identifies missing postoperative blood work for one control participant. The record does not describe the missing-data method, a sensitivity analysis, or an analysis population. It also does not explain the different group counts for the adverse-event summaries and clinical outcomes. These details make it difficult to assess the effect of missingness or to determine which participants contributed to each analysis.

The registry lists no reported analyses and does not report the original sample-size justification, the planned statistical method, multiplicity handling, interim analyses, or stopping rules. The secondary outcome’s collection schedule is stated, but the record does not describe a change-score analysis or adjustment for baseline score. The confidence level attached to the posted intervals is also not reported in the registry record.

These are limits on what can be concluded from the registry information; they do not show that a particular method was or was not used outside the record. The posted summaries permit descriptive comparisons, but not a comprehensive evaluation of the trial’s conduct or prespecified statistical decisions.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bone Wax Use for Hemostasis During Primary Unilateral Total Knee Arthroplasty — NCT04992052.
• Registry record last updated 2023-11-21; status last verified 2023-11.
• Results first posted 2023-11-21.
• 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

NCT04992052 is a randomized, parallel-group study of bone wax applied to exposed cancellous bone during primary unilateral total knee arthroplasty, compared with no bone wax. The registry lists 52 participants enrolled, identifies Northwell Health as sponsor, and records the study as terminated. Its official title describes a prospective superiority study; the reason for termination is not reported in the registry record.

The primary outcome is blood loss measured on the morning of postoperative day 1 using the Hb-balance formula. The posted arm summaries show a lower mean in the treatment group, while the recalculated unadjusted interval includes no difference and the p-value is 0.351. The record lists the Knee Society Scoring System as a secondary outcome and reports no analyses.

Important details—including the original sample-size justification, planned analysis, missing-data strategy, and reason for termination—are not reported in the registry record. The results are best interpreted as descriptive arm summaries with considerable uncertainty, rather than as a definitive demonstration of superiority or equivalence.