Improving Function After Knee Arthroplasty With Weight-Bearing Biofeedback: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Improving Function After Knee Arthroplasty With Weight-Bearing Biofeedback (NCT01333189), a randomized na study. The primary outcome is Weight-bearing Ratio During Five Times Sit-to-Stand Test (FTSST).

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, single-masked, factorial-model study sponsored by the University of Colorado, Denver. The recorded enrollment is 26. The listed phase is NA. The registry record gives a start of 2011-01 and primary completion of 2012-12. It does not report the masking role, the allocation procedure beyond randomization, or details of the factorial structure.

The comparison was between weight-bearing biofeedback exercise and standard-of-care exercise after total knee arthroplasty. Biofeedback sessions were delivered by a physical therapist twice weekly for 30 minutes across 6 weeks, in addition to standard rehabilitation. The standard-care group had two weeks of home rehabilitation with six visits, followed by four weeks of outpatient rehabilitation. The record says the total exercise dose across groups was matched, but further details of how dose was defined are not reported in the registry record.

The primary endpoint was weight-bearing ratio during the Five Times Sit-to-Stand Test at 6 weeks post-operative. The registered ratio is vertical ground reaction force on the surgical limb divided by that on the non-surgical limb. The endpoint was reported as a mean and standard deviation. At completion of the intervention, the registry notes one dropout in each group, attributed to time constraints or transportation difficulties.

The record lists 12 outcome measures and 20 analyses. It does not report the original sample-size justification, the intended analysis population, the planned handling of missing outcomes, or details of the factorial factors and their analysis. Those omissions limit assessment of how closely the posted results follow the original design and analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: At the completion of the intervention (6 weeks post-operative), one patient from each group had dropped out of the study due to either time constraints or transportation difficulties.

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 Weight-bearing Ratio During Five Times Sit-to-Stand Test (FTSST), measured over 6 weeks post-operative.

The primary endpoint is the weight-bearing ratio during the Five Times Sit-to-Stand Test, assessed at 6 weeks post-operative. The task involves repeated transitions between sitting and standing. The registry defines the ratio as vertical ground reaction force on the surgical limb relative to force on the non-surgical limb. A ratio nearer to 1 represents a more even distribution of measured force between the limbs; this is a general interpretation of the ratio’s definition, not a separate clinical threshold reported by the registry.

Weight-bearing symmetry is relevant to the study’s rehabilitation question because the intervention was designed to promote more balanced loading during functional activity. The sit-to-stand task gives a measure during a repeated movement rather than only at rest. It is one of the functional activities identified in the study description, alongside walking.

The registry reports group means and standard deviations for this endpoint. The biofeedback group mean was 0.77 with standard deviation 0.1, and the standard-care group mean was 0.8 with standard deviation 0.11. The posted re-calculation expresses the contrast as the biofeedback mean minus the standard-care mean. These summary values describe the recorded endpoint; they do not by themselves establish whether a difference is important to patients. A threshold for meaningful change is not reported in the registry record.

7. Results Posted in the Registry

• RELOAD: Weight-bearing Biofeedback Exercise: mean 0.77 versus 0.80 on control; difference -0.03 (95% CI -0.11 to 0.05), standardized effect d = -0.29; z-test p = 0.485.

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.

Weight-bearing Ratio During Walking

• 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:
  • RELOAD: Weight-bearing Biofeedback Exercise: mean 0.94 versus 0.92 on control; difference 0.02 (95% CI -0.05 to 0.09), standardized effect d = 0.23; z-test p = 0.565.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RELOAD: Weight-bearing Biofeedback Exercise and the control. The interval gives the range of effects that remain compatible with the data.

Five Times Sit-to-Stand Test (FTSST)

• 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:
  • RELOAD: Weight-bearing Biofeedback Exercise: mean 11.50 versus 12.70 on control; difference -1.20 (95% CI -3.28 to 0.88), standardized effect d = -0.46; z-test p = 0.257.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RELOAD: Weight-bearing Biofeedback Exercise and the control. The interval gives the range of effects that remain compatible with the data.

Walking Speed

• 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:
  • RELOAD: Weight-bearing Biofeedback Exercise: mean 1.20 versus 1.16 on control; difference 0.04 (95% CI -0.13 to 0.21), standardized effect d = 0.19; z-test p = 0.649.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RELOAD: Weight-bearing Biofeedback Exercise and the control. The interval gives the range of effects that remain compatible with the data.

The secondary measures cover loading symmetry during walking, performance on the Five Times Sit-to-Stand Test, walking speed, and joint moments during functional activity. The posted numerical summaries show a mixed pattern rather than a consistent separation between groups across all measures. The registry’s mixed-model analyses also produce different p-values across the reported secondary outcomes. No single directional pattern across function and loading is established by these results.

The re-calculated confidence intervals for the three secondary outcomes with numerical group summaries include zero. The registry’s own analyses report p = 0.891 for walking weight-bearing ratio, p = 0.021 for the sit-to-stand test, and p = 0.068 for walking speed. These registry p-values are model-based results, and the corresponding model estimates and confidence intervals are not reported. The re-calculated summaries and sponsor analyses should not be combined as though they were one method.

Secondary outcomes can help describe whether findings are consistent across measures, but they carry less evidential weight when many outcomes are examined and a testing hierarchy or adjustment is not reported in the registry record. The record lists 12 outcome measures and 20 analyses; it does not state how multiplicity was handled. An isolated p-value from a secondary analysis may reflect a true difference, random variation, or analysis choices, and the posted information cannot resolve those possibilities by itself.

The primary result remains the central comparison for the registered question about weight-bearing symmetry during sit-to-stand. The secondary findings add context but do not replace the primary endpoint or establish a broad effect across rehabilitation outcomes. The registry’s lack of estimates and confidence intervals for its mixed-model secondary analyses further limits assessment of their size and precision.

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

• Weight-bearing Ratio During Walking
• Five Times Sit-to-Stand Test (FTSST)
• Hip, Knee, and Ankle Joint Moments During Five Times Sit-to-Stand Test
• Walking Speed
• Hip, Knee, and Ankle Joint Moments During Walking
• Weight-bearing Ratio During Five Times Sit-to-Stand Test (FTSST)
• Weight-bearing Ratio During Walking
• Five Times Sit-to-Stand Test (FTSST)

9. Statistical Interpretation

10. Statistical Methods Explained

Randomization is intended to balance measured and unmeasured characteristics between comparison groups on average. It helps support a causal interpretation of a group contrast when allocation and follow-up are handled appropriately, but it does not guarantee balance in a small study. The registry states that allocation was randomized and masking was single. Which people were masked and how masking was maintained are not reported in the registry record.

What does the mean difference represent?

The posted re-calculation subtracts the standard-care mean from the biofeedback mean. For the primary endpoint, the result is -0.03. A negative value means that the observed mean ratio was lower in the biofeedback group than in the standard-care group. The ratio’s direction should be interpreted in light of its definition: a value nearer to 1 indicates more balanced measured loading. The difference is a comparison of group averages, not a statement about every participant or the course of recovery for an individual.

Why is a confidence interval useful?

A confidence interval describes the range of estimates that are reasonably compatible with the observed data under the assumptions of the analysis. It communicates precision as well as direction. An interval that includes zero means the data do not rule out no mean difference at the confidence level used for that interval. It does not prove that the true difference is zero, nor does it make all values in the interval equally likely. The registry’s own confidence interval for the primary mixed-model result is not reported, so the re-calculated interval and the sponsor’s result must be distinguished.

How should p-values be read?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, the probability that chance alone caused the results, or a measure of clinical importance. The registry reports p = 0.329 for the primary mixed-model analysis. The unadjusted re-calculation reports p = 0.485. Because these come from different analyses, their values should not be treated as interchangeable.

What is the role of a mixed model?

In general, mixed models can account for correlation among repeated observations or other grouped data, depending on the model structure. The registry labels its analyses “Mixed Models Analysis,” but does not report the model formula, included covariates, correlation structure, or observations used. It is therefore not possible to determine from the record exactly what dependence or adjustment the model addressed. No assumptions about those details should be inferred from the method label alone.

What does standard deviation describe?

In general, a standard deviation describes the spread of individual observations around a group mean. It is not the same as a confidence interval for the mean, and it does not directly express how precisely the between-group contrast is estimated. The primary standard deviations are 0.1 for biofeedback and 0.11 for standard care. The re-calculation uses the posted group summaries to estimate a contrast and its uncertainty. As group sizes are limited, the estimate can remain imprecise even when the observed means are close.

Why does multiplicity matter?

When many outcomes or analyses are examined, the chance of encountering an apparently notable result by chance can rise. This is a general statistical concern, not evidence that a particular result is false. The registry lists 12 outcome measures and 20 analyses, while a multiplicity adjustment or hierarchy for testing is not reported in the registry record. The primary endpoint should therefore be distinguished from the secondary findings, and secondary p-values should be interpreted cautiously.

All re-calculated contrasts are unadjusted comparisons of posted summary statistics. They do not reproduce the sponsor’s mixed-model analysis, and they cannot account for participant-level data, repeated measurements, or model adjustments that are not included in those summaries. The sponsor’s reported analysis remains the registry’s own analysis; the re-calculation offers a transparent, limited comparison based on the reported group means and variability.

11. Confidence Intervals and Precision

The primary re-calculated mean difference is -0.03, with a confidence interval that includes zero. This indicates that the posted group summaries do not pin down the direction of the underlying mean difference with high precision. Values on either side of no difference remain compatible with the re-calculation. The interval is not a statement that every value within it is equally plausible, and it does not settle whether any possible difference would be clinically important.

The group means and standard deviations are based on 12 observations per arm. With limited observations, estimates can be sensitive to the values of individual participants, and uncertainty about the group contrast can remain substantial. The registry notes one dropout from each group by the end of the intervention. The record does not explain whether the posted summaries include only participants with observed outcomes or whether missing values were handled in another way.

The registry’s mixed-model analysis reports p = 0.329 for the primary outcome but does not report its estimated contrast or confidence interval. That missing interval prevents assessment of the sponsor analysis’s precision from the registry record. The re-calculated interval is useful for understanding uncertainty under a simple unadjusted comparison, but it is not a substitute for the sponsor’s model-based estimate.

Precision and statistical significance are related but not identical. A confidence interval helps show which effect sizes are compatible with the data, while a p-value summarizes evidence against a null hypothesis under a particular analysis. Neither alone tells whether an effect matters clinically. The registry record does not report a clinical-importance threshold for this ratio, so the clinical meaning of values compatible with the data cannot be determined from the endpoint results alone.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For these continuous outcomes, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set at the listed fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect, if that effect and the calculation assumptions were correct. The 90% power column uses a higher target chance of detecting that same specified effect and therefore generally requires more participants per arm. These are planning targets, not guarantees of a result.

The rows consider planning for 100%, 75%, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so the corresponding planning calculation requires more participants per arm. The figures vary substantially by endpoint because the observed contrast and variability differ across measures. They should not be read as a recommended final design without considering the study question, analysis plan, feasibility, and other design features.

This is not observed power. It is a prospective planning illustration using the effect estimated in this trial, and the observed effect itself is uncertain. In particular, a small study can yield an unstable effect estimate, so basing future planning only on the observed estimate may not produce a reliable target. The table is most useful for understanding how assumptions about the effect size and desired power influence planning, rather than as a retrospective verdict on the trial.

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 = -0.030; pooled standard deviation σ = 0.105.
2. n = 2 × (1.96 + 0.842)² × 0.105² / -0.030² = 192.7, rounded up to 193 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 <- -0.03                      # observed difference in means
sigma <- 0.105118980208143                     # 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(1333189)
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 = 193 (80% power), 259 (90% power)
 75% of observed effect: n per arm = 343 (80% power), 459 (90% power)
 50% of observed effect: n per arm = 771 (80% power), 1,033 (90% power)
power.t.test: 193.7 
Simulated power at n = 193 per arm: 0.798 (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. Analyses Reported by the Sponsor

The registry reports a mixed-model analysis for the primary outcome with p = 0.329. It does not post the model’s estimated contrast or confidence interval. The unadjusted re-calculation from the group summaries gives a mean difference of -0.03 and p = 0.485, with a confidence interval that includes zero. These results address the same primary endpoint but arise from different analyses: one is the registry’s mixed-model result, and the other is a simple re-calculation from the posted means, standard deviations, and group sizes.

The registry’s own analysis is the trial’s reported analysis and should be distinguished from the re-calculation. The record does not give enough model details or participant-level data to reproduce the mixed-model result or explain the p-value difference. The discrepancy flag is false, but that does not make the methods identical; it indicates no identified discrepancy requiring the sponsor result to take precedence over a conflicting result.

For secondary outcomes, the registry also reports mixed-model p-values, while the re-calculation provides unadjusted contrasts from summary statistics. Those p-values can differ because the analyses may use different structures or assumptions, but the registry does not report enough detail to identify the reason. Neither the re-calculation nor a p-value alone supplies an estimate of clinical importance.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroup comparisons, or statistical tests are examined. In general, making more comparisons increases the possibility of finding a nominally notable result even when no corresponding effect exists. This does not mean that a particular finding is false; it means that the number and organization of analyses matter when judging evidence.

The registry lists 12 outcome measures and 20 analyses. It does not report a multiplicity adjustment, a hierarchy of outcomes, or a rule for interpreting the secondary tests. The primary endpoint is identified, which helps separate the main question from the additional measures, but the record does not explain how the broader family of tests was addressed. The reported secondary p-values should therefore be treated as exploratory or descriptive unless additional analysis-plan information is available.

Missing-data handling is also unclear. The primary outcome description notes one dropout in each group by the completion of the intervention, due to time constraints or transportation difficulties. The record does not state whether the outcome summaries include only participants with measured results, how missing observations were treated in the mixed models, or whether sensitivity analyses were performed. A dropout count alone does not establish the effect of missing data on the estimates.

The analysis population is not reported in the registry record. It is therefore unclear whether the sponsor’s models followed an intention-to-treat approach, a per-protocol approach, or another defined population. The record does not report protocol deviations or the number included in each analysis beyond the group summaries and their reported sample sizes. These omissions make it harder to assess how randomization was preserved in the analyses and how robust the findings are to missing outcomes.

The protocol’s statistical analysis plan, interim analyses, and original sample-size justification are not reported in the registry record. No assumptions about them can be made. These gaps affect interpretation of both the primary analysis and the multiple secondary results, particularly because the sponsor’s model estimates and intervals are not posted.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: late infection (7.7%).

The registry reports serious adverse events for 13 participants at risk in each group. One serious adverse event affected a participant in the biofeedback group, and none affected participants in the standard-care group. The listed serious adverse event term is Late Infection, reported as 7.7%. Other adverse events affected zero participants in either group. Deaths are not reported in the registry record.

These are event counts from a small trial and should be read descriptively. They do not establish whether an event was caused by the rehabilitation intervention, nor do they provide a precise estimate of comparative safety. The registry record does not provide further event narratives or explain the assessment of relatedness. The serious adverse event figures should not be interpreted as a complete safety profile beyond the events reported in the record.

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

The primary endpoint compares average weight-bearing ratios during the Five Times Sit-to-Stand Test at 6 weeks post-operative. The observed group means were close, and the unadjusted re-calculated difference was -0.03. Its confidence interval includes zero, while the registry’s mixed-model analysis reports p = 0.329 without a posted estimate or interval. The evidence in the registry record does not give a precise account of the size of a primary difference.

That finding is not proof that the approaches are identical. A non-significant result does not establish equivalence or exclude effects that the available data could not estimate precisely. An equivalence or non-inferiority conclusion would require an appropriate design, prespecified margins, and analysis; these are not reported in the registry record.

Nor does the primary outcome alone describe all aspects of recovery. The registry includes secondary functional measures and joint moments, but the pattern of secondary results is mixed and multiplicity handling is not reported. The available outcomes do not establish a general improvement across functional tasks. A threshold for clinically meaningful change in the primary ratio is also not reported, so statistical estimates cannot be translated into a clear statement about practical importance.

The results apply to the participants and follow-up described in this trial. The registry record does not provide detailed participant characteristics, the masking role, model specifications, missing-data methods, or an analysis population. The sample-size planning illustrations are not evidence of observed power and do not change what the trial estimates. Overall, the record offers a small randomized comparison with limited precision and incomplete reporting of analysis details; it does not support a definitive claim about comparative clinical benefit.

18. Why This Trial Matters Statistically

This trial illustrates the distinction between a registered analysis and a re-calculation from published group summaries. The sponsor reports a mixed-model p-value for the primary outcome, while the re-calculation reports a simple mean contrast, its confidence interval, and an unadjusted p-value. These answer related questions but are not interchangeable, especially when the model details and model-based estimate are absent.

It also shows why estimates and confidence intervals matter alongside p-values. A p-value gives limited information about effect size and precision. For the primary endpoint, the re-calculated contrast is small in the posted units and its interval includes zero. The sponsor’s primary p-value is available, but its estimate and interval are not. Readers therefore have different levels of information about the two analyses.

The trial has several listed outcomes and analyses, making prespecification and multiplicity important for interpretation. The record identifies a primary endpoint but does not report a testing hierarchy or adjustment. The secondary results can be useful for understanding the breadth of measurement, but isolated findings deserve caution when their place in the analysis plan is unknown.

Finally, the planning illustrations make clear that sample-size requirements depend on the effect selected for detection and the target power. Because those illustrations use the observed effect, they are not a measure of what the trial had power to detect and should not be confused with the original design justification. The original justification is not reported in the registry record. These features make the trial a useful example of how incomplete statistical reporting constrains interpretation, even when group summaries and selected p-values are available.

19. Limitations

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

The primary group summaries are based on 12 observations per arm, and the registry notes one dropout from each group by the end of the intervention. The handling of missing outcomes and the analysis population are not reported. This limits assessment of whether the posted estimates reflect all randomized participants and how sensitive the results are to missing data.

The sponsor reports mixed-model p-values but not the model estimates or confidence intervals. Model specifications, covariates, and the repeated-measure structure are not reported in the registry record. The unadjusted re-calculations cannot reproduce or replace the sponsor’s analysis. A reader cannot determine from the record why the model-based and summary-based p-values differ.

The registry lists multiple outcomes and analyses but does not report a multiplicity strategy. This is especially relevant to interpreting secondary findings. The record also does not report a clinical-importance threshold for the primary ratio, so statistical differences cannot be directly judged against a stated patient-relevant benchmark.

Further trial details are limited: the masking role, allocation procedures, factorial structure, participant characteristics, original sample-size justification, interim analyses, and statistical analysis plan are not reported in the registry record. The intervention descriptions give the main schedules but do not fully characterize treatment delivery or adherence. The reported follow-up for the primary outcome is 6 weeks post-operative, so the record does not establish whether any differences persist later. These limitations narrow what can be concluded about the estimates, conduct, and applicability of the comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Improving Function After Knee Arthroplasty With Weight-Bearing Biofeedback — NCT01333189.
• Registry record last updated 2019-04-23; status last verified 2019-04.
• Results first posted 2015-09-07.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed randomized, single-masked, factorial-model trial sponsored by the University of Colorado, Denver, comparing weight-bearing biofeedback exercise with standard-of-care exercise after total knee arthroplasty. Recorded enrollment was 26. The primary endpoint was weight-bearing ratio during the Five Times Sit-to-Stand Test at 6 weeks post-operative.

The primary group means were 0.77 for biofeedback and 0.8 for standard care. The unadjusted re-calculated difference was -0.03, with a confidence interval including zero and p = 0.485. The registry’s mixed-model analysis reports p = 0.329, but its estimate and confidence interval are not reported. Secondary analyses show a mixed pattern, and multiplicity handling is not reported.

The record notes one dropout in each group and reports one serious adverse event in the biofeedback group and none in standard care. Missing-data methods, analysis population, model details, original sample-size justification, and several other design and analysis details are not reported in the registry record.