Optimizing Local Anesthetic Concentration for Continuous Femoral Nerve Blocks: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Optimizing Local Anesthetic Concentration for Continuous Femoral Nerve Blocks (NCT00923598), a randomized phase 4 study. The primary outcome is Quadriceps Femoris Muscle Strength Maximum Voluntary Isometric Contraction (MVIC).

2. Clinical Question

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel study of continuous femoral nerve blocks for patients undergoing bilateral total knee arthroplasty. It lists Phase 4 and an enrollment of 48. The study status is completed. The registry lists the University of California, San Diego as sponsor and gives the study start as 2009-06 and primary completion as 2011-04.

The treatment comparison uses 0.1% and 0.4% ropivacaine. According to the brief summary, one side was randomized to one concentration and the contralateral side received the other. The arm descriptions define groups according to which concentration was assigned to the right leg. The outcome was to be measured on both legs. This bilateral arrangement is important when interpreting the posted group summaries: the two legs of a participant are linked observations, rather than observations that can automatically be treated as independent.

The study summary says all patients also received the usual analgesic regimen described for bilateral knee arthroplasty, including oral acetaminophen, a sustained-release oral opioid, celecoxib, and rescue opioid selected according to pain severity on a Numeric Rating Scale. These co-interventions form part of the treatment context; the registry does not provide results for their use in the posted primary outcome analysis.

The primary endpoint was quadriceps strength on the morning of postoperative day 2. The registry lists 23 participants in the arm with 0.1% ropivacaine on the right leg and 22 in the arm with 0.4% on the right leg. It does not explain how the analysis handled the paired measurements from each participant, nor does it report the trial’s original design assumptions or a full statistical 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

Analysis population for the primary outcome, as defined in the registry: Patients undergoing bilateral knee replacements

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 Quadriceps Femoris Muscle Strength Maximum Voluntary Isometric Contraction (MVIC), measured over morning of postoperative day 2.

The primary endpoint is quadriceps femoris muscle strength measured as maximum voluntary isometric contraction (MVIC), in newtons, on the morning of postoperative day 2. A dynamometer measured force while the participant contracted the quadriceps as strongly as possible. The device was placed on the anterior tibia on the same side as the measurement, perpendicular to the tibial crest and just proximal to the medial malleolus. Participants were asked to reach maximum effort over 2 seconds, maintain the effort for 5 seconds, and then relax.

MVIC is a continuous measure: it records force on a numerical scale rather than assigning participants to categories. A mean provides a measure of the group’s average recorded force, while the standard deviation describes how spread out individual measurements are around that mean. Measuring the outcome on both legs fits the bilateral treatment arrangement and permits a leg-specific comparison of strength under the two concentrations.

Muscle strength is used as an endpoint because the study is assessing a physical outcome during postoperative recovery, rather than pain alone. However, the registry record does not state a threshold for a clinically important difference in MVIC. The endpoint therefore describes measured strength, but the posted results alone do not establish how a particular difference should be interpreted in clinical terms.

7. Results Posted in the Registry

• 2) 0.4% Ropivicaine on Right Leg: mean 12.00 versus 13.00 on control; difference -1.00 (95% CI -5.68 to 3.68), standardized effect d = -0.12; z-test p = 0.675.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a continuous measurement of force in newtons. For a continuous outcome, a group mean describes the central value and a standard deviation describes variation among measurements. The registry posts means of 13.0 and 12.0, with a standard deviation of 8.0 in each right-leg assignment group. These summaries make it possible to describe the observed arm-level data, but they do not contain every detail needed to reproduce an analysis that accounts for the bilateral design.

What does the recalculated mean difference describe?

The unadjusted recalculation reports a mean difference of -1.0 for the comparison between the group with 0.4% ropivacaine on the right leg and the group with 0.1% on the right leg. It is based on the posted arm summaries. The corresponding 95% confidence interval is -5.676 to 3.676, and the unadjusted p-value is 0.675. “Unadjusted” means this recalculation is not presented as a covariate-adjusted model or as an analysis incorporating additional factors. It is a simple comparison of the posted summaries.

That description needs qualification because the treatment allocation is bilateral: each participant receives one concentration on each leg, and both legs are assessed. The arm labels distinguish which concentration was assigned to the right leg, not a design in which each participant receives only one concentration. Measurements within a participant may be related. A paired comparison uses the within-person difference between legs, and its uncertainty depends on the relationship between the two measurements. The registry record does not post the paired covariance or the participant-level measurements, so the recalculation cannot reproduce a paired analysis from the information available.

What does a confidence interval express?

A confidence interval gives a range of estimates compatible with the data under the statistical procedure and assumptions used. It conveys uncertainty about the estimated contrast; it is not a guarantee that the true value lies inside the particular interval. The recalculated interval includes zero and extends to differences in either direction. The sponsor-reported interval also includes zero, but it has different limits and is attached to a different reported estimate. Because those analyses disagree, their intervals should not be blended or treated as if they came from one model.

What does a p-value express?

A p-value describes how compatible the observed data are with a null hypothesis under a specified statistical model. It does not give the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The recalculated p-value is unadjusted. The sponsor reports p = 0.05 for its analysis and labels that analysis equivalence, but the registry record does not supply the equivalence margin or a detailed account of the test. The method is listed as Fisher Exact even though the reported parameter is a mean difference in final values. The record does not explain that method description.

Why does the equivalence label need context?

Equivalence is a distinct statistical question from whether a conventional test finds evidence of a difference. An equivalence analysis generally evaluates whether the plausible difference falls within prespecified bounds. Those bounds are essential to interpreting the conclusion: without them, readers cannot tell what size of difference the analysis was designed to regard as acceptably small. The registry record does not report such a margin. The sponsor’s analysis should therefore be described as reported, without inferring that its label is independently confirmed by the available statistics.

Why does over-dispersion matter in general?

In general, over-dispersion occurs when the observed variability is greater than a statistical model assumes. If a model understates variability, its uncertainty estimates can be too narrow and its tests can appear more decisive than warranted. This is a general consideration for statistical modeling, not a finding reported for this trial. The registry does not report an over-dispersion assessment or a model diagnostic for the primary outcome.

The registry lists one outcome measure and one analysis, and no secondary outcomes are posted. It does not report how missing measurements were handled, which participants were included in each analysis population, whether an interim analysis was conducted, or a complete statistical plan. Those absences limit assessment of analysis choices and of whether the reported summaries include all randomized participants or all planned measurements.

10. Confidence Intervals and Precision

The recalculated mean difference is -1.0, and its 95% confidence interval runs from -5.676 to 3.676. The interval communicates substantial uncertainty around the point estimate: values indicating a difference in either direction remain compatible with this unadjusted calculation. Because the interval includes zero, it does not provide clear evidence of a nonzero difference under the calculation used. It also does not show that the concentrations are equivalent.

The sponsor-reported estimate is 3, with a 95% confidence interval from -10 to 17. That interval likewise includes zero, but its estimate and limits differ from those of the recalculation. The discrepancy is material to interpretation, and the sponsor’s own analysis takes precedence when reporting the sponsor result. The registry record does not provide the analysis details or equivalence margin needed to reconcile the two sets of results or assess the sponsor’s equivalence claim fully.

Precision is affected by the amount of information in the analysis and by the variability and structure of the data. The posted standard deviation is 8.0 in each arm, and the listed group counts are 23 and 22. In this trial, the bilateral arrangement is particularly relevant: measurements on the two legs of the same participant are paired, but the summaries do not report their correlation. Without that information, the precision of a paired treatment contrast cannot be reconstructed from the arm means and standard deviations alone.

The confidence intervals describe uncertainty under their respective analyses; they do not address unreported outcomes, missing data, or whether the endpoint difference is clinically important. The registry record does not state a clinically meaningful MVIC difference. Accordingly, the posted intervals allow statistical interpretation of the estimated contrasts but do not by themselves settle the practical meaning of the results.

11. 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, not observed trial results. They give participants per arm for the listed continuous-outcome scenarios; they are not total event counts. The planning assumptions stated in the registry 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 trial’s own original design assumptions, including its original sample-size justification, are not reported in the registry record.

The 80% power column describes the planned number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect is present and the assumptions hold. The 90% power column describes the corresponding planning target for a design with a 90% chance under the same conditions. These are design calculations, not measures of the probability that the study’s result is correct.

The rows use the full observed effect and smaller fractions of that effect. Planning for 75% of the observed effect requires more participants than planning for the full observed effect; planning for 50% requires still more. This is the general pattern: smaller effects are harder to distinguish from random variation, so they require more information to achieve the same planned power.

The planning illustration is based on the recalculated observed effect and its stated assumptions. It does not incorporate a paired-data calculation based on the bilateral measurements, because the required within-participant covariance is not reported. It is not observed power.

12. 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 = -1.000; pooled standard deviation σ = 8.000.
2. n = 2 × (1.96 + 0.842)² × 8.000² / -1.000² = 1,004.7, rounded up to 1,005 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 <- -1                      # observed difference in means
sigma <- 8                     # 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(923598)
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 = 1,005 (80% power), 1,345 (90% power)
 75% of observed effect: n per arm = 1,787 (80% power), 2,392 (90% power)
 50% of observed effect: n per arm = 4,019 (80% power), 5,380 (90% power)
power.t.test: 1005.6 
Simulated power at n = 1,005 per arm: 0.802 (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.

13. Analyses Reported by the Sponsor

The sponsor-reported result is a mean difference of 3, with a 95% confidence interval from -10 to 17 and p = 0.05. The registry labels this as an equivalence analysis and lists Fisher Exact as the method. The unadjusted recalculation instead gives a mean difference of -1.0, a 95% confidence interval from -5.676 to 3.676, and p = 0.675. These are not matching estimates or uncertainty intervals.

The discrepancy flag is true, so the sponsor’s own analysis takes precedence when describing the trial’s reported result. The recalculation is a simple unadjusted comparison from the posted arm summaries; it is not a correction to the sponsor’s analysis. The bilateral design further complicates direct comparison because each participant received both concentrations, while the posted arm summaries do not show the within-participant relationship needed to reproduce a paired analysis.

The sponsor’s equivalence label cannot be fully evaluated from the registry record. An equivalence margin and further analysis details are not reported in the registry record. The reported estimate, interval, p-value, and method label can be stated as recorded, but they do not allow independent confirmation of the equivalence conclusion or explain why the recalculation differs.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one outcome measure and one analysis, and no secondary outcomes are posted. This limits the multiplicity questions that can be assessed from the posted results, but it does not establish that no other analyses were planned or performed. The registry record does not report whether the primary analysis was selected from a larger set of outcomes or analyses, or whether any multiplicity adjustment was planned or used.

The registry does not report a complete statistical analysis plan. It also does not report whether interim analyses were conducted. These details matter because repeated testing or choices among outcomes and analysis methods can affect how results should be interpreted. Their absence means the posted information cannot establish the full analysis history.

Missing-data handling is not reported in the registry record. The record does not say whether any leg-strength measurements were missing, how missing measurements were treated, or whether a method was used to account for them. It also does not identify analysis populations, such as whether the primary result included all randomized participants or a subset. The posted group counts are 23 and 22, but the registry does not explain how those counts relate to the enrolled population or to the availability of paired measurements.

Because each participant was described as receiving both concentrations and having both legs assessed, a participant-level paired analysis would require both measurements or an explicit approach to incomplete pairs. The registry record does not state how the analysis handled a missing measurement on one side. Without this information, readers cannot determine whether missingness changed the analysis population or how it may have affected the estimated contrast.

These omissions do not demonstrate that a particular analysis choice was made. They identify information that is not reported in the registry record and that would be needed to assess the analysis more completely.

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 registry reports zero serious adverse events in the group with 0.1% ropivacaine on the right leg, among 23 listed at risk, and zero in the group with 0.4% on the right leg, among 22 listed at risk. It also reports zero deaths in each group. No serious adverse-event terms are listed.

These figures describe the posted serious-event counts for the registry’s arm labels. They do not establish that no events of any kind occurred: the registry separately reports zero other adverse events in each listed group, but adverse-event reporting is limited to what is recorded there. A count of zero is not proof that a risk is absent, especially when the amount of information is limited.

The treatment arrangement was bilateral, with each participant receiving both concentrations on opposite legs. The safety counts are presented by right-leg assignment group, and the record does not explain whether adverse events were attributed by participant, leg, or treatment exposure. It also does not provide event definitions or further safety-analysis details. The figures should therefore be read as registry-reported counts, not as a complete comparison of all possible harms or as a basis for medical advice.

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

The posted primary outcome is quadriceps MVIC in newtons on the morning of postoperative day 2. The arm-level means are 13.0 for the group assigned 0.1% ropivacaine on the right leg and 12.0 for the group assigned 0.4% on the right leg. The unadjusted recalculation gives a mean difference of -1.0, with a 95% confidence interval from -5.676 to 3.676 and p = 0.675. The sponsor reports a different estimate and interval and labels its analysis equivalence.

These results do not establish that the concentrations produce the same strength outcome. Failure to show a clear difference in an unadjusted analysis is not the same as demonstrating equivalence. Assessing equivalence requires prespecified bounds, which are not reported in the registry record. The sponsor’s result should be described as reported, while noting that the recalculation differs and that its method details are incomplete.

The evidence also has a specific scope. It concerns a strength measurement at one postoperative time in patients undergoing bilateral knee replacements, under the analgesic regimen described in the registry. It does not report strength at other times, pain outcomes, rescue medication use, or other secondary outcomes. The registry lists no secondary outcomes. It therefore cannot answer broader questions about all aspects of recovery or the comparative effects of the concentrations on outcomes not posted.

The bilateral design means both concentrations were used by each participant, one on each side. The posted arm summaries are defined by which concentration was assigned to the right leg. Since the within-participant relationship between the left- and right-leg measurements is not reported, the unadjusted recalculation cannot be assumed to reproduce the paired analysis appropriate to the design. The registry record does not provide enough detail to resolve that issue or the discrepancy with the sponsor result.

In short, the posted data describe similar arm-level means, but uncertainty, design-related analysis details, and the sponsor-recalculation discrepancy prevent a definitive interpretation as equivalence. No treatment recommendation follows from these registry statistics.

17. Why This Trial Matters Statistically

This trial illustrates how the unit of randomization and the unit of measurement shape statistical interpretation. The study is described as bilateral: each participant receives both ropivacaine concentrations, one on each leg, and strength is measured on both sides. The arm labels then identify which concentration was assigned to the right leg. This arrangement creates paired measurements within participants, so an analysis that ignores the pairing may not reflect the design’s full information structure.

The posted summaries give group means and standard deviations, but not the within-participant association between leg measurements. That association matters for estimating the uncertainty of a paired difference. It cannot be recovered from the arm-level summaries alone. The example shows why a simple recalculation can be useful as a transparent descriptive comparison while still differing from a design-aware analysis.

The registry also reports a sponsor-labelled equivalence result that differs from the unadjusted recalculation. This highlights the need to distinguish a conventional test for a difference from an equivalence analysis, and to report the equivalence margin that defines what counts as sufficiently close. Without that margin and the underlying analysis details, the sponsor’s label cannot be fully assessed independently.

Finally, the sample-size illustration is based on the observed recalculated effect and stated planning assumptions, rather than the trial’s original design rationale. Such planning calculations show how smaller target effects demand larger samples, but they do not explain the trial’s enrollment or establish observed power. Together, these features make the study a useful example of the importance of matching analysis to design and separating statistical description from broader claims.

18. Limitations

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

The primary limitation for interpretation is incomplete reporting of the analysis for a bilateral design. Each participant was described as receiving both concentrations, with outcomes measured on both legs, but the registry does not report a paired analysis method or the within-participant covariance. The arm-level means and standard deviations cannot reconstruct that information. The unadjusted recalculation should therefore be treated as a summary-based comparison rather than as a reproduction of the intended or sponsor analysis.

The sponsor result and recalculation differ in their estimates, intervals, and p-values. Although the sponsor’s analysis takes precedence when describing the sponsor-reported result, the registry record does not provide enough detail to explain the discrepancy. It lists Fisher Exact for a mean difference and labels the analysis equivalence, but does not report an equivalence margin or a fuller testing procedure. The equivalence conclusion cannot be independently assessed from the posted record.

Additional analysis details are absent. Missing-data handling, analysis populations, interim analyses, the complete statistical plan, and the original sample-size assumptions are not reported in the registry record. The record does not explain how the listed group counts relate to paired outcome availability. No secondary outcomes are posted, limiting interpretation to the single reported endpoint and time point.

The outcome itself is a measurement of quadriceps force on the morning of postoperative day 2. The registry does not state a clinically important difference for MVIC, and the posted primary results do not cover other recovery outcomes or other measurement times. The results should be interpreted within that narrow outcome and timing rather than generalized to unreported endpoints.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Optimizing Local Anesthetic Concentration for Continuous Femoral Nerve Blocks — NCT00923598.
• Registry record last updated 2019-12-02; status last verified 2019-11.
• Results first posted 2019-12-02.
• 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

The registry describes a completed randomized, quadruple-masked, parallel Phase 4 study of 0.1% and 0.4% ropivacaine infusions for patients undergoing bilateral total knee arthroplasty. Enrollment is listed as 48. Each participant was described as receiving both concentrations, one on each leg, with the right-leg assignment defining the two posted arms.

The primary outcome was quadriceps femoris MVIC in newtons on the morning of postoperative day 2. The posted arm means are 13.0 and 12.0, with a standard deviation of 8.0 in each group. The unadjusted recalculation reports a mean difference of -1.0, a 95% confidence interval from -5.676 to 3.676, and p = 0.675. The sponsor reports an equivalence analysis with a mean difference of 3 and a 95% confidence interval from -10 to 17; the analyses differ, and the registry does not report the equivalence margin.

The registry reports zero serious adverse events and zero deaths in each arm. No secondary outcomes are posted. Important details, including paired-analysis methods, missing-data handling, analysis populations, and the trial’s original design assumptions, are not reported in the registry record.