Optimizing Local Anesthetic Concentration for Continuous Popliteal-Sciatic Nerve Blocks: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Optimizing Local Anesthetic Concentration for Continuous Popliteal-Sciatic Nerve Blocks (NCT01898689), a randomized phase 4 study. The primary outcome is Maximum Tolerance to Transcutaneous Electrical Stimulation.

2. Clinical Question

3. Trial Design

This was a Phase 4, randomized, quadruple-masked, parallel-design trial marked completed in the registry. The enrollment was 24, and the study population was relatively healthy volunteers. The recorded study dates are 2013-07 for the start and 2013-11 for primary completion. The sponsor was the University of California, San Diego.

The treatment comparison was conducted within participants rather than between separate groups of participants. The registry describes bilateral sciatic perineural catheters, with ropivacaine administered concurrently through the two catheters. Each participant therefore received both concentrations, one on each side. The record lists 24 participants for each treatment and explains that each of the 24 subjects received each treatment. Thus, the treatment observations are paired: a participant’s outcome under one concentration is related to that same participant’s outcome under the other.

The brief summary describes the intended comparison as ropivacaine 0.1% at 8 mL/hour versus ropivacaine 0.4% at 2 mL/hour, each intended to provide an equivalent total basal dose of 8 mg/hour. The detailed arm descriptions do not consistently match that account. One description gives 0.1% at 8 mL/h and 0.4% at 2 mL/h, while another describes 0.4% at 8 mL/h and 0.1% at 2 mL/h. Both describe a 6-hour infusion. The registry record does not clarify which rate assignment was used for each concentration in the analyzed comparison.

The outcome listing includes the primary measure and two secondary outcomes: maximum tolerance to transcutaneous electrical stimulation and percent of maximum voluntary isometric contraction baseline for the quadriceps femoris. The listed primary outcome was assessed at Hour 6. The original design assumptions, including any sample-size justification, are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Since this was a split-body study, we included each individual who received the treatment. Since each of the 24 subjects received each of the treatments, the overall number of participants analyzed was 24 for each of the treatments. For this reason, the Total number of subjects appears to be '48', when in fact it was 48 treated sides.

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 Maximum Tolerance to Transcutaneous Electrical Stimulation, measured over Hour 6.

The primary endpoint is maximum tolerance to transcutaneous electrical stimulation, measured in mA (milliamperes) at Hour 6. Electrocardiogram pads are placed on the lateral plantar surface of the foot, within the sciatic nerve distribution. A nerve stimulator increases the cutaneous electrical current from 0 mA until the participant detects it, subject to a maximum of 80 mA. The current recorded at detection is the endpoint value.

This measure is used as a sensory response in the territory posted by the sciatic nerve. In this experiment, comparing the response under the two ropivacaine concentrations offers a way to assess how the local anesthetic regimens relate to nerve-block effects. The outcome is a continuous measure: its values can vary across a range rather than being limited to categories such as event or no event.

The registry reports the treatment means and standard deviations at the specified assessment time. The mean was 27.0 mA for ropivacaine 0.1%, with a standard deviation of 20.2, and 26.9 mA for ropivacaine 0.4%, with a standard deviation of 20.4. Those summaries describe the treatment-specific observations, but they do not by themselves show the within-person differences. Because the same volunteers received both treatments, the paired relationship between each person’s two measurements matters when estimating the treatment contrast.

The endpoint is a measurement of electrical-stimulation tolerance, not a direct measure of every aspect of analgesia, muscle strength, or home infusion duration. The registry’s stated primary outcome is specifically this electrical-current response at Hour 6.

7. Results Posted in the Registry

• Ropivacaine 0.4%: mean 26.90 versus 27.00 on control; difference -0.10 (95% CI -11.59 to 11.39), standardized effect d = -0.00; z-test p = 0.986.

8. Statistical Interpretation

9. Statistical Methods Explained

Two types of statistical result appear in the record: the sponsor’s reported mixed-model equivalence analysis and an unadjusted recalculation based on treatment-level summary statistics. They address the same broad treatment comparison, but they are not interchangeable. The sponsor’s analysis takes precedence because the discrepancy flag is true. The recalculation can help readers understand the scale and uncertainty of a simple summary-based contrast, but it is not a replacement for the sponsor’s analysis.

What does the mean difference represent?

A mean difference expresses the contrast between average outcome values for two treatments, in the outcome’s units. Here, the outcome is electrical-stimulation tolerance in mA. The recalculation reports a mean difference of -0.1 for ropivacaine 0.4% relative to ropivacaine 0.1%. Its negative sign indicates that the 0.4% treatment mean is slightly lower in that calculation. The reported treatment means are 26.9 and 27.0, respectively. The difference is a summary of average values; it does not say that every participant had a lower response under one treatment.

The sponsor’s reported net mean difference is 0.2. Its sign and value do not match the recalculated difference. The registry identifies the sponsor result as a mixed-model analysis and the recalculation as unadjusted. Those labels indicate that the results were not produced using an identical analysis approach. The exact model specification and the source of the discrepancy are not reported in the registry record, so a more specific explanation would be speculative.

Why does the split-body design matter?

In a split-body study, each participant receives both treatments, with one treatment applied to each side. The comparison is therefore paired. Each person contributes a measurement under each condition, and the analysis can use how those two measurements relate within that person. Pairing is different from treating the two treatment groups as independent samples.

The registry lists 24 participants for each treatment, and explains that the same 24 subjects received each treatment. These treatment-specific counts should not be interpreted as independent sets of participants. For a paired comparison, the variance of the within-person differences is important. The record supplies the mean and standard deviation separately for each treatment, but does not provide the standard deviation of the paired differences or the individual paired measurements. Those marginal summaries are not enough to reproduce the paired uncertainty exactly.

A mixed model is a general approach for analyzing data with structured relationships, such as repeated or paired measurements. It can account for the fact that observations from the same participant are related. The registry names the method as “Mixed Models Analysis,” but does not report the model terms, covariance structure, estimation details, or missing-data handling. It is therefore possible to explain why a mixed model may be appropriate for a split-body design, but not to reconstruct the sponsor’s exact model from the registry record.

What is an equivalence analysis?

Equivalence is a distinct statistical question from whether a treatment difference is exactly zero. An equivalence analysis usually evaluates whether the plausible treatment difference lies within a prespecified range judged sufficiently small for the study question. That range is called the equivalence margin. The registry labels the sponsor’s method as an equivalence analysis and reports a 90% confidence interval and p = 0.02. The margin, the precise null and alternative hypotheses, and the testing procedure are not reported in the registry record.

Consequently, p = 0.02 should be understood in the context of the reported equivalence analysis, not automatically as evidence of a conventional difference between treatments. A p-value is calculated relative to a specified statistical hypothesis and analysis. Without the equivalence margin and full specification, the reader cannot verify how the reported test relates to the interval or independently reproduce the conclusion. The registry’s classification is informative, but the missing details limit assessment of the equivalence claim.

Why are the two intervals not necessarily comparable?

The sponsor reports an interval from -8.2 to 8.5 at 90% confidence. The unadjusted recalculation reports an interval from -11.59 to 11.39, but the confidence level for that recalculated interval is not stated in the registry record. The analyses also differ in method: the sponsor reports a mixed model, while the recalculation uses posted summary statistics without adjustment. Differences in analysis approach and the paired data structure can affect estimates and uncertainty. The available information does not identify the precise cause of the numerical discrepancy.

A confidence interval describes a range of values compatible with the estimate under the method and assumptions used. It is not a guarantee that the true effect lies in the interval, nor does it describe the range of individual participants’ responses. For this study, the reported intervals concern a difference in mean electrical-stimulation tolerance, not individual outcomes and not the secondary outcome measures.

What does over-dispersion mean in general?

Over-dispersion is a general concern for outcomes whose variability is greater than a model assumes. It can make standard errors too small if the model does not accommodate the extra variability. This trial’s primary endpoint is continuous and the record reports standard deviations, but it does not identify over-dispersion as an issue or describe a specific adjustment for it. That concept should not be mistaken for a documented feature of this analysis.

What is not documented?

The registry record does not report the original sample-size justification, the equivalence margin, full mixed-model specification, a confidence level for the unadjusted recalculated interval, or a complete account of missing observations and analysis populations. It lists three outcome measures, with one analysis listed, and two secondary outcomes posted. Those counts do not establish how multiplicity was handled or whether every planned analysis is represented. Any claims about a prespecified statistical plan, interim analyses, or particular missing-data procedures would go beyond what the registry record reports.

10. Confidence Intervals and Precision

The sponsor’s interval for the net mean difference runs from -8.2 to 8.5 and is reported at 90% confidence. It contains zero, as does the unadjusted recalculated interval, which runs from -11.59 to 11.39. An interval containing zero is compatible with no average difference under the method used, but it can also include nonzero differences. The recalculated interval extends in both directions, so the point estimate near zero should not be mistaken for a highly precise estimate.

The level of confidence for the recalculated interval is not reported in the registry record. It should therefore not be described as a 90% or other specified confidence interval. The sponsor’s interval and the recalculated interval also come from different analyses, so direct comparison of their widths is limited. The sponsor’s analysis is the result to prioritize because the discrepancy flag is true.

Precision is not the same as the size of the estimated difference. The means are close, but the treatment-specific standard deviations are 20.2 and 20.4, and the interval around the recalculated contrast is broad relative to its point estimate. In a split-body design, precision depends in part on the within-person association between the two measurements. That association is not reported, so the treatment means and separate standard deviations do not fully explain the uncertainty.

For an equivalence interpretation, precision must be considered in relation to the prespecified equivalence margin. That margin is not reported in the registry record. The reported 90% interval therefore cannot be judged against the study’s intended boundary for equivalence. The interval is informative about the range of estimates under the sponsor’s model, but the registry does not provide all the information needed to assess the equivalence decision independently.

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 based on the observed effect, not the original trial design assumptions. Because the endpoint is continuous, the figures are participants per arm, not total events. The 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 to the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned participants per arm under which a study would have an 80% probability of detecting the specified effect, if the planning assumptions and model held. The 90% power column gives the corresponding planning target for a 90% probability. These are design calculations for a hypothetical future study, not descriptions of what the completed trial achieved. This is not observed power.

The planning rows use the full observed effect, 75% of the observed effect, and 50% of the observed effect. The corresponding participants-per-arm figures are extremely large because the observed mean difference used for planning is very close to zero. As the target effect becomes smaller, it is harder to distinguish from random variation, so more participants are required to achieve the same planned power. The figures are illustrations, not recommended sample sizes: they inherit the assumptions and limitations of the calculation, and the registry does not report that the original trial was designed using this approach.

The split-body study structure also matters when interpreting the planning figures. The trial itself measured both treatments within participants, whereas the stated planning assumptions describe equal allocation between two arms. The displayed calculations should be read according to their stated assumptions rather than as a reanalysis of the trial’s paired design. They do not establish the number of participants that would be needed under a paired-design calculation.

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 = -0.100; pooled standard deviation σ = 20.300.
2. n = 2 × (1.96 + 0.842)² × 20.300² / -0.100² = 646,904.7, rounded up to 646,905 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 <- -0.100000000000001                      # observed difference in means
sigma <- 20.3002463039245                     # 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(1898689)
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 = 646,905 (80% power), 866,022 (90% power)
 75% of observed effect: n per arm = 1,150,053 (80% power), 1,539,595 (90% power)
 50% of observed effect: n per arm = 2,587,619 (80% power), 3,464,088 (90% power)
power.t.test: 646905.6 
Simulated power at n = 646,905 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.

13. Analyses Reported by the Sponsor

The sponsor’s reported result is a mixed-model equivalence analysis: net mean difference 0.2, 90% confidence interval -8.2 to 8.5, and p = 0.02. The separate unadjusted recalculation from posted treatment summaries gives a mean difference of -0.1, interval -11.59 to 11.39, and p = 0.986. These are not matching estimates or tests.

The discrepancy is explicitly flagged, so the sponsor’s own analysis takes precedence. The recalculation is an unadjusted check based on summary statistics; it does not reproduce the reported mixed model. The split-body design means that the relationship between each participant’s two measurements is relevant, while the posted treatment means and standard deviations do not provide the paired differences. The registry record does not give enough detail to identify the exact reason for the difference.

The sponsor’s p-value is associated with an analysis labeled as equivalence. It should not be interpreted automatically as a conventional test of a nonzero treatment difference. The equivalence margin and model details are not reported in the registry record, limiting independent verification. Readers should keep the sponsor result, the recalculation, and their different analytical roles distinct rather than combining their estimates or treating them as corroborating tests.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists three outcome measures and identifies maximum tolerance to transcutaneous electrical stimulation at Hour 6 as the primary outcome. It also lists two secondary outcomes: maximum tolerance to transcutaneous electrical stimulation and percent of maximum voluntary isometric contraction baseline for the quadriceps femoris. The record lists one analysis. The presence of multiple outcome measures raises a general multiplicity question: when several outcomes or comparisons are tested, the chance of at least one apparently notable result can increase. The registry record does not report a multiplicity adjustment or explain how the analyses were prioritized beyond identifying the primary outcome.

The posted results described in this analysis concern the primary continuous endpoint. The record does not provide results for the two secondary outcomes in the registry record for this account. Their status or numerical findings should not be inferred. Nor does the count of listed analyses establish that all analyses conducted by investigators were reported.

The population description states that each participant received both treatments and that 24 participants were analyzed for each treatment. This identifies the treatment-specific analysis counts, but the registry record does not give a fuller account of analysis populations, exclusions, protocol deviations, or missing endpoint measurements. It also does not state whether the primary analysis used all randomized participants, all participants with a measurement, or another defined population.

Missing-data handling is not reported in the registry record. There is no basis to claim that outcomes were complete, that a particular imputation method was used, or that a sensitivity analysis assessed missingness. The mixed-model method is named, but that alone does not establish the model’s missing-data assumptions or how incomplete paired observations were handled.

The original statistical plan, including any prespecified multiplicity strategy, analysis population definitions, and interim analyses, is not reported in the registry record. These omissions limit assessment of whether the reported result reflects the intended analysis plan. They also mean that no stronger statement about prespecification or completeness of reporting can be made from this record alone.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

The adverse-event record lists zero serious adverse events for ropivacaine 0.1% and zero for ropivacaine 0.4%. It also lists zero participants affected by other adverse events for each treatment, and zero deaths. The record gives 24 participants at risk under each treatment. Because this was a split-body study, the same participants received both treatments; the treatment-specific entries are not separate independent participant groups.

These figures describe what was recorded in the registry for the study. They do not establish that no adverse events of any kind occurred outside the categories or reporting captured in the record. The listed serious-event terms are empty, and the record does not provide further event narratives or a detailed safety analysis.

The study involved relatively healthy volunteers and a 6-hour infusion described in the arm information. The adverse-event figures should be interpreted within that study context, not generalized to other populations, procedures, or durations. They are descriptive registry counts and should not be read as a comparative estimate of safety or as evidence about uncommon events.

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

The posted primary-outcome summaries show similar treatment means at Hour 6: 27.0 mA for ropivacaine 0.1% and 26.9 mA for ropivacaine 0.4%. The sponsor reports a mixed-model equivalence analysis with a net mean difference of 0.2 and a 90% confidence interval from -8.2 to 8.5. The sponsor analysis takes precedence over the unadjusted recalculation, which gives a different estimate and interval.

The registry labels the sponsor’s result as an equivalence analysis, but the equivalence margin and full statistical specification are not reported. That limits an independent assessment of whether the interval met the trial’s intended equivalence criterion. The recalculated interval includes zero and is broad, but it is not a substitute for the sponsor’s paired mixed-model analysis. The values should be presented with their respective methods rather than treated as one unified result.

The result concerns maximum tolerance to transcutaneous electrical stimulation in the sciatic nerve distribution, not all aspects of sensory block, pain relief, muscle function, falls, or infusion duration. The brief summary discusses potential motivations involving pain control, muscle weakness, fall risk, and pump duration; those motivations are not themselves findings from the primary outcome. No claim about those outcomes follows from the electrical-stimulation endpoint alone.

The study was conducted in relatively healthy volunteers, and the recorded arm descriptions specify a 6-hour infusion. Its applicability to people undergoing surgery, longer use, or other clinical circumstances cannot be established from this endpoint and population alone. In addition, the concentration-rate assignments in the arm descriptions conflict with the brief summary, and the record does not resolve that issue. These limitations call for a narrow reading: the registry reports a comparison of the two concentrations on the stated endpoint, with an equivalence analysis whose margin and detailed model are not available in the record.

17. Why This Trial Matters Statistically

This trial raises a useful statistical issue: the design is split-body, so each participant contributes an observation under both treatments. That pairing can be valuable because the comparison can account for differences between participants, but it also means that treatment observations cannot be treated as independent groups. To understand precision, the within-person relationship matters. The registry provides treatment means and standard deviations but not the paired differences or their variability.

The record also illustrates why the method and estimand matter. The sponsor reports a mixed-model equivalence analysis, while an unadjusted calculation from the posted summaries gives a different estimate and p-value. Those figures answer questions using different information and methods. A small point estimate does not by itself demonstrate equivalence; the equivalence margin and analysis specification are needed to interpret that claim.

The design’s stated motivation distinguishes concentration from total dose: the brief summary describes different concentrations and infusion rates intended to deliver an equivalent basal dose. That is a statistically specific comparison, but the detailed arm descriptions conflict about which rate accompanied each concentration. Clear treatment definitions are essential for connecting an estimated contrast to the intervention being compared.

Finally, the endpoint is a measured sensory response at Hour 6, in relatively healthy volunteers. It is not a universal summary of clinical benefit or safety. The case demonstrates the importance of aligning conclusions with the measured outcome, the design, the analysis, and the completeness of the registry record.

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 contains an internal inconsistency in treatment descriptions. The brief summary frames the comparison as ropivacaine 0.1% at 8 mL/hour versus 0.4% at 2 mL/hour, with an equivalent total basal dose of 8 mg/hour. One arm description matches those concentration-rate assignments, while another lists 0.4% at 8 mL/h and 0.1% at 2 mL/h. Although both arm descriptions specify bilateral catheters and a 6-hour infusion, the record does not clarify which assignment is correct. This makes it harder to tie the numerical contrast to a clearly specified regimen.

The reported analysis and the unadjusted recalculation differ. The mixed-model equivalence analysis is the sponsor’s result and takes precedence, but the equivalence margin and model details are not reported. The summary statistics do not include the within-person difference data needed to reproduce a paired analysis. The registry record also does not state the confidence level for the recalculated interval or explain the source of the discrepancy.

The primary outcome is a surrogate sensory measurement at Hour 6, recorded from electrical stimulation in the sciatic nerve distribution. The record does not provide primary-outcome findings for pain control, duration of analgesia, muscle weakness, or fall risk. The study population is relatively healthy volunteers, which limits what can be inferred about other populations from this outcome.

The record does not report the original sample-size justification, the full statistical plan, missing-data procedures, analysis population definitions, or a multiplicity strategy. It lists two secondary outcomes, but numerical results for them are not included in the registry record for this account. These reporting gaps constrain assessment of precision, completeness, and the planned scope of inference.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Optimizing Local Anesthetic Concentration for Continuous Popliteal-Sciatic Nerve Blocks — NCT01898689.
• Registry record last updated 2021-03-19; status last verified 2021-03.
• Results first posted 2021-03-19.
• 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

NCT01898689, “Optimizing Local Anesthetic Concentration for Continuous Popliteal-Sciatic Nerve Blocks,” is recorded as a completed, randomized, quadruple-masked, parallel-design Phase 4 study sponsored by the University of California, San Diego. Enrollment was 24 relatively healthy volunteers. The registry lists study start at 2013-07 and primary completion at 2013-11.

The split-body design gave each participant both ropivacaine concentrations through bilateral sciatic perineural catheters. The primary outcome was maximum tolerance to transcutaneous electrical stimulation at Hour 6. The sponsor reported a mixed-model equivalence analysis; an unadjusted recalculation from posted summary statistics differs, and the sponsor analysis takes precedence. The equivalence margin, full model details, and original sample-size assumptions are not reported in the registry record. The detailed concentration-rate descriptions are inconsistent, and the record does not resolve that discrepancy.