Local Infiltration Analgesia With and Without EXPAREL Following Total Knee Arthroplasty: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Local Infiltration Analgesia With and Without EXPAREL Following Total Knee Arthroplasty (NCT02713490), a randomized phase 4 study. The primary outcome is Area Under The Curve (AUC) of Visual Analog Scale (VAS) Pain Intensity Scores From 12 to 48 Hours.

2. Clinical Question

The trial asked whether adding EXPAREL to local infiltration analgesia was associated with a different amount of pain after total knee arthroplasty than local infiltration analgesia without EXPAREL. The main comparison used the area under the curve (AUC) of visual analog scale (VAS) pain-intensity scores from 12 to 48 hours. The AUC combines the pain scores across that timeframe into a measure of total pain experienced; its unit is cm*hr.

The posted primary endpoint results describe least-squares means for both groups. The registry also reports an analysis comparing the groups. The statistical question concerns the estimated difference and its uncertainty; it does not, by itself, establish the clinical importance of any difference. The registry record does not report a threshold defining a clinically important difference.

3. Trial Design

This was a Phase 4, multicenter, randomized, double-blind, controlled trial with a parallel-group model. The registry lists triple masking. The study compared two local infiltration analgesia regimens following total knee arthroplasty: one including EXPAREL and one without EXPAREL. Both regimens included bupivacaine HCl and were expanded to a total volume of 120 mL with normal saline.

The registry lists enrollment as 140 and describes approximately 140 adult subjects undergoing primary unilateral total knee arthroplasty under spinal anesthesia with bupivacaine HCl 10-15 mg. The study status is completed. The listed start date is 2016-04-18 and the primary completion date is 2017-02-08. These registry entries describe the trial but do not establish how the analysis population relates to every enrolled participant.

For the primary endpoint, the efficacy population is defined as participants who received study drug and underwent surgery, with analysis based on randomized treatment. The posted primary endpoint group sizes are 69.0 in each treatment group. The adverse-event risk groups are reported separately, with 70 at risk for EXPAREL and 69 at risk for Bupivacaine. These are endpoint-specific figures; they should not be treated as interchangeable analysis populations.

The registry lists five outcome measures and five analyses. It names three secondary outcomes: percentage of opioid-free subjects at 48 hours, time to first opioid rescue in the first 48 hours, and overall benefit of analgesia score at 48 hours. Detailed results are posted for two of these outcomes; results for time to first opioid rescue are not reported in the registry record. The original protocol’s sample-size justification, planned interim analyses, and full statistical analysis plan 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.

Before assignment: A total of 167 patients were screened; there were 27 screen failures, including 2 patients who were randomized in error to the EXPAREL 266 mg + bupivacaine hydrochloride (HCl) group.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy population: all participants who received study drug and underwent the surgery, with analysis based on randomized treatment

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.

Population: Safety population included all participants who received study drug, with analysis by actual treatment received.

6. Primary Endpoint

The registry lists the primary outcome as Area Under The Curve (AUC) of Visual Analog Scale (VAS) Pain Intensity Scores From 12 to 48 Hours, measured over From 12-48 hours.

The primary endpoint was the area under the curve (AUC) of VAS pain-intensity scores from 12 to 48 hours. The VAS is described as a straight 10 cm line, with 0 cm representing no pain and 10 cm the worst pain possible. Participants were asked to indicate their current pain by marking the line. The endpoint’s timeframe is from 12-48 hours, and its unit is cm*hr.

Instead of focusing on a single pain rating, an AUC combines scores over the stated period into a measure representing total pain experienced from 12 to 48 hours. In general, this approach can capture both the level of a measured outcome and how it changes over a defined period. It is useful when the research question concerns cumulative experience across time rather than one measurement alone.

The registry reports least-squares means and standard errors for this continuous endpoint. A least-squares mean is a model-based estimate; the registry record does not give enough detail to specify all adjustments used in that model. The primary endpoint’s efficacy population included participants who received study drug and underwent the surgery, with analysis based on randomized treatment. No clinically important AUC threshold is reported in the registry record, so statistical evidence about a group difference should not be equated with evidence that its size is important to patients.

7. Results Posted in the Registry

• Bupivacaine: mean 208.41 versus 181.52 on control; difference 26.88 (95% CI -3.05 to 56.82), standardized effect d = 0.30; z-test p = 0.078.

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.

Percentage of Opioid-free Subjects at 48 Hours

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Bupivacaine: 0.0% (0/69) versus 10.0% (7/70) on control; risk difference -10.0 percentage points (95% CI -17.0 to -3.0); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Bupivacaine than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Benefit of Analgesia Score at 48 Hours

• 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:
  • Bupivacaine: mean 4.60 versus 4.10 on control; difference 0.50 (95% CI -0.90 to 1.90), standardized effect d = 0.12; z-test p = 0.484.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupivacaine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes offer a mixed set of signals rather than a single consistent extension of the primary result. They cover opioid-free status, time to first opioid rescue, and overall benefit of analgesia, and they use different outcome definitions and statistical methods. That makes them related clinical measures, but not interchangeable tests of the primary AUC question.

Detailed registry results are posted for opioid-free status at 48 hours and overall benefit of analgesia score at 48 hours. The detailed result for time to first opioid rescue in the first 48 hours is not reported in the registry record. The secondary findings should therefore be interpreted as incomplete with respect to the full set of named outcomes. They do not provide a complete account of every listed secondary question.

Secondary outcomes may help describe the broader pattern of observations and whether results across measures point in a similar direction. They do not automatically confirm or overturn the primary endpoint. In this trial, the posted secondary analyses use a Cochran-Mantel-Haenszel method for the binary opioid-free outcome and a Kruskal-Wallis method for the score. A simple summary-statistic recalculation for a secondary endpoint is not identical to those reported analyses.

The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting secondary tests. When multiple outcomes are tested, the chance of at least one small p-value can increase if each is considered independently. Unadjusted secondary p-values therefore carry less weight than a single, prespecified primary analysis and are best treated as exploratory signals. They should be interpreted alongside effect estimates, uncertainty, endpoint completeness, and the limitations of the reported analysis rather than as standalone proof of a general treatment effect.

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

• Percentage of Opioid-free Subjects at 48 Hours
• Time to First Opioid Rescue in the First 48 Hours
• Overall Benefit of Analgesia Score at 48 Hours

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is an AUC measured in cm*hr. The registry reports least-squares means and standard errors for the two groups, and an analysis of variance (ANOVA) result for their comparison. ANOVA is a general statistical method for comparing group means. A least-squares mean is an estimated mean from a statistical model; it can differ from a simple arithmetic mean when the model includes adjustments. The registry record does not report the complete model specification or identify all covariates, if any, used in the primary analysis.

What does the reported difference represent?

The registry’s primary analysis reports a least-squares mean difference of -26.884 for the groups listed in its analysis, together with a 95% confidence interval and p-value. A difference is directional: changing which group is subtracted from which reverses its sign. The group estimates and the sign of the reported contrast should therefore be read together. A simple recalculation from posted summaries instead expresses the comparison as Bupivacaine minus EXPAREL, yielding 26.88. That recalculation is unadjusted and is not a substitute for the sponsor’s model-based analysis.

The posted standard errors describe uncertainty in each estimated least-squares mean. They are not standard deviations of individual participants’ AUC values. Standard deviations describe spread among individual observations; standard errors describe the precision of an estimate. Confusing the two can make group variability appear much smaller than it is.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the data and the statistical method, under its assumptions. In general, a 95% confidence procedure would capture the true parameter in 95% of repeated studies conducted under the same conditions and assumptions. It is not a probability statement that this particular interval has a 95% chance of containing the true value. The interval also does not indicate whether values within it are clinically important; that requires a clinically meaningful threshold, which is not reported in the registry record.

The registry reports a 95% interval from -56.608 to 2.841 for the primary contrast and p = 0.038. The interval includes zero, while the reported p-value is below 0.05. For a conventional two-sided test and a confidence interval built from the same model, these summaries would ordinarily be consistent. The record does not explain the mismatch. It is more transparent to note it than to infer which reported quantity should be corrected.

What does the recalculation add?

The recalculated primary comparison uses posted group summaries to make a simple unadjusted comparison. The standard deviation used for this calculation is marked as approximate in the registry-derived analysis because the posted primary endpoint summaries are least-squares means with standard errors, rather than ordinary means and standard deviations. Such a reconstruction cannot reproduce every feature of a model-based ANOVA. It may not account for covariates, model structure, missing observations, or other analytical decisions. Those details are not reported in the registry record.

The unadjusted recalculation has a different estimate, confidence interval, and p-value from the sponsor’s reported analysis. That discrepancy means it should be used to understand how a basic comparison of posted summaries behaves, not to override the trial analysis. The sponsor’s own analysis takes precedence when describing the reported result.

Why can outcome types require different methods?

Continuous outcomes, such as AUC or a score, are often compared using methods focused on means or distributions. Binary outcomes, such as whether a participant was opioid-free at a stated time, concern counts or proportions and may use methods for categorical data. The registry reports a Cochran-Mantel-Haenszel analysis for the opioid-free outcome and a Kruskal-Wallis analysis for overall benefit of analgesia. These methods do not estimate precisely the same quantity as a simple comparison of means or proportions, so their reported statistics should be interpreted according to the method and outcome.

For repeated counts or rates, general statistical analyses may need to account for over-dispersion: variation greater than a simple model assumes. No such count-rate analysis is detailed among the posted primary results, and the record does not report an over-dispersion assessment. It would be inappropriate to assume that a particular model or diagnostic was used.

In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. It does not measure the probability that the null hypothesis is true, the probability that a result is due to chance, or the clinical importance of an effect. An unadjusted p-value also does not account for testing multiple outcomes. The registry does not report whether or how multiplicity was handled.

11. Confidence Intervals and Precision

Precision is conveyed chiefly by the confidence interval, not by the point estimate or p-value alone. The sponsor’s reported primary 95% confidence interval extends from -56.608 to 2.841 for its least-squares mean contrast. It includes zero, so the reported interval is compatible with values on either side of no difference under the stated analysis. Its width also indicates that the estimate is not tightly localized. The registry record does not report a threshold for a clinically important difference against which to judge the interval.

The sponsor’s primary p-value is 0.038, but the confidence interval includes zero. Under the usual pairing of a two-sided test and a 95% interval, this is an apparent inconsistency. The record does not explain it, so neither statistic should be silently altered or treated as if the other were absent. The simple unadjusted recalculation has a 95% confidence interval from -3.052 to 56.82 and p = 0.078; it is a different analysis and does not resolve the discrepancy in the reported analysis.

In general, a confidence interval reflects both the amount of information in the data and variability under the model. A narrower interval indicates greater precision for the parameter being estimated, while a wider interval leaves more uncertainty about its value. An interval is not a range containing every participant’s outcome, and it does not show the distribution of individual pain scores.

Precision is also conditional on analysis choices. The primary group values are least-squares means with standard errors, and the complete model specification is not reported in the registry record. The efficacy population is defined, but full details about missing observations and their handling are not reported. Those omissions limit independent assessment of the interval’s assumptions. Even a statistically notable estimate would not, without a clinical-importance threshold, establish that the magnitude matters to patients.

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 justification. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. For these continuous-outcome planning figures, the entries are participants per arm, not total participants or total events. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrated number of participants per arm for a design that would have an 80% chance of detecting the specified effect if that effect were real and the assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective design concepts: they describe hypothetical study planning, not the probability that the completed trial found a true effect.

The rows that plan for 100%, 75%, and 50% of the observed effect show how the assumed effect size changes the required sample. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm to reach the same target power. For example, the primary-outcome illustration lists 175 participants per arm for 80% power when planning for 100% of the observed effect, and 700 participants per arm when planning for 50% of that effect. These figures are illustrations under the listed assumptions, not recommendations or reconstructions of the original trial plan.

This is not observed power. Observed power, calculated after a trial from its estimated effect, is not a substitute for interpreting the confidence interval and the data. The planning figures depend on the observed effect, which is itself uncertain; if the true effect differs, the operating characteristics would differ as well. The corresponding sample-size curve should be read as a visual representation of how the planning requirement changes with the assumed effect, not as evidence about the outcome of the completed 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 = 26.884; pooled standard deviation σ = 89.712.
2. n = 2 × (1.96 + 0.842)² × 89.712² / 26.884² = 174.8, rounded up to 175 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 <- 26.884                      # observed difference in means
sigma <- 89.7116130944038                     # 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(2713490)
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 = 175 (80% power), 235 (90% power)
 75% of observed effect: n per arm = 311 (80% power), 417 (90% power)
 50% of observed effect: n per arm = 700 (80% power), 937 (90% power)
power.t.test: 175.8 
Simulated power at n = 175 per arm: 0.799 (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’s reported primary analysis is an ANOVA with a least-squares mean difference of -26.884, a 95% confidence interval from -56.608 to 2.841, and p = 0.038. The simple recalculation from posted summaries instead gives a mean difference of 26.88 for Bupivacaine compared with EXPAREL, a 95% confidence interval from -3.052 to 56.82, and an unadjusted p-value of 0.078. The contrasts use opposite group orders, and the analyses differ in their estimates and inferential results.

The recalculation is a basic, unadjusted reconstruction from summary statistics. It does not reproduce the sponsor’s ANOVA model, and the primary summaries are least-squares means with standard errors. The standard deviation used for the recalculation is approximate. The registry record does not provide enough model detail to identify the source of the discrepancy or recreate the sponsor analysis from first principles.

Because a discrepancy is flagged, the sponsor’s own analysis takes precedence when describing the trial’s reported primary result. That does not remove the apparent mismatch between its p-value and confidence interval: the record reports p = 0.038 while the 95% interval includes zero. Both should be presented as reported, with the inconsistency acknowledged. The recalculation can illustrate sensitivity to analytical approach, but it should not be portrayed as a correction to the sponsor’s result.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and multiple secondary outcomes, but the registry record does not report whether the analyses used a multiplicity adjustment, a testing hierarchy, or another procedure to control the overall chance of false-positive findings across outcomes. Without that information, the posted secondary p-values should be understood as unadjusted unless the registry explicitly states otherwise. A small unadjusted p-value from one of several outcomes is not equivalent to a result that has been protected against multiple testing.

The registry identifies an efficacy population for the primary outcome: participants who received study drug and underwent the surgery, analyzed according to randomized treatment. This definition is informative, but it is not the same as a full account of all analysis populations. The record does not report a complete accounting of exclusions, protocol deviations, or the handling of participants with missing endpoint measurements. Those details are important for assessing how closely the analyzed group reflects randomization and how missingness might affect the estimate.

The record also does not report the assumptions used for handling missing primary or secondary outcomes, whether any imputation was performed, or whether sensitivity analyses assessed alternative assumptions. Missing data can affect group comparisons when the probability of a missing measurement is related to the outcome or differs between groups. This is a general concern, not evidence that missingness occurred in a particular way in this trial.

Similarly, the original statistical analysis plan, the trial’s sample-size justification, and any interim analyses are not reported in the registry record. The posted planning illustrations are based on the observed effect and should not be confused with the original design plan. Together, these reporting gaps limit independent assessment of prespecification, multiplicity control, and robustness to missing data. They do not prove that the trial lacked such procedures; they mean the registry record does not report them.

16. 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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: influenza (1.4%), incision site cellulitis (1.4%).

The adverse-event figures are presented for separate at-risk groups. For serious adverse events, the registry reports 1 affected participant among 70 at risk in the EXPAREL group and 1 among 69 at risk in the Bupivacaine group. It reports zero deaths in each group. The registry also identifies Influenza and Incision site cellulitis at 1.4% each among the top serious-event terms.

These counts are descriptive. They do not, by themselves, establish whether an event was caused by a treatment, and the registry record does not provide enough detail to assess event timing, severity beyond the serious-event classification, or attribution. A small number of events also leaves substantial uncertainty about comparative rates. No new risk difference or percentage is calculated from these figures.

The registry separately reports other adverse events in 45 participants at risk in the EXPAREL group and 39 at risk in the Bupivacaine group. These are not serious-event counts and should not be combined with the serious-event figures. The safety summaries are distinct from the efficacy population and endpoint analyses. They describe what was recorded in the registry, not a complete safety profile or a causal conclusion.

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

The primary endpoint measures cumulative pain intensity from 12 to 48 hours using the area under the curve of VAS scores. The posted group estimates are numerically lower for EXPAREL than for Bupivacaine. The registry’s reported ANOVA gives a p-value below 0.05, but its 95% confidence interval includes zero, an apparent inconsistency that the record does not explain. A simple unadjusted recalculation also differs from the reported analysis, and the sponsor’s own analysis takes precedence when describing the trial result.

These data do not establish the clinical importance of the estimated difference. The registry record does not report a threshold for a clinically meaningful change in AUC. Statistical significance, even when reported, does not by itself show that a difference is large enough to matter to patients. Conversely, an interval that includes zero does not show that the groups are identical; it reflects uncertainty across a range of possible values under the analysis.

The results also do not establish that one regimen is appropriate for a particular patient or that the findings apply to settings beyond the studied population and procedures. This is a Phase 4 multicenter randomized trial of adults undergoing primary unilateral total knee arthroplasty under spinal anesthesia, but the registry record does not provide all details needed to judge broader generalizability. No medical advice follows from these statistical summaries.

Secondary outcomes add context but are not a uniform confirmation of the primary result. The named time-to-first-opioid-rescue outcome has no detailed result reported in the registry record, and no multiplicity approach is reported. Safety counts are descriptive, with low serious-event counts and no basis for causal attribution. The most defensible reading is therefore bounded: the registry reports a primary analysis, a discordant unadjusted reconstruction, incomplete secondary results, and uncertainty about clinical importance and analytical details.

18. Why This Trial Matters Statistically

This trial illustrates why a registry result should be read as more than a p-value. The primary endpoint is a continuous measure of pain accumulated across a defined period, and the posted results include group estimates, a model-based contrast, a confidence interval, and a p-value. Reading these together exposes an important feature of the record: the reported p-value and confidence interval do not align under the usual interpretation of a two-sided test and 95% interval.

It also demonstrates the limits of recalculating a result from summary statistics. A simple unadjusted comparison can be useful as a check, but it cannot necessarily reproduce a model-based analysis, especially when the registry reports least-squares means and standard errors rather than ordinary means and standard deviations. Here, the recalculation differs from the sponsor analysis, so the sponsor’s result takes precedence while the discrepancy remains visible.

The trial is also a useful example of the distinction between statistical and clinical importance. The reported estimate and interval address uncertainty about a statistical contrast; the registry does not provide a clinically important threshold. Secondary measures cover related but distinct aspects of analgesia, and the missing detailed result for one named secondary outcome, together with unreported multiplicity handling, limits how strongly those results can be combined into a single conclusion.

Finally, sample-size illustrations derived from observed effects are planning aids, not evidence of the completed trial’s power. Separating design assumptions, reported analyses, descriptive safety counts, and recalculations helps avoid treating distinct statistical quantities as if they answered the same question.

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 finding has an apparent inconsistency between the sponsor-reported p-value and confidence interval. The registry record does not explain why the reported p-value is 0.038 while the 95% interval extends across zero. This prevents a straightforward interpretation of the two summaries as a conventional matched test and interval.

A simple unadjusted recalculation also differs from the sponsor’s own analysis. The primary endpoint summaries are least-squares means with standard errors, and the standard deviation used in the recalculation is approximate. The registry record does not report the full ANOVA model, its covariates, or other details that would allow an independent reproduction. The sponsor’s own analysis therefore takes precedence, but the discrepancy remains relevant to interpretation.

The registry describes an efficacy population, but does not report full details of missing-data handling, participant exclusions, protocol deviations, or sensitivity analyses. It also does not report the original sample-size justification, any interim analyses, or the statistical analysis plan. Multiplicity handling for the set of outcomes is not reported. These gaps limit assessment of how prespecified and robust the reported inferences were.

Detailed results are not reported for the named time-to-first-opioid-rescue secondary outcome. The remaining secondary outcomes use different methods and should not be treated as direct replications of the primary endpoint. The record also does not report a clinically important threshold for the AUC or provide the information needed to evaluate broader applicability beyond the described population and trial setting.

Finally, the safety figures are descriptive and do not establish causal attribution. The registry reports relatively few serious events, so the counts alone cannot characterize uncommon risks precisely. These are limits of what the registry record reports, not proof that additional information or analyses do not exist elsewhere.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Local Infiltration Analgesia With and Without EXPAREL Following Total Knee Arthroplasty — NCT02713490.
• Registry record last updated 2020-12-11; status last verified 2020-12.
• Results first posted 2020-12-11.
• 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

NCT02713490 is a completed Phase 4, multicenter, randomized, double-blind, controlled, parallel-group trial comparing local infiltration analgesia with EXPAREL against local infiltration analgesia without EXPAREL following total knee arthroplasty. The primary endpoint was AUC of VAS pain-intensity scores from 12 to 48 hours in an efficacy population defined by receipt of study drug and surgery, analyzed according to randomized treatment.

The sponsor-reported primary ANOVA gives a least-squares mean difference of -26.884, a 95% confidence interval from -56.608 to 2.841, and p = 0.038. The confidence interval and p-value appear inconsistent under the usual paired interpretation. An unadjusted recalculation differs, so the sponsor’s own analysis takes precedence. The record does not report a clinically important threshold, complete analysis-plan details, multiplicity handling, or the detailed result for time to first opioid rescue. Safety counts are descriptive and do not establish causation.