Efficacy of Exparel (TM) on Post-operative Pain After Laparoscopic Gastric Bypass Using Circular EEA Stapler: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Exparel (TM) on Post-operative Pain After Laparoscopic Gastric Bypass Using Circular EEA Stapler (NCT03187379), a randomized phase 4 study. The primary outcome is Post-Operative Pain.

2. Clinical Question

3. Trial Design

The registry describes NCT03187379 as a Phase 4, randomized, single-masked, parallel-group study. It is listed as completed. The study start date is 2017-06-01 and the primary completion date is 2021-01-26. The sponsor is Matthew Kroh. The listed enrollment is 102.

Participants were assigned to Exparel, Liposomal Bupivacaine, or Control. The intervention arm description says that Exparel liposomal bupivacaine was injected concurrently with 0.25% bupivacaine at incisional sites before closing. The control arm received 0.25% bupivacaine alone. The brief summary describes 75 patients in each planned cohort, while the posted enrollment and outcome group counts differ from those cohort figures. The registry does not explain this difference.

The primary outcome is post-operative pain at 24 hours after surgery. It is recorded as a mean on a 0-100 Visual Analog Scale, with standard deviation describing variation among participants. The registry also posts pain scores at 48 hours as a secondary outcome. The brief summary says assessments were made using a nursing protocol and describes a research-team questionnaire at 24 and 48 hours, including the VAS and the Revised American Pain Society Post-Operative Questionnaire. Results for that questionnaire are not posted as outcome measures.

The registry does not report the randomization procedure, allocation concealment, the identity of the masked party, or detailed eligibility criteria. It also does not report the trial's original sample-size assumptions or a full statistical analysis plan. Those omissions limit how completely the design and conduct can be assessed from 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

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 Post-Operative Pain, measured over 24 hours post-surgery.

The primary endpoint is patient-reported pain at 24 hours after surgery, measured in units on a Visual Analog Scale. The scale runs from 0 to 100: 0 represents less pain and 100 represents more pain. The posted group summaries are means and standard deviations, so the principal comparison concerns average reported pain and the spread of individual scores within each group.

A patient-reported scale captures the experience of pain directly rather than relying only on a clinical observation or a treatment decision. A common numeric scale also makes it possible to describe group averages and compare the distributions of scores across randomized groups. The brief summary indicates that pain assessment was part of routine nursing evaluation and that a research-team questionnaire was administered at the stated assessment times.

Using a mean provides a concise summary, but it does not describe every participant's experience. The standard deviation helps convey how much scores varied within each group. Neither measure indicates whether scores were clustered at particular points on the scale, and the registry does not post the individual observations or additional distribution summaries. The registry identifies this as the primary outcome, but does not describe a threshold for a difference considered important to patients.

7. Results Posted in the Registry

• Exparel, Liposomal Bupivacaine: mean 49.40 versus 56.60 on control; difference -7.20 (95% CI -17.98 to 3.58), standardized effect d = -0.26; z-test p = 0.190.

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.

Post-Operative Pain

• 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:
  • Exparel, Liposomal Bupivacaine: mean 42.20 versus 51.50 on control; difference -9.30 (95% CI -21.22 to 2.62), standardized effect d = -0.30; z-test p = 0.126.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exparel, Liposomal Bupivacaine and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: mean VAS pain at 48 hours after surgery. Its group means follow the same direction as the primary outcome, with a lower mean in the Exparel, Liposomal Bupivacaine arm. As with the primary assessment, the posted interval includes zero. This gives a broadly similar descriptive pattern across assessment times, but does not independently resolve the uncertainty in the primary comparison.

The outcomes are related: both measure post-operative pain using the same scale, at different times after surgery. Scores at those times may reflect related experiences, so the secondary result should not be treated as an entirely separate replication. The registry does not report a formal analysis of change over time or a joint model of the repeated measurements.

Unadjusted secondary results carry less weight when several outcomes or assessment times may be examined, because the chance of finding a striking result can increase with repeated testing. In general, a prespecified multiplicity strategy can address that issue, but the strategy for this trial is not reported in the registry record. The registry also lists no reported formal analyses for the secondary outcome. The unadjusted result is therefore best read as supportive descriptive information, not as a confirmatory finding.

The brief summary mentions an additional questionnaire concerning pain and interference with daily activity, but the registry does not post results for that measure. The secondary result should not be generalized to other pain-related outcomes that are not reported.

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

• Post-Operative Pain

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are continuous measurements summarized by group means and standard deviations. For each assessment time, the comparison is expressed as the Exparel, Liposomal Bupivacaine mean minus the Control mean. This makes the sign interpretable: a negative mean difference indicates a lower mean VAS score in the intervention arm, while a positive value indicates a higher mean. This is a general explanation of a difference in means.

What does the mean summarize?

In general, the arithmetic mean combines all observed scores in a group into one measure of central tendency. It is useful when a continuous outcome can be meaningfully represented by an average, but it does not say that every participant had a score near that average. Here, the registry reports the mean and standard deviation for each arm at each posted assessment time. It does not provide individual scores, medians, or a description of the score distributions.

The standard deviation describes how spread out scores are around the group mean. A larger standard deviation indicates more variation among observed scores. In this trial, the reported standard deviations are large relative to the estimated mean differences. In general, that degree of within-group variation can make it harder to estimate a group contrast precisely, particularly when the number of observations is limited. The standard deviation is not the uncertainty around the mean; the standard error and confidence interval address uncertainty in the estimate.

How is the comparison expressed?

The comparison is an unadjusted difference in group means. The recalculated estimate uses the posted summary statistics, without adjustment for additional variables. The 24-hour estimate is -7.2 VAS points, and the 48-hour estimate is -9.3 VAS points. A mean difference is expressed in the same units as the measured outcome, so these estimates are in VAS points. It is not a percentage change or a ratio.

In general, an unadjusted comparison describes the observed contrast between groups without accounting for other characteristics that might be related to the outcome. Randomization is intended to make groups comparable on average, but it does not guarantee identical group characteristics in a particular study. The registry record does not report an adjusted analysis or identify covariates used in a model. The posted estimates therefore should not be described as adjusted effects.

What does the interval communicate?

In general, a confidence interval gives a range of values compatible with the observed estimate under the statistical method used. Its width reflects precision: narrower intervals indicate more precise estimation, while wider intervals leave more uncertainty about the size and direction of the contrast. The posted intervals at both time points include zero. Zero represents no difference in group means. Inclusion of zero means the posted interval does not rule out that value under its construction.

The registry gives the interval endpoints but does not report the confidence level or the procedure used to construct the intervals. Those details are not reported in the registry record. For that reason, the endpoints can be described as posted intervals, but a specific confidence level or an exact inferential procedure should not be attributed to them.

What does the p-value say?

In general, a p-value measures how incompatible the observed data, or data more extreme, are with a specified null model if that model and the test assumptions hold. It is not the probability that the null hypothesis is true, nor a direct measure of clinical importance. The posted unadjusted p-values are 0.19 at 24 hours and 0.126 at 48 hours. They should be interpreted alongside the effect estimates and intervals, rather than as stand-alone decisions.

The record does not specify the test used to produce the displayed p-values, whether they are two-sided, or any adjustment for multiple outcome comparisons. The planning illustration separately specifies a two-sided significance level of 0.05 for its sample-size calculations; this is not evidence that the trial's own analysis used that level. The original statistical plan and analysis choices are not reported in the registry record.

Why does variation matter?

In general, over-dispersion describes variation greater than a statistical model expects. The posted outcomes are continuous VAS measurements, and no over-dispersion parameter or model-based count analysis is reported. More broadly, a high spread in measurements relative to a mean contrast reduces precision because participants' scores vary widely around their group average. Here, the standard deviations provide a direct description of that spread; there is no basis in the registry record for claiming a particular distributional problem or a correction for it.

These methodological descriptions distinguish the reported summaries from statistical details that remain undocumented. The registry states the outcome scale, group means, standard deviations, comparison estimates, intervals, and unadjusted p-values. The precise analysis population, treatment of missing data, model specification, confidence level, and prespecified multiplicity strategy are not reported in the registry record.

11. Confidence Intervals and Precision

The 24-hour mean difference is -7.2 VAS points, with a posted interval from -17.98 to 3.575. The 48-hour mean difference is -9.3 points, with an interval from -21.22 to 2.616. Both intervals include zero, the value corresponding to no difference in average scores. Thus, the posted results do not pin down the direction of the mean difference with high precision.

Each interval also includes values on either side of zero. The negative endpoint is compatible with a lower average score in the Exparel, Liposomal Bupivacaine arm, while the positive endpoint permits a higher average score in that arm. This does not establish that all values in the interval are equally plausible, nor does it indicate that the full range has a particular clinical meaning. The registry does not report a threshold for a patient-important difference, so the clinical importance of particular points on the scale cannot be judged from the record alone.

In general, an interval is more informative than a point estimate alone because it conveys uncertainty about the estimate. Here, the intervals are broad in relation to the observed differences. The group standard deviations also indicate substantial variability in individual VAS scores. These features mean the estimated average contrasts are not highly precise.

The confidence level and construction method for the posted intervals are not reported in the registry record. The numerical endpoints should therefore be read as posted, without assigning an unreported confidence level. The interval interpretation does not replace consideration of study conduct, missing data, or the analysis plan, which are also incompletely documented in the registry.

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 illustration gives the number of participants per arm, not a total across both arms and not a total number of events. It is based on the observed effect and displays planning for 100%, 75%, and 50% of that effect. For the 24-hour outcome, the listed participants per arm for 80% power are 233, 414, and 930, respectively; the corresponding figures for 90% power are 312, 554, and 1,245. For the 48-hour outcome, the corresponding 80% figures are 172, 305, and 686, and the 90% figures are 230, 408, and 918.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The registry's original design assumptions and sample-size justification are not reported in the registry record, so these calculations should not be taken as the trial's own prospective target.

In plain terms, 80% power describes the planned chance of detecting the specified effect under the calculation's assumptions if that effect is present; the 90% column uses a higher target chance. The smaller-effect rows require more participants per arm because a smaller group difference is harder to distinguish from random variation. These figures are planning illustrations, not observed power.

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 = -7.200; pooled standard deviation σ = 27.705.
2. n = 2 × (1.96 + 0.842)² × 27.705² / -7.200² = 232.4, rounded up to 233 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 <- -7.2                      # observed difference in means
sigma <- 27.7045050488183                     # 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(3187379)
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 = 233 (80% power), 312 (90% power)
 75% of observed effect: n per arm = 414 (80% power), 554 (90% power)
 50% of observed effect: n per arm = 930 (80% power), 1,245 (90% power)
power.t.test: 233.4 
Simulated power at n = 233 per arm: 0.801 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry posts pain outcomes at 24 and 48 hours. These are related measurements of the same broad outcome, but they create more than one opportunity to examine a group contrast. In general, when multiple outcomes, time points, or analyses are tested, the probability of at least one apparently unusual result can increase. A prespecified multiplicity plan can define which result is primary and how secondary comparisons will be interpreted or adjusted.

The registry identifies the 24-hour pain score as primary and the 48-hour score as secondary. It does not report a multiplicity adjustment, a hierarchy for testing the secondary outcome, or a detailed plan for interpreting multiple comparisons. The unadjusted secondary p-value should therefore be considered descriptive rather than treated as a standalone confirmatory result. The original statistical analysis plan is not reported in the registry record.

The record posts group counts and outcome summaries, but does not report the number of missing outcome observations, reasons for missingness, or how missing values were handled. It also does not specify whether all randomized participants were analyzed in their assigned groups, whether an alternative analysis population was used, or how exclusions after randomization were handled. These details matter because results can depend on which participants contribute measurements and how incomplete data are addressed.

The registry does not report interim analyses, stopping rules, or the trial's original sample-size justification. It also does not provide details of allocation concealment or state who was masked. These items should not be inferred from the randomized and single-masked labels. Without this information, the record supports interpretation of the posted summaries but not a complete audit of the prespecified analysis and trial conduct.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abdominal pain (9.6%), vomiting (7.7%), nausea (6.0%), ileus (3.8%), pneumonia (2.0%).

The posted serious adverse event figures are 10 affected participants among 50 at risk in the Exparel, Liposomal Bupivacaine arm and 15 among 52 at risk in the Control arm. The registry reports no deaths in either arm. These are descriptive counts; the registry does not provide a statistical comparison of serious adverse events or establish whether individual events were caused by study medication.

For other adverse events, the posted figures are 14 among 50 at risk in the Exparel, Liposomal Bupivacaine arm and 27 among 52 at risk in the Control arm. The record lists Abdominal Pain at 9.6%, Vomiting at 7.7%, Nausea at 6.0%, Ileus at 3.8%, Pneumonia at 2.0%, and Small Bowel Obstruction at 2.0% among the top serious terms. Those percentages are listed in the registry without arm-specific attribution in the term list.

Adverse event counts depend on how events were defined, collected, and coded. The registry does not provide enough detail to assess those procedures or the timing and severity of each event. These figures describe the posted safety data and should not be interpreted as proof of a causal difference between groups.

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

The posted results show lower average VAS scores in the Exparel, Liposomal Bupivacaine arm than in the Control arm at both reported assessment times. The estimated mean differences are modest relative to the variability in scores, and both posted intervals include zero. The comparisons therefore leave uncertainty about the direction and size of the average difference.

A result that does not exclude zero is not proof that the groups are identical. It means that the posted interval includes no difference, while also including other possible values. Likewise, an estimated difference in one direction does not establish that the intervention caused that contrast. Randomization strengthens the basis for comparison, but interpretation still depends on how the trial was conducted, how outcomes were measured, and how missing observations and analyses were handled.

The registry record does not identify a threshold for a clinically important difference on the VAS. It therefore does not allow a conclusion about whether a particular difference would matter to patients. Nor can group means describe each participant's pain or determine whether the result applies to populations, procedures, or care settings beyond those represented in the study.

The 48-hour result has a direction consistent with the 24-hour result, but its unadjusted status and the absence of a reported multiplicity plan limit how strongly it can support the primary comparison. The posted record also lacks results for the questionnaire described in the brief summary.

Overall, these data support a cautious description of the observed averages and their uncertainty. They do not establish a definitive causal, clinical, or safety conclusion. Interpretation should remain tied to the outcomes, times, and analyses actually reported in the registry.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between the direction of a point estimate and the precision of that estimate. The group means are lower in the Exparel, Liposomal Bupivacaine arm at both assessment times, but the intervals extend across zero. A reader who focuses only on the direction of the means could overstate what the results establish; a reader who focuses only on whether an interval includes zero could overlook the range of differences still compatible with the data.

The posted standard deviations also make the role of variation visible. Pain scores differ considerably among participants, and that spread contributes to uncertainty around a group-average comparison. Reporting means without measures of spread would make it harder to judge how heterogeneous the observed scores were.

The study also provides a useful example of how a randomized design label does not replace reporting the analysis plan. Randomization is important, but a full interpretation also depends on information about who was analyzed, missing observations, masking, and how repeated outcomes were handled. Several of those details are not reported in the registry record.

Finally, the planning illustration shows how sample-size requirements depend on the target effect and desired power. A smaller target difference requires more participants per arm under the stated planning assumptions. Those calculations are distinct from evidence about the actual trial's design or its observed ability to detect an effect.

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 leaves several trial-specific uncertainties. The brief summary describes 75 patients in each cohort, while the posted enrollment is 102 and the outcome groups contain 50 and 52 participants. The record does not explain the differences among these figures. It also does not say how many randomized participants contributed outcome data or whether any observations were missing.

Masking is labeled single, but the record does not identify who was masked. Details of the randomization process and allocation concealment are also not reported. This makes it difficult to assess from the registry alone how assignment was implemented or which people involved in care, outcome collection, or analysis knew the group assignments.

The registry provides means, standard deviations, intervals, and unadjusted p-values, but does not report the specific inferential procedure, the confidence level for the intervals, or a detailed analysis plan. It does not describe adjustment for baseline characteristics, handling of repeated measurements, or a multiplicity strategy. The trial's original sample-size justification and interim-analysis procedures are not reported in the registry record.

The primary endpoint description concerns pain at 24 hours, and the secondary outcome concerns pain at 48 hours. Although the brief summary mentions the Revised American Pain Society Post-Operative Questionnaire, the registry does not post results for that measure. The record also does not identify a threshold for a patient-important VAS difference. These gaps constrain assessment of the broader patient experience and clinical relevance of the observed score contrasts.

These are limitations of what can be established from the registry record; they do not show that a particular procedure was or was not followed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy of Exparel (TM) on Post-operative Pain After Laparoscopic Gastric Bypass Using Circular EEA Stapler — NCT03187379.
• Registry record last updated 2022-06-21; status last verified 2022-06.
• Results first posted 2022-06-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT03187379 is a completed Phase 4, randomized, single-masked, parallel-group study of Exparel liposomal bupivacaine alongside 0.25% bupivacaine versus 0.25% bupivacaine alone for pain after Roux-en-Y gastric bypass. The primary posted outcome is mean VAS pain at 24 hours after surgery; pain at 48 hours is posted as a secondary outcome.

The intervention arm had lower posted mean scores at both times, but the unadjusted intervals include zero. The registry does not report the original sample-size rationale, detailed analysis plan, missing-data handling, analysis population, or multiplicity strategy. The results are therefore best read as imprecise descriptive comparisons rather than definitive conclusions.