Exparel vs. Bupivacaine Hydrochloride vs. Placebo for Hernia Repair: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Exparel vs. Bupivacaine Hydrochloride vs. Placebo for Hernia Repair (NCT03541941), a randomized phase 4 study. The primary outcome is Cumulative Opioid Requirements for 72 Hours After Surgery.

2. Clinical Question

The registry describes two intended aims: assessing additional opioid requirements and pain scores. Its stated hypothesis anticipated a 30% decrease in total opioid requirements during the first 72 hours after surgery for Exparel. That is a protocol-era hypothesis, not a result. The posted primary outcome data summarize observed means and standard deviations for the three arms. They do not establish that a particular block reduces pain or opioid use. Pain-score results and other secondary outcome details are not reported in the registry record in the registry record for interpretation.

3. Trial Design

This is a phase 4, randomized, triple-masked, parallel-group trial. The registry reports enrollment of 164 and a completed status. The recorded start date is 2018-07-03, and the primary completion date is 2019-12-19. The sponsor is The Cleveland Clinic. These registry entries describe the trial structure and timeline; they do not by themselves establish how masking was implemented or maintained.

Participants were allocated to one of three interventions: an Exparel-containing solution, bupivacaine hydrochloride, or normal saline placebo. The listed arm descriptions specify that the surgeon administered each solution through an intraoperative transversus abdominis plane block under direct visualization. The Exparel arm also included bupivacaine hydrochloride, so its comparison with the bupivacaine-only arm concerns the different formulations as described, not Exparel given alone. The placebo arm received saline through the block procedure.

The primary outcome is cumulative opioid requirements measured from the end of surgery until 72 hours after surgery. The registry reports a mean and standard deviation for each arm. The posted primary comparisons use placebo as the reference, with separate estimates for Exparel versus placebo and bupivacaine hydrochloride versus placebo. No direct Exparel-versus-bupivacaine comparison is reported in the registry record.

Secondary outcomes listed include opioid requirements over the hospital stay, pain scores at several postoperative time points, length of stay, 30-day pain scores, and 30-day patient-reported quality of life. The available secondary result details include hospital-stay opioid requirements and 30-day quality-of-life Z-scores. Results for the other listed secondary outcomes are not reported in the registry record. The protocol, eligibility criteria, allocation concealment details, and the trial's original sample-size assumptions 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

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 Cumulative Opioid Requirements for 72 Hours After Surgery, measured over Measured from end of surgery until 72 hours after the surgery.

The primary endpoint is cumulative opioid requirements during the 72 hours after surgery. The registry defines the measurement window as starting at the end of surgery and ending 72 hours later. Opioids administered intravenously, including through a patient-controlled analgesia device and as rescue medication, as well as opioids administered orally, were to be recorded. Different opioid doses were converted to oral morphine equivalent daily dose, and the cumulative amount was assessed on the third postoperative day.

This endpoint expresses opioid use on a common scale despite differences in opioid medications and routes of administration. In general, a standardized dose measure makes it easier to summarize total use across participants receiving different opioid preparations. It captures medication administered, not pain intensity itself, and should be interpreted alongside pain and other clinical outcomes when those are available.

The registry reports the primary outcome as a mean, with standard deviation as the measure of spread, in mg morphine equivalents/day. The Exparel arm mean was 325.0, with standard deviation 225.0; the bupivacaine hydrochloride arm mean was 350.0, with standard deviation 284.0; and the placebo arm mean was 310.0, with standard deviation 272.0. These summaries describe the observed groups. The registry record does not report an adjusted analysis, a detailed analysis population, or the handling of missing endpoint measurements.

7. Results Posted in the Registry

• Exparel: mean 325.00 versus 310.00 on control; difference 15.00 (95% CI -79.22 to 109.22), standardized effect d = 0.06; z-test p = 0.755.
• Bupivacaine Hcl 0.25% Inj: mean 350.00 versus 310.00 on control; difference 40.00 (95% CI -65.35 to 145.35), standardized effect d = 0.14; z-test p = 0.457.

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.

Opioid Requirements for Total Length of Hospital Stay

• 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: mean 50.50 versus 51.00 on control; difference -0.50 (95% CI -7.64 to 6.64), standardized effect d = -0.03; z-test p = 0.891.
  • Bupivacaine Hcl 0.25% Inj: mean 50.10 versus 51.00 on control; difference -0.90 (95% CI -8.42 to 6.62), standardized effect d = -0.05; z-test p = 0.815.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exparel and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupivacaine Hcl 0.25% Inj and the control. The interval gives the range of effects that remain compatible with the data.

30-day Patient-Reported Quality of Life

• 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: mean 46.90 versus 45.20 on control; difference 1.70 (95% CI -8.19 to 11.59), standardized effect d = 0.06; z-test p = 0.736.
  • Bupivacaine Hcl 0.25% Inj: mean 38.40 versus 45.20 on control; difference -6.80 (95% CI -15.86 to 2.26), standardized effect d = -0.28; z-test p = 0.141.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Exparel and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupivacaine Hcl 0.25% Inj and the control. The interval gives the range of effects that remain compatible with the data.

The available secondary results cover opioid requirements over the hospital stay and patient-reported quality of life at the 30-day follow-up. Their overall pattern does not provide a consistent direction of estimated differences relative to placebo: the opioid-use estimates are close to zero, while the quality-of-life estimates point in different directions for the two active arms. The reported intervals for these comparisons include zero. These results are secondary and do not overturn or resolve the uncertainty in the primary 72-hour opioid comparison.

The registry also lists postoperative pain scores at multiple time points, length of hospital stay, 30-day pain scores, and additional opioid requirements as secondary outcomes. Although the record indicates that eight secondary outcomes are posted, numerical results for the other listed measures are not reported in the registry record among the registry entries available for interpretation. The missing details limit assessment of whether the broader pattern aligns with the primary outcome.

Secondary endpoints can add context by examining other time windows or different aspects of recovery. Hospital-stay opioid requirements are not the same endpoint as opioid use through 72 hours, and a quality-of-life Z-score is not a measure of opioid consumption or pain intensity. Differences in measurement and timing mean that secondary results should be interpreted on their own terms rather than combined into a single conclusion.

The available secondary comparisons are unadjusted. When many outcomes or comparisons are examined, the chance of seeing an apparently unusual result by chance can increase. General statistical explanation: a prespecified multiplicity strategy can control that risk, but the registry record does not report whether one was planned or used. Accordingly, individual secondary p-values carry less weight than a result supported by a prespecified, fully reported analysis. The absence of detailed results for other secondary measures further limits interpretation.

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

• Opioid Requirements for Total Length of Hospital Stay
• Pain Scores at Postoperative Day 0
• Pain Scores at Postoperative Day 1
• Pain Scores at Postoperative Day 2
• Pain Scores at Postoperative Day 3
• Length of Hospital Stay
• 30-day Pain Scores
• 30-day Patient-Reported Quality of Life

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: opioid requirements are summarized as a numerical dose measure. The registry specifies a mean and standard deviation for each arm. A mean describes the center of the observed values, while a standard deviation describes how dispersed individual values are around that center. These summaries are useful for describing groups, but they do not show the full distribution or how each participant's result relates to the group result.

What does a mean difference describe?

The posted primary comparisons express the difference between each active arm mean and the placebo mean. For Exparel versus placebo, the estimate is 15.0; for bupivacaine hydrochloride versus placebo, it is 40.0. The direction follows the order of the arm means: positive estimates correspond to higher observed means in the named active arm than in placebo. A mean difference is an estimate, not a certainty about the underlying group difference. It is expressed in the endpoint's measurement scale and should be interpreted together with its confidence limits.

What do confidence limits add?

A confidence interval communicates uncertainty around an estimated effect. In general, a wider interval means the data allow a broader range of effect sizes than a narrower interval does. The reported primary limits are -79.22 to 109.2 for Exparel versus placebo and -65.35 to 145.4 for bupivacaine hydrochloride versus placebo. Both ranges include zero, the value representing no mean difference, and extend to values on either side. The confidence level and the exact interval method are not reported in the registry record, so they should not be inferred.

How should p-values be read?

The unadjusted p-values are 0.755 for Exparel versus placebo and 0.457 for bupivacaine hydrochloride versus placebo. In general, a p-value describes how compatible the observed data are with a specified null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, and it does not quantify the size or clinical importance of an effect. These values are unadjusted; the registry record does not report a multiplicity procedure or an inferential analysis plan. The p-values should therefore be considered alongside effect estimates, confidence limits, and the trial's reporting limitations rather than treated as stand-alone verdicts.

Why does outcome variability matter?

The primary standard deviations are 225.0 for Exparel, 284.0 for bupivacaine hydrochloride, and 272.0 for placebo. General statistical explanation: greater spread in individual outcomes makes it harder to distinguish a group-level difference from random variation, all else being equal. A standard deviation is not the uncertainty of the mean; it describes variability among observed participants. The reported comparison intervals provide a separate view of uncertainty in the estimated differences.

Opioid use is converted to oral morphine equivalents so different opioid medications and routes can contribute to a shared dose measure. This conversion provides a common scale, but the registry record does not report the conversion rules in detail. It also does not give a distributional summary beyond the mean and standard deviation, so skewness, unusually high values, and other distribution features cannot be assessed from these summaries alone.

The primary endpoint is described as cumulative requirements but reported in mg morphine equivalents/day. The registry explains that medication administered over the defined period would be recorded and converted to oral morphine equivalent daily dose. Readers should retain the posted unit when interpreting the estimates and avoid converting them to a different time basis. The exact analysis model, assumptions checks, treatment of any incomplete medication records, and use of covariates are not reported in the registry record.

The listed comparisons are against placebo. They do not provide a direct estimate for Exparel versus bupivacaine hydrochloride. Comparing whether one active-arm p-value is smaller than another would not establish that the active arms differ; a direct contrast would be needed. No such direct comparison is reported in the registry record. Likewise, the group summaries alone do not establish equivalence between any arms.

Randomization is intended, in general, to create groups that are comparable on average with respect to measured and unmeasured baseline factors. It does not guarantee that all observed group characteristics are balanced, particularly in a trial of this size. Baseline characteristics and the detailed randomization procedure are not reported in the registry record, so their balance cannot be evaluated from these registry entries. The reported trial design identifies randomized allocation, but does not supply enough detail to reconstruct the statistical analysis.

The calculations presented as planning illustrations use the observed effects and simple assumptions, not the trial's original design rationale. General statistical explanation: planning with an observed effect can be unstable because an estimate from one study is uncertain and may not represent the effect in a future study. The planning figures are not evidence that the completed trial had a particular power. The trial's own sample-size justification and original assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate an effect. For the primary endpoint, the Exparel-versus-placebo estimate is 15.0, with reported limits from -79.22 to 109.2. The bupivacaine-hydrochloride-versus-placebo estimate is 40.0, with limits from -65.35 to 145.4. Each interval includes zero and allows values on either side of zero. The estimates therefore leave uncertainty about both the direction and size of the group differences.

The interval width is relevant because a point estimate alone can make an uncertain comparison look more definitive than it is. The primary results are not precise enough to isolate a small range of plausible differences. The registry record does not state the confidence level or the method used to construct the intervals. Those details cannot be posted from the posted summaries.

Precision also depends on the variability of the outcome and the amount of information in each comparison. The arm standard deviations are 225.0, 284.0, and 272.0, while the arm sizes are 57, 55, and 52, respectively. These registry entries accompany the reported wide confidence limits, but they do not justify recalculating or replacing the posted intervals. The statistical model, missing data handling, and any adjustment used in the sponsor's analysis are not reported in the registry record.

An interval that includes zero is not proof that the true effect is exactly zero. Nor does it establish equivalence: that conclusion would require an appropriate design and prespecified bounds, which are not reported in the registry record. The most defensible reading is that the available estimates have substantial uncertainty, and the registry results do not narrowly determine whether either active intervention changes the primary outcome relative to placebo.

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 assumptions. For these continuous outcomes, the figures are participants per arm, not total participants and not total events. The registry's 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 trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm in a hypothetical design that would have an 80% chance of detecting the stated effect under those assumptions. The 90% power column gives the corresponding planning figure for a 90% chance. These are design concepts; power is not a measure of the probability that a treatment works or of the strength of evidence in the completed trial.

Rows describe planning for 100%, 75%, or 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the planning illustration requires more participants per arm as the target effect gets smaller. For example, the posted primary comparison for Exparel uses 4,309 participants per arm for 80% power when planning for 100% of the observed effect, and 17,236 participants per arm when planning for 50% of that effect. These are illustrations under the stated assumptions, not recommendations for a future study.

This is not observed power. It does not describe the probability that the completed trial detected its true effect. The calculations reuse an estimated effect from the posted results, which is itself uncertain. A different underlying effect, analysis method, allocation, or design assumption would produce different planning figures.

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 = 15.000; pooled standard deviation σ = 248.513.
2. n = 2 × (1.96 + 0.842)² × 248.513² / 15.000² = 4,308.8, rounded up to 4,309 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 <- 15                      # observed difference in means
sigma <- 248.513035818974                     # 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(3541941)
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 = 4,309 (80% power), 5,769 (90% power)
 75% of observed effect: n per arm = 7,661 (80% power), 10,255 (90% power)
 50% of observed effect: n per arm = 17,236 (80% power), 23,073 (90% power)
power.t.test: 4309.7 
Simulated power at n = 4,309 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 record lists a primary endpoint and multiple secondary outcomes, including repeated pain assessments and outcomes measured over different follow-up periods. The available comparisons are reported with unadjusted p-values. The registry record does not report whether the trial prespecified a hierarchy among outcomes, adjusted for multiple comparisons, or identified a limited set of confirmatory secondary analyses. Without that information, isolated secondary p-values should be treated cautiously. Testing many outcomes can increase the chance that at least one comparison appears notable through random variation.

The record gives mean and standard deviation summaries for the primary endpoint and selected secondary outcomes, but does not report the analysis population used for each result. It is not stated whether analyses followed an intention-to-treat principle, included only participants with measured outcomes, or used another population definition. The registry record also does not report the number of missing measurements, reasons for missingness, or how missing data were handled. These omissions matter because incomplete outcome data can affect estimates, especially if missingness differs between groups or is related to the outcome.

The detailed statistical analysis plan is not reported in the registry record. In particular, model specifications, covariate adjustments, assumptions checks, and any prespecified subgroup analyses are not available. The comparison summaries therefore cannot be treated as a full account of the planned analysis. The confidence level and interval construction method are also not reported.

The record reports randomized allocation and triple masking, but the methods used to generate the allocation sequence, conceal assignment, and maintain masking are not reported in the registry record. These details are relevant to evaluating possible sources of bias. The record also does not give baseline characteristics in the registry record for interpretation, so comparability of enrolled groups cannot be reviewed.

These are reporting gaps, not proof that procedures were absent. They constrain what can be concluded from registry summaries. Complete reporting of the analysis populations, missing-data approach, outcome hierarchy, and multiplicity plan would help readers distinguish exploratory patterns from confirmatory evidence.

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: respiratory failure (1.8%), pulmonary embolism (1.8%), cardiac arrest (1.8%).

The registry reports serious adverse events among 1 participant in the Exparel arm, 2 in the bupivacaine hydrochloride arm, and 0 in the placebo arm. The corresponding numbers at risk were 57, 55, and 52. The record reports 0 deaths in each arm. These are counts as reported; they do not by themselves establish whether an event was caused by an intervention.

Other adverse events were reported for 15 participants in the Exparel arm, 17 in the bupivacaine hydrochloride arm, and 7 in the placebo arm, with the same respective numbers at risk as reported for each arm. The record lists Respiratory Failure, Pulmonary Embolism, and Cardiac Arrest among the top serious adverse event terms, each reported as 1.8%. The registry entries do not specify how those terms map to individual arms, or whether an individual could contribute to more than one event term.

Adverse-event counts are descriptive. The registry record does not provide event-level timing, severity details beyond the serious-event classification, exposure-adjusted rates, or a causal assessment. Differences in counts should not be interpreted as proof of a safety difference or as evidence that an intervention caused or prevented an event. The data also do not establish that unlisted adverse events did not occur.

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

The posted primary results describe mean opioid requirements during the 72 hours after surgery in three randomized groups. The observed mean was 325.0 mg morphine equivalents/day for Exparel, 350.0 for bupivacaine hydrochloride, and 310.0 for placebo. Both active-versus-placebo comparison intervals include zero and span values on either side. These estimates do not precisely establish the direction or magnitude of a difference in the primary outcome.

That interpretation is narrower than saying the treatments are the same. A result with an interval that includes zero does not prove no effect, and it does not demonstrate equivalence. Equivalence or noninferiority would require a suitable design, prespecified margins, and an analysis directed at that question. Those elements are not reported in the registry record.

The registry's hypothesis anticipated a 30% decrease in total opioid requirements for Exparel during the first 72 hours. The posted Exparel mean is numerically higher than the placebo mean. However, the comparison is imprecise, and the available summary does not justify a definitive conclusion about the underlying effect. Nor does a difference in opioid use alone establish a difference in pain or overall recovery. The registry record describes pain scores as outcomes, but their results are not reported in the registry record for interpretation.

Randomization supports comparisons between assigned groups in general, but interpretation also depends on complete outcome reporting and appropriate analysis. The record does not report its original sample-size rationale, analysis population, missing-data handling, multiplicity strategy, or detailed model. Those gaps make it difficult to determine how closely the posted summary reflects the prespecified analysis.

The appropriate conclusion is descriptive and cautious: the registry records numerical differences in group means, but the reported intervals leave considerable uncertainty. The available information neither establishes a clinically important benefit nor rules one out. It also does not support a conclusion about individual responses, longer-term pain, or safety beyond the adverse-event summaries reported.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated effect and its precision should be considered together. The primary mean differences are 15.0 and 40.0, but the reported limits extend to values on both sides of zero. The point estimates alone would give an incomplete account; the intervals show that the registry results are compatible with a broad range of possible differences.

It also highlights the distinction between a trial hypothesis and a trial result. The registry describes an anticipated 30% decrease in opioid requirements with Exparel. A hypothesis states what investigators set out to examine; it is not evidence that the expected effect occurred. The posted group summaries must be interpreted on their own, with uncertainty kept visible.

The three-arm design offers both an active comparator and a saline placebo, which frames different questions about the intervention formulations. Since the Exparel solution also contains bupivacaine hydrochloride, the intervention is a combination as described in the registry. The posted comparisons are each against placebo; without a direct Exparel-versus-bupivacaine estimate, the results do not answer whether those active regimens differ from one another.

The example also shows why sample-size planning illustrations are distinct from a trial's original design. Figures based on observed effects depend on uncertain estimates and stated hypothetical assumptions. They do not establish the completed trial's observed power or explain the choices made when the trial was designed. The original sample-size rationale is not reported in the registry record.

Finally, safety counts, secondary outcomes, and the primary endpoint answer related but nonidentical questions. A careful statistical reading keeps the outcome definitions, follow-up windows, uncertainty, and reporting gaps in view rather than compressing them into a simple claim of effectiveness.

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 posted primary summaries provide group means and standard deviations, but the registry record does not report detailed baseline characteristics. It is therefore not possible to assess balance in prognostic features from the registry entries. Randomization is reported, but details of sequence generation and allocation concealment are not reported in the registry record.

The record does not specify the analysis population, missing outcome counts, or methods for handling missing data. It also does not report the statistical model, covariate adjustment, confidence level, or interval method. These omissions limit the ability to reproduce the analysis or assess whether the posted comparisons correspond to the trial's prespecified analysis.

The primary outcome is measured over 72 hours, while some secondary outcomes cover the hospital stay or follow-up around 30 days. Those time windows address different questions. Numerical results for several listed secondary endpoints, including pain scores and length of stay, are not reported in the registry record in the registry record for interpretation. The available evidence therefore cannot characterize the full set of outcomes named in the record.

The intervention arms are not simply three isolated medications: the Exparel solution contains both Exparel and bupivacaine hydrochloride, while the active comparator contains bupivacaine hydrochloride alone. The placebo is saline administered through the block procedure. This composition should be kept in mind when describing the comparison. The registry summaries do not report a direct comparison between the two active arms.

Finally, the registry does not report a multiplicity strategy, original sample-size justification, or detailed safety assessment methods. The available summaries support cautious descriptive interpretation, but do not resolve these design and analysis questions.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Exparel vs. Bupivacaine Hydrochloride vs. Placebo for Hernia Repair — NCT03541941.
• Registry record last updated 2021-10-12; status last verified 2021-09.
• Results first posted 2021-10-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed phase 4, randomized, triple-masked, parallel-group trial of an intraoperative transversus abdominis plane block during open retromuscular hernia repair. The three arms were an Exparel-containing solution, bupivacaine hydrochloride, and normal saline placebo. Enrollment was 164.

The primary outcome was cumulative opioid requirements from the end of surgery through 72 hours, converted to oral morphine equivalents and reported as a mean with standard deviation. The posted active-versus-placebo estimates have confidence limits that include zero and extend in both directions, leaving substantial uncertainty about the size and direction of differences.

The record also lists secondary pain, opioid-use, length-of-stay, and quality-of-life outcomes. Detailed results are available for selected secondary measures; several listed outcome results and important analysis details are not reported in the registry record. The estimates should therefore be read as posted summaries rather than a complete account of the trial's analysis.