Local Anesthetic as Single Shot Versus Catheter in Patients Undergoing Video Assisted Thoracoscopic Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Local Anesthetic as Single Shot Versus Catheter in Patients Undergoing Video Assisted Thoracoscopic Surgery (NCT04559347), a randomized phase 2 study. The primary outcome is Numeric Rated Pain Scale at Rest 0-4 Hours Post-operative.

2. Clinical Question

3. Trial Design

The registry record describes a phase 2, randomized, parallel-group, open-label, single-center trial comparing two local-anesthetic approaches for erector spinae plane block in patients undergoing video-assisted thoracoscopic surgery. One group received a single shot of liposomal bupivacaine (EXPAREL®)/bupivacaine. The other received ropivacaine through a continuous catheter, with a 0.5% bolus followed by a 0.2% infusion. The record does not report masking; the trial is explicitly identified as having none.

Enrollment was 45. The record gives a start date of 2020-12-10 and a primary completion date of 2024-01-10. Its status is terminated. The reason for termination, timing of the decision, and whether termination affected the planned enrollment or analysis are not reported in the registry record. No explanation should be inferred from the status alone.

The primary outcome is numeric rated pain at rest during 0-4 hours after surgery. The posted primary outcome summaries include 17 analyzed participants in each arm. The record cautions that participant counts differ across outcome measures because of incomplete data collection. The total enrolled number therefore should not be treated as the analysis size for every endpoint. Further details of the analysis populations, including whether the primary analysis was intention-to-treat or per-protocol, are not reported in the registry record.

The official title calls the study a non-inferiority trial, but the record does not state the non-inferiority margin, how it was chosen, or the prespecified statistical criterion. A sample-size justification, original power target, allocation ratio in the protocol, and detailed statistical analysis plan are also not reported in the registry record. The posted planning illustrations are based on observed effects and are not evidence of the study's original design assumptions.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The number of participants analyzed differs across outcome measures due to incomplete data collection for some outcomes.

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: Due to per protocol analysis for the noninferiority study, the number analyzed differs from the number randomized. For the group Single Shot Liposomal Bupivacaine (EXPAREL®)/Bupivacaine: 23 subjects were randomized but only 19 subjects received the assignment and only 17 subjects met compliance with protocol to include in final analysis. For the Continuous Catheter Infusion Ropivacaine group: 22 subjects were randomized but only 19 met compliance with the protocol to include in final analysis.

6. Primary Endpoint

The registry lists the primary outcome as Numeric Rated Pain Scale at Rest 0-4 Hours Post-operative, measured over 0-4 hours post operative.

The primary endpoint is a patient-reported numeric pain rating at rest during 0-4 hours after surgery. The scale ranges from 0, defined as no pain, to 10, defined as the worst pain imaginable. The registry record reports the outcome as a mean and standard deviation for each arm. The single-shot arm had a mean score of 4.824 with a standard deviation of 2.531 among 17 participants. The continuous-catheter arm had a mean of 5.176 with a standard deviation of 2.744 among 17 participants.

As a general statistical concept, a numeric rating scale turns a subjective symptom into an ordered numeric measure that can be summarized across participants. A mean describes the average reported score, while the standard deviation describes the variability of scores around that mean. Pain at rest in the early postoperative period is the trial's chosen primary measure; why this particular time window and measure were selected is not reported in the registry record. The score should be read as a group summary, not as a description of every participant's experience.

The registry record's description gives the scale anchors but does not report a threshold for a clinically important difference. It also does not say whether the primary estimand concerned a particular contrast beyond the comparison of the two arms. Those details matter when interpreting whether a numerical difference is meaningful and how a non-inferiority conclusion would be reached.

7. Results Posted in the Registry

• Continuous Catheter Infusion Ropivacaine: mean 5.18 versus 4.82 on control; difference 0.35 (95% CI -1.42 to 2.13), standardized effect d = 0.13; z-test p = 0.697.

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 Consumption in Morphine Equivalent Dose 0-4 Hours Post-operative

• 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:
  • Continuous Catheter Infusion Ropivacaine: mean 37.89 versus 23.47 on control; difference 14.42 (95% CI 0.02 to 28.82), standardized effect d = 0.66; z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Continuous Catheter Infusion Ropivacaine than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Opioid Consumption in Morphine Equivalent Dose 4-8 Hours Post-operative

• 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:
  • Continuous Catheter Infusion Ropivacaine: mean 39.94 versus 29.00 on control; difference 10.94 (95% CI -5.94 to 27.82), standardized effect d = 0.43; z-test p = 0.204.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Continuous Catheter Infusion Ropivacaine and the control. The interval gives the range of effects that remain compatible with the data.

Opioid Consumption in Morphine Equivalent Dose 8-16 Hours Post-operative

• 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:
  • Continuous Catheter Infusion Ropivacaine: mean 52.53 versus 38.44 on control; difference 14.09 (95% CI -7.03 to 35.21), standardized effect d = 0.44; z-test p = 0.191.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Continuous Catheter Infusion Ropivacaine and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists secondary outcomes that include opioid consumption over postoperative time windows, total intraoperative opioid consumption, and acetaminophen consumption. It records 35 posted secondary outcomes, but the detailed summaries considered in the posted endpoint data cover opioid consumption during 0-4, 4-8, and 8-16 hours after surgery. For these intervals, the arm means were numerically higher in the catheter group. The estimates and intervals vary, and only the earliest interval's unadjusted interval narrowly remains above zero based on the posted summaries. Detailed numeric summaries for the other listed secondary measures are not reported in the registry record.

This overall direction differs from the primary pain result only in the sense that the primary contrast was small, while the posted opioid means are higher in the catheter arm across the listed early intervals. These outcomes measure different things: pain ratings describe a participant-reported symptom at rest, while opioid consumption records medication use in morphine equivalent dose. They are related aspects of postoperative care but are not interchangeable measures, and the registry record does not report an analysis linking an individual's pain score to opioid use.

These secondary findings should be treated as exploratory context rather than as a replacement for the primary endpoint. The record lists many outcomes, while the secondary comparisons shown are unadjusted and no analysis plan for multiplicity is reported. When many outcomes or time windows are examined, chance findings become more likely across the set. The record does not report a correction procedure, a prespecified hierarchy, or an approach to deciding which secondary outcomes were confirmatory.

The secondary results also have outcome-specific participant counts. For the opioid measures described, analyzed counts were 17 in the single-shot arm and 18 in the catheter arm, different from the primary endpoint's 17 participants per arm. The record attributes variation in analyzed counts to incomplete data collection, but does not state the reasons or handling. Taken together, the secondary summaries offer descriptive information about observed opioid use in this sample, but do not establish a consistent treatment effect across all secondary measures or settle the primary non-inferiority question.

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

• Opioid Consumption in Morphine Equivalent Dose 0-4 Hours Post-operative
• Opioid Consumption in Morphine Equivalent Dose 4-8 Hours Post-operative
• Opioid Consumption in Morphine Equivalent Dose 8-16 Hours Post-operative
• Opioid Consumption in Morphine Equivalent Dose 16-24 Hours Post-operative
• Opioid Consumption in Morphine Equivalent Dose 24-48 Hours Post-operative
• Opioid Consumption in Morphine Equivalent Dose 48-72 Hours Post-operative
• Total Intraoperative Opioid Consumption in Morphine Equivalent Dose
• Acetaminophen Consumption in Milligrams 0-4 Hours Post-operative

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant contributes a numeric pain rating, and the registry record summarizes those scores using a mean and standard deviation. The mean is the arithmetic average of the recorded values. The standard deviation describes how dispersed individual scores are around that average. These summaries are useful for comparing group averages, but they do not show the distribution of individual ratings or how many participants had especially low or high values.

The posted primary comparison is a mean difference, calculated as the continuous-catheter mean minus the single-shot mean. Its estimate is 0.352. The sign indicates the direction under that ordering: a positive value means the catheter-arm mean is higher. Since the scale defines 0 as no pain and 10 as the worst pain imaginable, a higher score corresponds to a higher reported pain rating. This direction statement concerns the scale and group means; it does not imply a causal or clinical conclusion beyond the trial comparison.

The confidence interval runs from -1.423 to 2.127. As a general statistical concept, a confidence interval gives a range of values compatible with the observed data under a specified method and its assumptions. It conveys uncertainty in the estimated mean difference, rather than the spread of individual pain scores. The interval crosses zero, the value corresponding to equal group means. It also spans values on both sides of zero, so the data do not pin down the direction of the difference with precision.

The reported p-value is unadjusted and equals 0.697. As a general concept, a p-value assesses how unusual data at least as discordant with a null model would be if that model and the statistical assumptions held. It is not an effect size and does not quantify clinical importance. The record does not report whether this p-value was generated by the trial sponsor's prespecified method; no reported analysis is listed. Accordingly, the displayed inferential comparison should be understood as an unadjusted calculation from the posted summary statistics, not as a substitute for a missing sponsor analysis.

General statistical explanation: a non-inferiority analysis asks whether the data rule out a loss larger than a prespecified acceptable margin. The margin is essential: without it, a reader cannot determine what size of difference the study was designed to exclude. The official title identifies this as non-inferiority, but the margin, its rationale, and the formal analysis criteria are not reported in the registry record. The posted confidence interval alone cannot supply those missing design choices.

General statistical explanation: random allocation is intended to make treatment groups comparable, on average, with respect to measured and unmeasured baseline factors. In a small trial, randomization does not ensure that the groups are closely balanced in every characteristic. The registry record identifies randomized allocation but does not provide baseline characteristics or details of the randomization procedure. Open-label status means masking was not used, according to the record. It does not establish whether participants, clinicians, or outcome assessors knew allocation at every stage; those operational details are not reported.

The analysis counts differ by endpoint. For the primary outcome, 17 participants were analyzed in each arm. The record explicitly notes that counts vary across outcomes because of incomplete data collection. General statistical explanation: missing outcome data can affect precision and may also introduce bias if the availability of a score is related to treatment or the unobserved score. The registry record does not describe the missingness pattern, reasons by arm, imputation, or sensitivity analyses. Therefore, the effect of incomplete collection on the primary comparison cannot be assessed from these summaries.

The registry record lists 47 outcome measures and reports no analyses in its analysis listing. This distinction matters: posted outcome summaries are not the same as a complete statistical analysis report. The analysis plan, covariate adjustments, assumptions checks, treatment of multiple endpoints, and analysis-population definitions are not reported in the registry record. In the absence of those details, interpretation should stay close to the posted descriptive statistics and simple unadjusted comparison, and should not imply that an unreported model or prespecified procedure was used.

Dispersion also matters for continuous outcomes. General statistical explanation: when participant measurements vary substantially within groups, the mean difference is estimated less precisely for a given group size. The posted standard deviations are 2.531 and 2.744 for the primary pain scores. They describe within-arm variation and help contextualize the uncertainty in the mean contrast. They should not be confused with the confidence interval, which concerns uncertainty about the between-arm mean difference.

Finally, statistical significance, clinical importance, and non-inferiority are distinct ideas. A p-value addresses compatibility with a null model; a confidence interval communicates uncertainty about the effect; clinical importance requires an interpretable threshold; and non-inferiority requires a margin and criterion. The registry record gives the score scale and primary summaries but does not report a clinically important difference threshold or the non-inferiority design details. No one of these concepts can replace the others.

11. Confidence Intervals and Precision

The primary mean difference is 0.352 points, with a confidence interval from -1.423 to 2.127. This interval is wide enough to include a negative contrast, zero, and a positive contrast. Under the comparison's direction convention, a negative value would mean a lower mean in the catheter arm, while a positive value means a higher mean in that arm. The interval therefore does not determine the direction of the group difference.

As a general statistical concept, confidence interval width reflects both the variability of the measurements and the amount of information available. Here, the primary summaries are based on 17 analyzed participants in each arm, and the standard deviations are 2.531 and 2.744. The interval communicates uncertainty in the mean difference; it is not a range containing a specified proportion of individual participants' pain ratings.

The registry record does not report a clinically important difference threshold. It also does not report the non-inferiority margin. Therefore, the interval cannot be judged against a stated clinical threshold or used to decide whether the study met a non-inferiority criterion. In particular, an interval that crosses zero is not itself proof of equivalence. The observed means are close, but the estimates remain compatible with a range of contrasts that includes values in both directions.

The unadjusted p-value of 0.697 gives a different summary of the comparison and does not make the estimate more precise. The confidence interval is the more direct guide to the range of mean differences supported by the posted data under the calculation's assumptions. The record does not report a sponsor analysis or additional uncertainty analyses, so precision beyond this unadjusted comparison is not established.

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 calculations are planning illustrations based on the observed effect, not a record of the trial's original design. The figures are participants per arm for 80% power and participants per arm for 90% power; they are not total event counts. The assumptions stated for these illustrations 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 80% power column describes a planning scenario in which a study with the indicated number of participants per arm would have 80% probability of detecting the specified effect under the calculation's assumptions. The 90% column uses a higher target probability for that same modeled effect, and therefore generally requires more participants per arm. These are prospective planning interpretations, not descriptions of what happened in the completed trial. The figures are not observed power.

The rows that use 100%, 75%, and 50% of the observed effect illustrate how changing the assumed target effect changes the planning estimate. Smaller effects require more participants to distinguish them from random variation under otherwise fixed assumptions. For the primary pain outcome, the posted planning illustration gives 883 participants per arm for 80% power and 1,182 participants per arm for 90% power when using 100% of the observed effect; the smaller-effect rows require still larger per-arm counts. These figures follow from the planning assumptions and observed estimate, not from a reported original trial calculation.

The curve should be read as a visual version of the same modeled relationship between a target effect and required sample size, rather than as independent evidence about treatment effects. The original sample-size justification, target effect, non-inferiority margin, and trial-specific power assumptions are not reported in the registry record. The illustrations therefore should not be used to infer what the investigators planned or whether the terminated trial achieved a planned target.

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 = 0.352; pooled standard deviation σ = 2.640.
2. n = 2 × (1.96 + 0.842)² × 2.640² / 0.352² = 882.8, rounded up to 883 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.352                      # observed difference in means
sigma <- 2.6396493138294                     # 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(4559347)
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 = 883 (80% power), 1,182 (90% power)
 75% of observed effect: n per arm = 1,570 (80% power), 2,101 (90% power)
 50% of observed effect: n per arm = 3,532 (80% power), 4,728 (90% power)
power.t.test: 883.7 
Simulated power at n = 883 per arm: 0.798 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists 47 outcome measures, including the primary pain rating and multiple secondary measures. It does not report a statistical analysis plan or describe how the primary endpoint was prioritized relative to the secondary endpoints. It also does not report a multiplicity strategy, such as a hierarchy, adjustment procedure, or explicit designation of which secondary comparisons were confirmatory. These omissions matter because evaluating many outcomes can increase the chance that at least one comparison appears notable through random variation.

The posted secondary comparisons are unadjusted. Their p-values should therefore be read as individual comparisons, not as conclusions corrected for the full family of outcomes. The record does not say whether analyses were planned for all listed outcomes or whether some were added or changed; no such history should be inferred. The registry record reports no analyses in its analysis listing, which leaves the sponsor's formal testing procedures and interpretation unavailable.

Missing data are also relevant. The record states that analyzed participant counts differ across outcome measures because of incomplete data collection. It does not report how many observations were missing for each measure beyond the posted analysis counts, why data were incomplete, whether missingness differed by arm, or how missing values were handled. The primary endpoint has 17 analyzed participants in each arm, while the enrollment total is 45. The registry record does not provide an analysis-population definition or a flow accounting for participants from enrollment to each outcome analysis.

For a non-inferiority trial, population choice and missing-data handling can be especially consequential because different analysis populations may yield different estimates. This is a general methodological consideration, not a claim about what occurred in this trial. The record does not state whether an intention-to-treat, per-protocol, or other primary analysis population was used, nor does it report sensitivity analyses addressing missing data or protocol deviations.

The open-label design and incomplete information on outcome collection also limit assessment of potential measurement or performance effects. The primary outcome is patient-reported, but details about instruction, assessment procedures, or masking of outcome assessment are not reported in the registry record. These limits do not show that bias occurred; they mean that its possibility and direction cannot be evaluated from the posted registry information.

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: pneumothorax (4.5%), hypoxia (4.5%), cardiac arrest (4.5%), subcutaneous emphysema (4.3%), intraoperative hemorrhage (4.3%).

The registry record lists serious adverse events for 2 of 23 participants at risk in the single-shot group and 1 of 22 participants at risk in the continuous-catheter group. Other adverse events are listed for 3 of 23 and 2 of 22 participants at risk, respectively. Deaths are listed as 2 in the single-shot group and 0 in the catheter group. These are counts alongside the recorded numbers at risk, and should not be confused with the primary endpoint analysis counts or total enrollment.

These figures are descriptive safety summaries. The registry record does not provide event-level timing, severity detail beyond the serious/non-serious grouping, exposure duration, or an assessment of whether events were related to an intervention. A count difference alone cannot establish that an intervention caused or prevented an event. The record also does not report a statistical comparison of adverse events. The listed serious event terms include pneumothorax, hypoxia, cardiac arrest, subcutaneous emphysema, and intraoperative hemorrhage; the record does not provide enough information to assign causality from those terms.

The safety data should be read in light of the limited group sizes and the differing denominators used for those summaries. They do not provide a precise estimate of comparative risk or establish a safety difference between strategies. No medical advice or treatment conclusion follows from these counts.

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

The posted results describe a randomized comparison of two local-anesthetic strategies in patients undergoing video-assisted thoracoscopic surgery. For the primary outcome, the average pain-at-rest scores during 0-4 hours after surgery were 4.824 with the single-shot strategy and 5.176 with the continuous catheter strategy. The estimated mean contrast was 0.352, catheter minus single shot. The confidence interval from -1.423 to 2.127 indicates uncertainty in the size and direction of the difference.

That result does not demonstrate that the strategies are equivalent. It also does not answer the formal non-inferiority question on its own, despite the official title's description, because the registry record does not report a non-inferiority margin or analysis criterion. A close pair of sample means is not enough to show that any difference is acceptably small. The uncertainty interval and the missing decision rule both matter.

The result also does not establish that either strategy is better or worse. The p-value is 0.697, and the available comparison is unadjusted. The record does not report the sponsor's formal analysis, a complete statistical plan, or sensitivity analyses. The means are group-level summaries and do not describe the distribution of individual participant experiences.

The trial enrolled 45 participants and was terminated. The reason for termination and whether the posted analysis represents the planned analysis are not reported in the registry record. The primary endpoint analysis includes 17 participants per arm, and outcome-specific counts vary because of incomplete data collection. These factors limit the information available for interpreting the estimate. The posted adverse-event counts are descriptive and do not establish causal differences in safety.

More generally, the registry record can support a careful description of the observed results, but it does not support an unqualified clinical conclusion. Important interpretive details—including the original sample-size justification, analysis populations, missing-data approach, multiplicity strategy, and non-inferiority margin—are not reported in the registry record. Conclusions should remain bounded by the posted summaries and their uncertainty, without extending them to unreported outcomes or populations.

17. Why This Trial Matters Statistically

This trial illustrates why the design label and the numerical result need to be read together. The official title identifies a non-inferiority comparison, but the margin and decision rule are not reported in the registry record. Those details define what degree of loss would be considered acceptable and what evidence would be needed to rule out a larger loss. Without them, a reader can describe the mean contrast and its interval but cannot reconstruct the intended non-inferiority decision.

The primary analysis also shows why confidence intervals are important. The point estimate is 0.352, but the interval from -1.423 to 2.127 spans both directions. The point estimate alone can sound more definite than the data warrant. The sample-size illustrations further emphasize that estimates from small groups can be imprecise and that smaller target effects require more participants under the stated planning assumptions.

Several design and reporting features are relevant to statistical interpretation: randomized allocation, open-label status, outcome-specific analysis counts, termination, and a large set of outcome measures. None of these registry entries alone invalidates the results. Together with missing information on analysis populations, missing-data handling, multiplicity, and the original sample-size rationale, however, they define limits on how strongly the posted results can answer the intended question.

The study is therefore a useful example of distinguishing descriptive evidence from a formal decision. A registry can report means, variability, intervals, and event counts, while still leaving key elements of a trial's inferential framework unavailable. Careful statistical reading keeps the observed summaries visible while avoiding claims that require information the registry record does not report.

18. Limitations

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

The primary outcome analysis includes 17 participants per arm, despite total enrollment of 45. The record states that analyzed counts vary because of incomplete data collection, but does not report the full participant flow, reasons for missing outcomes, or the method used to handle missing data. That limits assessment of how representative the analyzed participants are of those enrolled.

The trial status is terminated, but the reason, timing, and consequences for the planned enrollment or analysis are not reported in the registry record. The original sample-size justification and design assumptions are also not reported. The posted planning calculations are based on the observed effect and should not be mistaken for the protocol's target or for evidence that the trial was adequately sized for its intended question.

The official title describes a non-inferiority trial, but the non-inferiority margin and formal decision criteria are not reported in the registry record. Without those details, the primary contrast cannot be evaluated against the stated design objective. The record also does not report a sponsor analysis, statistical analysis plan, primary analysis population, multiplicity strategy, or sensitivity analyses.

The study is open label and single center according to its title and design details. Baseline characteristics, eligibility criteria, randomization procedures, and details about outcome assessment are not reported in the registry record. The primary outcome is subjective and patient-reported; the record does not state whether any outcome assessment procedures reduced the potential influence of knowing allocation.

Finally, the record lists many outcomes, while only a subset of secondary endpoint summaries is detailed in the posted information used for interpretation. The safety summaries are counts without reported causal assessments or statistical comparisons. These limitations do not prove that the results are biased or that an intervention caused an event; they restrict the strength and scope of conclusions that can be drawn from the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Local Anesthetic as Single Shot Versus Catheter in Patients Undergoing Video Assisted Thoracoscopic Surgery — NCT04559347.
• Registry record last updated 2025-06-12; status last verified 2025-05.
• Results first posted 2025-06-12.
• 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

NCT04559347 is a phase 2, randomized, parallel, open-label, single-center trial of local-anesthetic strategies for erector spinae plane block in patients undergoing video-assisted thoracoscopic surgery. It compared single-shot liposomal bupivacaine (EXPAREL®)/bupivacaine with continuous catheter ropivacaine, described as a 0.5% bolus followed by a 0.2% infusion. Enrollment was 45, and the record status is terminated.

The primary outcome was numeric pain at rest during 0-4 hours after surgery. The analyzed groups each included 17 participants. The means were 4.824 and 5.176, and the posted mean difference was 0.352 with a confidence interval from -1.423 to 2.127; the unadjusted p-value was 0.697. The official title calls the trial non-inferiority, but the margin and formal analysis criteria are not reported in the registry record.

Outcome-specific participant counts vary because of incomplete data collection. The record lists 47 outcome measures, but does not report a full statistical analysis plan, original sample-size justification, or reason for termination. The posted summaries support a description of this sample, while leaving important details needed for stronger conclusions unavailable.