Efficacy and Safety of a Collagen Bupivacaine Implant in Women Following Abdominal Hysterectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of a Collagen Bupivacaine Implant in Women Following Abdominal Hysterectomy (NCT00624910), a randomized phase 2 study. The primary outcome is Total Use of Opioid Rescue Analgesia.

2. Clinical Question

In statistical terms, the study compares average opioid rescue use across randomized groups during a prespecified postoperative interval. The outcome is continuous, so the comparison concerns the magnitude and uncertainty of mean differences, not just whether participants did or did not use rescue medication. The registry record identifies the trial as phase II, randomized, triple-masked, and parallel-group. It records enrollment of 54. Although it gives a primary outcome population and group-level summaries, it does not report the number of participants with complete primary-outcome data or details about missing observations. The reported group summaries therefore need to be interpreted as posted, without assuming how missing measurements were handled.

3. Trial Design

The registry record describes a randomized, triple-masked, parallel-group phase II study. It lists three treatment groups: bupivacaine sponges, collagen sponges, and standard care without an implant. In the bupivacaine group, three 5 × 5-cm sponges were placed at specified wound layers before closure. The collagen group received three collagen sponges in specified layers, while the standard-care group received no implant during surgery. The study status is completed, and recorded enrollment is 54.

Random allocation is intended to support comparable treatment groups on average, reducing the risk that systematic differences at baseline explain an observed outcome contrast. Masking is intended to limit influences from knowledge of treatment assignment on care, measurement, and assessment. The record identifies triple masking but does not explain which people were masked or how masking was maintained. The study used a parallel-group structure, so participants were assigned to a group and outcomes were compared across groups rather than within the same participant under multiple treatments.

The primary outcome was total use of opioid rescue analgesia over 0 to 24 hours postoperatively, expressed as mg morphine equivalents. Group-level means and standard deviations are posted for the Intent-to-Treat Population. The record also lists secondary outcomes that include opioid use over a longer postoperative interval, time to first opioid rescue use, and pain ratings at rest and after cough. It records eight outcome measures and seven posted secondary outcomes, but does not provide posted inferential analyses for those secondary outcomes.

The registry record does not report the original sample-size assumptions, a formal statistical analysis plan, interim analyses, or details of allocation concealment. It also does not report the confidence level used for the posted interval estimates. These omissions limit what can be said about the trial's planned precision and confirmatory analysis strategy. The planning illustrations associated with the posted results are separate from the original trial 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

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Population

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: Intent-to-Treat Population

6. Primary Endpoint

The registry lists the primary outcome as Total Use of Opioid Rescue Analgesia, measured over 0 to 24 hours postoperatively.

The primary endpoint is total opioid rescue analgesia used during the first 24 hours after surgery, measured in mg morphine equivalents. It is a continuous measure: the posted summaries describe an average amount used in each group, along with the standard deviation. The endpoint is defined so that a higher value represents greater rescue medication use and a worse outcome on this measure. It addresses the study's stated question about how much opioid rescue medication was needed during the early postoperative period.

This endpoint can capture differences in the amount of rescue medication used, including differences among participants who all receive some medication. That is distinct from measuring only whether rescue medication was used. Expressing use in morphine equivalents makes the outcome a common quantity across opioid rescue medicines, as described in the endpoint unit. The registry record does not report which medicines were permitted, the rules for administering rescue medication, or any additional details about conversion to morphine equivalents.

Mean use is useful for comparing average medication consumption between randomized groups, but a mean does not describe every participant's experience. The standard deviations show that individual observations vary around the group means; they do not provide the full distribution or explain why use differed between participants. The endpoint also cannot, by itself, establish whether pain was adequately controlled, because it is a measure of rescue medication use rather than a direct measure of pain. Pain intensity and other measures were listed among secondary outcomes, but the registry record does not post inferential analyses for them.

7. Results Posted in the Registry

• Bupivacaine Sponges: mean 53.65 versus 53.73 on control; difference -0.08 (95% CI -30.78 to 30.62), standardized effect d = -0.00; z-test p = 0.996.
• Collagen Sponges: mean 66.56 versus 53.73 on control; difference 12.83 (95% CI -24.23 to 49.89), standardized effect d = 0.27; z-test p = 0.497.

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.

Total Use of Opioid Rescue Analgesia

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Bupivacaine Sponges: mean 67.78 versus 66.03 on control; difference 1.75 (95% CI -21.84 to 25.34), standardized effect d = 0.05; z-test p = 0.884.
  • Collagen Sponges: mean 80.87 versus 66.03 on control; difference 14.84 (95% CI -17.33 to 47.01), standardized effect d = 0.34; z-test p = 0.366.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bupivacaine Sponges 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 Collagen Sponges and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the questions beyond opioid use during the first postoperative day. The registry record lists opioid rescue use over a longer interval, time to first rescue use, pain intensity at rest, and pain intensity after cough, measured with visual analog and Likert scales. The posted secondary summaries include opioid use through 48 hours, while the record does not post inferential analyses for the secondary outcomes as a whole.

At a broad descriptive level, the 48-hour opioid-use summaries follow a pattern resembling the primary outcome: the bupivacaine group mean is close to the standard-care mean, while the collagen group mean is higher. This offers a longer-window descriptive context for the primary comparison, but it is not an independent confirmation of the same result. The two measures are related in time and both reflect opioid use, so agreement in their general pattern should not be counted as separate, conclusive evidence.

The pain ratings and time-to-first-use outcomes could address different aspects of postoperative experience, but their results are not reported in the registry record. No direction or magnitude for those outcomes can be inferred from their inclusion in the outcome list. The registry record also does not report a combined analysis that integrates medication use and pain measures.

Unadjusted secondary results generally carry less weight than a prespecified primary analysis because evaluating multiple outcomes and comparisons creates more opportunities for apparently notable findings by chance. The record does not report a multiplicity adjustment or a hierarchy for secondary outcomes. The primary endpoint should therefore remain the main focus, while secondary outcomes are best treated as supportive or exploratory descriptions when numerical results are available. Missing inferential analyses and absent multiplicity details limit stronger claims about consistency across outcomes.

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

• Total Use of Opioid Rescue Analgesia
• Total Use of Opioid Rescue Analgesia
• Pain Intensity Rating on a Visual Analog Scale (at Rest)
• Time to First Use of Opioid Rescue Analgesia
• Pain Intensity Rating on a Visual Analog Scale (After Cough)
• Pain Intensity Rating on a 4-point Likert Scale (at Rest)
• Pain Intensity Rating on a 4-point Likert Scale (After Cough)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, so its posted group summaries are means and standard deviations. A mean describes the average observed amount of opioid rescue analgesia within a group. A standard deviation describes the spread of individual observations around that average. These quantities answer different questions: the mean locates the group's average, while the standard deviation reflects variation among participants. Neither alone shows the shape of the outcome distribution or whether a small number of observations strongly influenced the mean.

The principal contrasts are mean differences between each implant group and standard care without an implant. A mean difference is calculated by subtracting the comparator mean from the intervention-group mean. Its sign indicates the direction of the estimated contrast, given the group ordering used in the record. Because higher opioid use is defined as worse, a positive difference indicates a higher estimated mean in the implant group, while a negative difference indicates a lower estimated mean. The numerical estimate is only one part of the result; its uncertainty also matters.

The posted comparison estimates and intervals are recalculated, unadjusted comparisons based on the group summary statistics. They are not reported sponsor analyses. The registry record lists no reported analyses, and its interval confidence level is not reported in the registry record. A p-value from an unadjusted comparison assesses how incompatible the observed contrast is with a null comparison under the method's assumptions; it is not a measure of the probability that the null hypothesis is true. It also does not indicate whether an effect is clinically important.

Randomization is the design feature that supports comparisons between assigned groups by limiting systematic allocation differences. It does not guarantee that groups will be identical, particularly in a small trial. The parallel-group structure compares separate groups of participants. The record says the study was triple-masked, but it does not specify who was masked. Masking can reduce the chance that expectations influence treatment delivery or outcome assessment, but the record does not provide details that allow an assessment of how masking operated in practice.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model expects. When a model understates variability, standard errors may be too small and intervals too narrow, making apparent precision misleading. This is a general statistical concern, not a finding that over-dispersion occurred in this trial. The registry record provides standard deviations for the primary outcome but does not describe a distributional assessment or report a model-based adjustment for over-dispersion. A mean-and-standard-deviation summary also cannot show whether the outcome was skewed or had unusually influential observations.

What does an interval estimate contribute?

In general, an interval estimate presents a range of values compatible with the observed data under the method used. A narrow interval indicates more precision than a broad one, though interpretation also depends on the method and assumptions. The intervals for the primary contrasts span both negative and positive differences, so they do not isolate a single direction of mean difference. The registry record does not state the confidence level for these intervals; that omission prevents describing them as a specific confidence level.

What do the p-values contribute?

A p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the chance that the result happened by chance, nor is it evidence that two groups are equivalent when it is not small. In this trial, the p-values belong to unadjusted recalculations. The record does not state whether the original sponsor analysis used a different test, covariate adjustment, or other procedures, so no such method should be assumed. When multiple outcomes or contrasts are considered, unadjusted p-values also do not account for the overall opportunity to find an apparently unusual result.

What is not documented?

The registry record does not report the original sample-size justification, the trial's prespecified statistical analysis plan, interim analyses, handling of missing outcome data, or details of protocol deviations. The primary population is identified as Intent-to-Treat, but the record does not explain how that population was operationalized or whether all randomized participants contributed to the posted summaries. These gaps do not invalidate the posted descriptive statistics, but they limit reconstruction of the planned analysis and assessment of its robustness. The reported group summaries and recalculations should therefore be read as a statistical description of the posted results rather than as a substitute for an unreported full analysis.

11. Confidence Intervals and Precision

The estimated bupivacaine-versus-standard-care mean difference is -0.08 mg morphine equivalents, with an interval from -30.78 to 30.62. This range includes the possibility of lower mean use in the bupivacaine group and the possibility of higher mean use. Its breadth relative to the point estimate makes clear that the near-zero estimate is not a precise determination that the underlying means are the same.

The collagen-versus-standard-care mean difference is 12.83 mg morphine equivalents, with an interval from -24.23 to 49.89. This interval also extends across zero and includes a range of possible directions and magnitudes. The estimate therefore does not sharply distinguish between lower and higher mean use in the collagen group. The p-values, 0.996 and 0.497 respectively, are consistent with the fact that neither recalculated comparison provides a clear distinction from zero under its unadjusted test. They do not establish equivalence.

Intervals communicate precision more directly than a point estimate alone because they show how much uncertainty remains under the calculation method. A wide interval can arise when group sizes are limited, variability is substantial, or both. The primary group standard deviations are 32.78 for bupivacaine sponges, 47.53 for collagen sponges, and 47.71 for standard care without an implant. The registry record does not provide the confidence level or the original sponsor's interval method, so the recalculated intervals should be interpreted with that limitation in mind.

Precision is not the same as clinical importance. The record does not specify a threshold for a meaningful difference in opioid use. Consequently, the intervals cannot be classified as excluding or confirming a clinically important effect based on a threshold that is not reported. They show uncertainty around the mean differences, but they do not resolve the clinical meaning of all values within those ranges.

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 planning illustrations give the number of participants per arm for the continuous-outcome comparisons. They are not total-event counts. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The original trial's own sample-size assumptions are not reported in the registry record.

The 80% power column describes the estimated number of participants per arm needed, under those planning assumptions, for an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column uses a higher target chance of detection and therefore generally requires more participants. These are design-planning quantities, not probabilities that the posted trial result is correct. Smaller target effects require more participants because subtle differences are harder to distinguish from random variation.

The figures are especially sensitive to the observed effect used as their starting point. For the bupivacaine comparison, the observed mean difference is very close to zero, and the corresponding planning figures are extremely large. That does not mean the trial had such a target or that a particular number would guarantee a definitive result. It reflects the arithmetic consequences of using a very small observed difference as the effect to detect. The collagen comparison uses a larger observed difference and yields smaller planning figures, though those figures remain illustrations based on the same stated assumptions.

These calculations are not observed power. They do not tell whether the trial was adequately powered based on its original design, because the original design assumptions are not reported. They are best read as a sensitivity exercise: if the effect to detect were the specified fraction of the observed effect, the calculation indicates the approximate per-arm size under the stated model and planning choices.

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 = -0.080; pooled standard deviation σ = 37.407.
2. n = 2 × (1.96 + 0.842)² × 37.407² / -0.080² = 3,432,208.2, rounded up to 3,432,209 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 <- -0.0799999999999983                      # observed difference in means
sigma <- 37.4074381243494                     # 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(624910)
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 = 3,432,209 (80% power), 4,594,754 (90% power)
 75% of observed effect: n per arm = 6,101,704 (80% power), 8,168,450 (90% power)
 50% of observed effect: n per arm = 13,728,833 (80% power), 18,379,013 (90% power)
power.t.test: 3432209 
Simulated power at n = 3,432,209 per arm: 0.802 (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 trial has one listed primary endpoint and multiple secondary outcomes, with comparisons of each implant group against standard care. When many outcomes or contrasts are tested, the chance of at least one apparently unusual result can increase. A multiplicity strategy can address this issue by defining which comparisons are primary, adjusting error rates, or specifying an ordered testing plan. The registry record does not report a multiplicity procedure, an outcome hierarchy, or a statistical analysis plan that explains how multiple comparisons were handled.

The recalculated p-values are unadjusted. They do not account for testing more than one treatment contrast or examining several outcome measures. This does not change the numerical values of the posted recalculations, but it affects how they should be interpreted as evidence. In particular, the lack of reported adjustment means that the p-values should not be treated as if they arose from a single isolated test selected in advance.

Missing-data handling is also not reported in the registry record. The primary outcome identifies the Intent-to-Treat Population, but the record does not explain whether all randomized participants were included in each group summary, how unavailable measurements were treated, or whether any imputation was used. It does not report the extent or reasons for missing outcome observations. Without those details, it is not possible to assess whether missingness could have affected the group comparisons.

The record lists no reported analyses. Therefore, the posted inferential comparisons are recalculations from the summary statistics rather than sponsor-reported adjusted analyses. The record does not describe model covariates, assumptions checked, sensitivity analyses, or handling of protocol deviations. Nor does it state whether interim analyses were planned or conducted. These omissions leave uncertainty about the full analysis process and make it important to distinguish descriptive group summaries from a documented confirmatory statistical analysis.

The record's naming of an Intent-to-Treat Population indicates the stated population for the primary outcome, but does not itself establish how that population was implemented. The reported group sizes for the outcome summaries are 28 for bupivacaine sponges, 15 for collagen sponges, and 11 for standard care without an implant. Because further accounting of randomized participants and outcome availability is not reported, the contribution of missing data cannot be independently evaluated.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abdominal abscess (9.1%), intestinal obstruction (3.6%), seroma (3.6%).

The registry record reports serious adverse events for each group alongside the number at risk. Serious adverse events were reported for 2 of 28 participants at risk in the bupivacaine-sponges group, 0 of 15 in the collagen-sponges group, and 1 of 11 in the standard-care group. Deaths were reported as 0 in each group. These counts are descriptive; they do not establish that an intervention caused or prevented an event.

Other adverse events were reported for 21 of 28 participants at risk in the bupivacaine group, 12 of 15 in the collagen group, and 9 of 11 in the standard-care group. The record lists abdominal abscess at 9.1%, intestinal obstruction at 3.6%, and seroma at 3.6% among the top serious adverse event terms. These listed terms do not provide a complete account of severity, timing, relatedness, or participant-level overlap. The registry record does not report additional details needed to compare event patterns or attribute them to study treatment.

With small groups and no reported inferential safety analysis, differences in event counts should be interpreted cautiously. The figures describe what the record reports, rather than proving comparative safety.

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

The posted primary summaries show similar mean opioid rescue use for the bupivacaine-sponges and standard-care groups, while the collagen-sponges group had a higher mean than standard care. The recalculated mean differences have intervals that include values in both directions. The data therefore do not provide a precise estimate of the direction or magnitude of either contrast. A point estimate close to zero is not proof that the groups are equivalent, and an estimate above zero is not by itself proof of a real difference.

The endpoint is limited to total opioid rescue analgesia during the first 24 postoperative hours. It does not directly measure pain intensity, function, satisfaction, or longer-term recovery. Although the registry record lists several secondary outcomes, it does not report inferential analyses for them. As a result, the posted primary summaries should not be expanded into a general conclusion about all postoperative outcomes.

The record also includes safety counts, but event counts alone cannot establish causality or provide a full comparative safety assessment. The small group sizes and absence of detailed analysis reporting make safety patterns descriptive. The results do not establish that an implant caused an adverse event, or that the absence of a reported event in a group establishes absence of risk.

These limitations are important when reading a phase II study. The results describe observed group summaries and the uncertainty around recalculated comparisons; they do not settle the treatment question. The trial's original design assumptions, missing-data procedures, multiplicity approach, and sponsor inferential analyses are not reported in the registry record. The appropriate statistical conclusion is correspondingly bounded: the available summaries show no precise separation in average primary endpoint use, while leaving a broad range of possible differences compatible with the data.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its primary result combines a near-zero estimated contrast with broad uncertainty. Readers can see why the point estimate alone is insufficient: the interval extends in both directions and includes substantially different possible mean differences. Interpreting the estimate alongside its precision avoids treating a nonsignificant comparison as proof of no difference.

The three-arm design also highlights the importance of keeping contrasts distinct. Bupivacaine sponges and collagen sponges are each compared with standard care without an implant. The results do not represent a single comparison of all implant use against no implant. The comparator chosen matters to the question, and combining groups would change the estimand.

The registry record illustrates how group sizes and outcome variation shape precision. The standard-care group is smaller than either implant group, and the posted standard deviations show variability in opioid use. Together, limited group sizes and variable measurements contribute to uncertainty in mean comparisons. The planning illustrations further show how an extremely small observed contrast can translate into very large sample-size requirements when treated as the effect to detect. Those calculations are not the trial's original design plan and should not be mistaken for evidence about the original power.

Finally, the record makes clear why transparent analysis reporting matters. The listed population and descriptive statistics are useful, but the registry record does not report the sponsor's inferential analyses, missing-data procedures, multiplicity strategy, or original sample-size justification. Those details are needed to judge how the planned analysis relates to the recalculated comparisons and how robust the interpretation might be.

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.

Several limitations specific to this record constrain interpretation. The outcome group sizes are modest, particularly for the standard-care group, and the reported standard deviations indicate substantial variation in opioid use. This combination limits the precision of mean differences. The primary intervals are broad, so a range of underlying contrasts remains compatible with the posted summaries.

The primary measure covers only 0 to 24 hours postoperatively. It does not establish what happened outside that interval or whether medication use corresponded to pain intensity. While secondary outcomes include pain ratings, time to first rescue use, and a longer opioid-use interval, the registry record does not post inferential analyses for those outcomes. This restricts assessment of whether the primary pattern aligns with other measures of recovery.

Comparisons are unadjusted recalculations from group summaries. The registry record does not provide sponsor analyses, the original statistical plan, details of missing-data handling, or a multiplicity procedure. The record identifies the Intent-to-Treat Population but does not explain participant inclusion for each summary. These omissions prevent a full audit of the analysis choices and sensitivity to missing observations.

The registry record also does not specify the confidence level for its interval estimates, the identities of people covered by triple masking, or the original sample-size assumptions. Safety results are counts with limited contextual detail, and no comparative safety analysis is reported. Finally, a completed phase II trial with small groups should be read as a limited evidence base; the posted findings do not by themselves support broad conclusions beyond the outcomes and periods recorded.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of a Collagen Bupivacaine Implant in Women Following Abdominal Hysterectomy — NCT00624910.
• Registry record last updated 2021-07-23; status last verified 2021-07.
• Results first posted 2021-01-12.
• 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 record describes a completed randomized, triple-masked, parallel-group phase II trial with enrollment of 54. It compared bupivacaine sponges, collagen sponges, and standard care without an implant. The primary endpoint was mean total opioid rescue analgesia use, in mg morphine equivalents, from 0 to 24 hours after surgery in the Intent-to-Treat Population.

The recalculated, unadjusted primary comparisons show a mean difference of -0.08 for bupivacaine sponges versus standard care and 12.83 for collagen sponges versus standard care. Both intervals include zero and are broad. The registry record does not report sponsor inferential analyses, the original sample-size assumptions, missing-data handling, or multiplicity procedures. Secondary outcomes are listed, but inferential analyses are not reported. Adverse-event counts are descriptive and do not establish causation.