An International Trial to Evaluate the Efficacy and Safety of SABER®-Bupivacaine for Postoperative Pain Control in Patients Following Arthroscopic Shoulder Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An International Trial to Evaluate the Efficacy and Safety of SABER®-Bupivacaine for Postoperative Pain Control in Patients Following Arthroscopic Shoulder Surgery (NCT00993798), a randomized phase 2 study. The primary outcome is Pain Intensity (PI).

2. Clinical Question

The trial’s stated objective was to identify an optimal SABER-Bupivacaine dose based on pharmacokinetics, efficacy, and safety evaluations. The posted primary outcome addresses pain intensity rather than every part of that objective: it records the average movement-related pain score during the specified early postoperative period. The score uses a 0 to 10 numeric rating scale, with 0 meaning no pain and 10 the worst pain imaginable.

The registry also lists time to first opioid rescue medication usage and opioid-related side effects as secondary outcomes. A numerical result for time to first opioid rescue medication usage is not reported in the registry record. The posted opioid-related side-effects measure covers 0-7 days after surgery. The question is therefore best read as a comparison of recorded outcome measures across randomized groups, not as a complete account of every pharmacokinetic, safety, or dose-selection consideration in the trial’s objective.

3. Trial Design

The registry describes NCT00993798 as a completed phase 2 trial with randomized allocation, double masking, and a parallel design. Its official title describes an international, randomized, double-blinded, multicentre trial with active and placebo controls and a dose-response objective. Enrollment was 107. The record lists Durect as the sponsor, a start date of 2009-04, and primary completion in 2011-06.

The study population was patients undergoing elective arthroscopic shoulder surgery. The intervention list contains SABER-Bupivacaine, SABER-placebo, and Bupivacaine HCl treatment labels, with labels ending in 1a, 1b, 1c, 2a, 2b, and 2c. The posted primary outcome summaries use the group names SABER-Bupivacaine, SABER-placebo, and Bupivacaine HCl. Specific doses and the mapping of the treatment labels to the posted groups are not reported in the registry record.

The registry describes screening for up to 14 days, a treatment period of 14 days, and long-term follow-up at 6 months. These are descriptions of the planned study duration; the record does not establish that every participant completed each period. It also does not report the trial’s original sample-size justification, detailed allocation procedures, or the full set of analysis-population definitions. The listed design features describe how the study was organized, but they do not by themselves resolve how missing observations or multiple comparisons were handled.

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 Pain Intensity (PI), measured over 0-3 days after surgery.

The primary endpoint is mean pain intensity on movement during 0-3 days after surgery. Pain was rated on a 0 to 10 numeric rating scale, where 0 represents no pain and 10 represents the worst pain imaginable. The measure is reported as a time-normalized area under the curve (AUC), expressed on the natural pain scale.

For each patient, the AUC was computed using the standard trapezoidal rule and divided by the time interval over which it was calculated. In general, an AUC combines repeated measurements across time into a summary of the outcome’s level over the interval. Dividing by the interval length makes this outcome easier to interpret on the original rating scale rather than as an accumulated quantity. It also allows the trial’s treatment contrast to be expressed in pain-score units.

The endpoint focuses on movement-related pain in the early postoperative period. It is not a single pain rating at one moment, nor does it measure pain beyond the specified interval. The registry gives a mean and standard deviation for each posted group. Lower scores correspond to lower recorded pain intensity on the scale, but the endpoint alone does not describe other aspects of recovery, medication use, or longer-term outcomes.

7. Results Posted in the Registry

• SABER-Bupivacaine: mean 5.16 versus 6.43 on control; difference -1.27 (95% CI -2.14 to -0.40), standardized effect d = -0.67; z-test p = 0.004.
• Bupivacaine HCl: mean 5.16 versus 6.43 on control; difference -1.27 (95% CI -2.38 to -0.16), standardized effect d = -0.60; z-test p = 0.025.

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 Related Side Effects

• 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:
  • SABER-Bupivacaine: mean 0.22 versus 0.22 on control; difference 0.00 (95% CI -0.15 to 0.15), standardized effect d = 0.00; z-test p = 1.000.
  • Bupivacaine HCl: mean 0.25 versus 0.22 on control; difference 0.03 (95% CI -0.11 to 0.17), standardized effect d = 0.12; z-test p = 0.679.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SABER-Bupivacaine 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 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes offer a more limited and less definitive picture than the primary pain-intensity comparison. The registry lists time to first opioid rescue medication usage and opioid-related side effects. A numerical result for time to first opioid rescue medication usage is not reported in the registry record. The posted opioid-related side-effects measure covers 0-7 days after surgery, and its sponsor-reported comparison does not indicate a clear group difference in the model-based result.

That secondary pattern does not reproduce the primary outcome’s estimated separation in group averages. It also does not contradict the primary result: opioid-related side effects and pain intensity are different measures, assessed over different periods. The registry record does not establish how these outcomes relate at the participant level or whether changes in one measure correspond to changes in another.

The secondary findings should carry less weight than the primary result when drawing an overall statistical conclusion. In general, testing multiple outcomes and comparisons increases the opportunity to observe apparently notable results by chance, especially when the analyses are unadjusted. The record does not report whether a multiplicity plan was specified or applied. The recalculated secondary p-values are unadjusted, and the sponsor’s secondary analysis does not establish that all planned comparisons were accounted for.

Secondary measures can still be informative about the range of outcomes considered, but the registry does not provide enough detail to determine the role assigned to each measure in the original analysis plan. The absence of a numerical result for time to first opioid rescue medication usage should not be interpreted as evidence of no difference. More broadly, the posted secondary information is not a substitute for a complete outcome-by-outcome analysis, including prespecified hypotheses, analysis populations, and handling of missing observations.

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

• Time to First Opioid Rescue Medication Usage
• Opioid Related Side Effects

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric pain score summarized as a mean for each group. The registry reports each group’s mean and standard deviation. A mean describes the group’s average recorded score, while a standard deviation describes how spread out individual scores were around that average. In general, the standard deviation is a description of variability among observations, not the uncertainty of the group mean or of a treatment contrast.

The recalculated mean difference compares the SABER-Bupivacaine group with the SABER-placebo group by subtracting the placebo mean from the SABER-Bupivacaine mean. The posted recalculated estimate is -1.27. A negative estimate indicates a lower average pain score in the SABER-Bupivacaine group. The same direction applies to the recalculated Bupivacaine HCl comparison. These recalculations use the posted summary statistics and are unadjusted; they are not substitutes for a trial analysis that may account for design features or covariates.

A confidence interval expresses a range of values compatible with the estimate under the assumptions of the analysis. In general, a narrower interval indicates greater precision than a wider interval, while an interval that includes values on both sides of zero is compatible with contrasts in either direction. The recalculated primary interval does not include zero. Its interpretation is still conditional on the method and data used; it does not measure the chance that an individual participant will have a particular result.

The reported primary method is a t-test in an ANOVA model, with the result expressed as an LS mean difference. In general, an ANOVA model estimates group contrasts while representing variation in the outcome; a least-squares mean is a model-based group mean or contrast. The registry gives the reported estimate, interval, and p-value but does not report the model specification, covariates, or other details needed to reproduce that adjusted analysis. The recalculated unadjusted comparison and the sponsor’s model-based analysis therefore answer closely related but not necessarily identical statistical questions.

The posted comparisons also include pooled standard deviations and standardized effect estimates. In general, a standardized effect expresses a mean contrast relative to a measure of variability, making the contrast less dependent on the outcome’s original units. For SABER-Bupivacaine versus SABER-placebo, the posted standardized effect estimate is -0.673; for Bupivacaine HCl versus SABER-placebo, it is -0.599. These standardized quantities do not replace the mean difference in pain-score units, which is more directly tied to the scale used in the trial.

Each p-value is a measure of how inconsistent the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not quantify the clinical importance of a contrast. The recalculated p-values are explicitly unadjusted. The registry’s reported primary p-value comes from the stated ANOVA analysis. Details of any multiplicity adjustment are not reported in the registry record, so these p-values should not be treated as if they necessarily account for all outcomes or comparisons considered.

The secondary opioid-related side-effects measure is also continuous and is summarized by group means and standard deviations. The sponsor reports an ANOVA result for final values. The recalculated SABER-Bupivacaine comparison has a mean difference of 0.0, a 95% confidence interval from -0.152 to 0.152, and unadjusted p = 1.0. The Bupivacaine HCl comparison has a recalculated mean difference of 0.03, with a 95% confidence interval from -0.112 to 0.172 and unadjusted p = 0.679. In general, uncertainty around a small estimated difference is important: a non-small p-value does not demonstrate equivalence, particularly when the interval remains compatible with more than one direction of contrast.

For planning illustrations, the posted assumptions specify a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. In general, over-dispersion means that outcome variability is greater than a model assumes; when present, it can make standard errors and significance tests too optimistic if not accounted for. The registry record does not report an over-dispersion assessment or a method for handling it, and the primary continuous-outcome analyses should not be presumed to have used a particular additional correction.

11. Confidence Intervals and Precision

The recalculated primary mean difference is -1.27, with a 95% confidence interval from -2.138 to -0.402. This interval conveys the precision of the unadjusted estimate: values throughout the interval represent contrasts compatible with the data under the recalculation’s assumptions. The interval is on the original pain-score scale, which makes it interpretable in the same units as the 0 to 10 rating measure.

The sponsor’s reported primary interval is -2.25 to -0.28. It also lies below zero, but it is not identical to the recalculated interval. The sponsor’s estimate comes from a t-test in an ANOVA model and is reported as an LS mean difference; the recalculation uses posted group summaries without that model-based adjustment. Different methods can produce different uncertainty estimates even when their point estimates agree. The registry record does not provide model details that would allow a fuller reconstruction of the sponsor’s interval.

The recalculated Bupivacaine HCl comparison has a wider interval, -2.38 to -0.160. That interval also excludes zero, but it expresses less precision than the primary recalculated comparison. General interpretation of precision should consider interval width and the scale of the outcome, not just whether the interval includes zero or whether a p-value crosses a threshold.

A confidence interval is not a range containing every participant’s likely response, and it is not a guarantee that the true contrast lies within the displayed endpoints. It describes uncertainty about a group-level estimate under a specified statistical procedure. The posted group standard deviations describe variability among recorded scores, whereas the confidence intervals describe uncertainty in the contrasts. The registry does not report confidence intervals for each group mean or the distribution of individual treatment responses.

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 figures are participants per arm for comparisons of two arms. They are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. These are planning illustrations based on the observed effect, not the trial’s original design assumptions. The trial’s own sample-size justification is not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% probability of detecting the specified effect under the planning assumptions, if that effect and the other assumptions are correct. The 90% power column uses a higher target probability of detection. In general, a higher target power requires more participants when other assumptions stay the same.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect illustrate how the planning requirement changes when the effect being targeted is smaller than the observed contrast. Smaller effects need more participants to detect, all else equal. The displayed values are specific to the comparison and its observed effect; they should not be read as a universal requirement for another study or outcome.

This is not observed power. It is a planning illustration and does not measure the probability that the completed trial’s result is correct or that a future study will reproduce it. The registry does not report the assumptions used in the original protocol’s sample-size calculation, so these illustrations cannot establish whether the trial enrollment matched its original planning 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 = -1.270; pooled standard deviation σ = 1.888.
2. n = 2 × (1.96 + 0.842)² × 1.888² / -1.270² = 34.7, rounded up to 35 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 <- -1.27                      # observed difference in means
sigma <- 1.88797022724072                     # 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(993798)
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 = 35 (80% power), 47 (90% power)
 75% of observed effect: n per arm = 62 (80% power), 83 (90% power)
 50% of observed effect: n per arm = 139 (80% power), 186 (90% power)
power.t.test: 35.7 
Simulated power at n = 35 per arm: 0.790 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary comparison is a model-based analysis described as a t-test in an ANOVA model, with an LS mean difference of -1.27 and a 95% confidence interval from -2.25 to -0.28; p = 0.012. The recalculated unadjusted comparison has the same point estimate, -1.27, but a 95% confidence interval from -2.138 to -0.402 and p = 0.004.

The matching point estimates indicate that both analyses place the group-average contrast in the same direction and at the same displayed magnitude. The interval and p-value differ because the recalculation and reported analysis use different methods. The recalculation is based on the posted group summaries; the sponsor reports an ANOVA-model result. Details of the sponsor’s model beyond the stated method are not reported in the registry record.

The registry record does not flag a discrepancy between the recalculation and the sponsor’s primary result. The sponsor’s analysis is therefore best read as the reported trial analysis, while the recalculation is a supplementary unadjusted check from summary statistics. They should not be treated as interchangeable analyses or as independent replications. The separate Bupivacaine HCl recalculation is not accompanied by a sponsor-reported result in the posted analyses, so it does not have the same direct comparison between reported and recalculated methods.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, treatment contrasts, time points, or analyses are examined. In general, the more statistical tests considered, the greater the chance that at least one will appear noteworthy even if no underlying contrast exists. Common approaches include prespecifying a primary comparison, adjusting significance thresholds, or organizing tests in a hierarchy. These approaches address different inferential goals and cannot be assumed without documentation.

The registry identifies a primary endpoint and lists secondary outcomes, including time to first opioid rescue medication usage and opioid-related side effects. It posts a primary sponsor analysis and a secondary sponsor analysis. Whether the protocol or statistical analysis plan included a multiplicity strategy, and whether any adjustment was performed, is not reported in the registry record. The recalculated p-values are unadjusted. They therefore should not be interpreted as accounting for all possible outcomes, contrasts, or analyses.

The record also does not report the analysis-population definitions for the primary endpoint, such as whether the analysis followed an intention-to-treat, per-protocol, or other rule. The numbers contributing to each posted outcome are available in the group summaries, but reasons for differences in analyzed group sizes across outcomes are not reported in the registry record. The handling of missing outcome measurements, withdrawals, protocol deviations, or imputation is also not reported in the registry record.

These omissions matter because missingness and analysis-population choices can affect the group estimates and their uncertainty. In general, an analysis based only on participants with recorded outcomes can be biased if the availability of measurements is related to the outcome or assigned group. The registry record does not provide information sufficient to assess whether that concern applies. The appropriate conclusion is not that the analyses were necessarily flawed, but that the posted record leaves important safeguards and analytic decisions undocumented.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: drug intolerance (4.0%), pleurisy (3.4%), musculoskeletal pain (3.4%), tongue paralysis (3.4%), pregnancy (3.4%).

The registry reports serious adverse events for SABER-Bupivacaine, SABER-placebo, and Bupivacaine HCl. The numbers at risk were 53, 25, and 29, respectively; the corresponding serious adverse event counts were 1, 1, and 4. These are counts of participants with a serious adverse event, not a measure of event severity beyond the registry’s serious-event classification or of causal attribution to treatment.

The record also reports other adverse event counts of 12 for SABER-Bupivacaine, 6 for SABER-placebo, and 6 for Bupivacaine HCl. Deaths are recorded as 0 in each group. The registry lists several serious-event terms with percentages, including Drug intolerance at 4.0%, Pleurisy at 3.4%, Musculoskeletal pain at 3.4%, Tongue paralysis at 3.4%, Pregnancy at 3.4%, and Pulmonary arterial hypertension at 1.9%. The record does not provide enough context in these figures alone to infer causation or compare risks reliably.

Safety counts are descriptive and should be interpreted alongside the group sizes, follow-up, event definitions, and ascertainment procedures. Further details about attribution and the analysis of safety events are not reported in the registry record.

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

The posted primary data describe lower mean movement-related pain scores in the SABER-Bupivacaine group than in the SABER-placebo group during 0-3 days after surgery. The recalculated unadjusted estimate is -1.27 points, and the sponsor’s reported model-based estimate is also -1.27. Their confidence intervals differ, but both are reported zero. This is a statistical description of group averages for the recorded endpoint.

It does not establish that every participant experienced a lower score, nor does it describe how many participants had meaningful improvement, no change, or worse scores. The registry record does not report a threshold for clinical importance on the pain scale. Statistical evidence about a mean difference is not by itself a judgment about the value of that difference to patients.

The result also does not settle the trial’s broader dose-selection objective. Specific doses and the detailed pharmacokinetic findings are not reported in the registry record. The posted comparisons do not establish the best dose, and they do not supply a complete comparison of all treatment labels. The Bupivacaine HCl result is a separate recalculated contrast with SABER-placebo; it is not a substitute for a reported sponsor analysis of every treatment comparison.

Nor do these results establish effects beyond the measured time interval or on outcomes that are not numerically reported. The record lists opioid rescue medication timing, but a numerical result is not reported in the registry record. The secondary opioid-related side-effects measure is distinct from pain intensity. Safety counts are also descriptive and do not, on their own, determine whether an event was caused by a treatment.

Overall, the findings support a comparison of recorded group-average outcomes under the posted analyses. Unreported analysis details, missing-data handling, multiplicity procedures, and population definitions limit how completely the registry record can characterize the trial’s evidence.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation benefits from separating an estimated effect from its uncertainty and from the method used to obtain it. The sponsor’s reported mean difference and the unadjusted recalculation agree in displayed magnitude, while the confidence intervals and p-values differ. That pattern shows how model-based and summary-statistic analyses can produce related but non-identical inferential results.

The primary outcome also demonstrates the value of understanding how a continuous endpoint was constructed. The time-normalized AUC combines movement-related pain scores over an early postoperative interval and expresses the result on the original pain scale. Without understanding that normalization, an AUC could be mistaken for a cumulative score rather than an average-scale summary over time.

The registry includes active and placebo comparisons, secondary outcomes, and safety counts, but those results do not all answer the same question. The primary pain measure, opioid-related side-effects measure, time to first opioid rescue medication usage, and adverse events have different definitions and timeframes. A coherent reading therefore requires attention to endpoint, comparator, analysis, and uncertainty rather than treating every reported statistic as interchangeable.

Finally, the record illustrates the importance of transparent reporting. The original sample-size justification, multiplicity strategy, missing-data handling, and analysis-population definitions are not reported in the registry record. Those details affect how confidently readers can connect a result to a prespecified plan. Recognizing what is documented and what remains unknown is part of sound biostatistical interpretation.

19. Limitations

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

The registry record does not report the specific doses associated with the SABER-Bupivacaine treatment labels or explain how those labels map to the three posted group summaries. That limits interpretation of the stated dose-response objective and prevents assessment of a dose-specific pattern from the posted primary summaries alone.

For the primary sponsor analysis, the registry gives the method and result but does not report the model specification, covariates, or analysis-population definition. The handling of missing measurements and withdrawals is not reported in the registry record. Those details would be needed to assess whether the reported analysis represents all randomized participants and how incomplete outcome data may have influenced estimates.

The registry does not report the original sample-size justification or whether a multiplicity strategy was planned and applied. The posted planning figures are illustrations based on observed effects, not evidence about the trial’s original design assumptions. Without documentation of the prespecified plan, it is difficult to judge how the analyses relate to the trial’s intended confirmatory questions.

Numerical results for time to first opioid rescue medication usage are not reported in the registry record, despite that outcome being listed. The secondary side-effects result and safety counts provide only part of the broader efficacy and safety picture described in the trial objective. Further detail on event attribution, ascertainment, and follow-up by outcome is not reported in the registry record.

Finally, the primary endpoint is an average over 0-3 days after surgery. It does not convey individual response patterns or pain outcomes outside that interval. The registry record does not report a clinical-importance threshold for the scale, so the statistical estimates cannot alone determine the practical importance of the observed mean contrast.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: An International Trial to Evaluate the Efficacy and Safety of SABER®-Bupivacaine for Postoperative Pain Control in Patients Following Arthroscopic Shoulder Surgery — NCT00993798.
• Registry record last updated 2021-06-09; status last verified 2021-05.
• Results first posted 2021-06-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT00993798 is a completed phase 2 randomized, double-blind, parallel trial sponsored by Durect. It enrolled 107 patients undergoing elective arthroscopic shoulder surgery and evaluated SABER-Bupivacaine against SABER-placebo, with Bupivacaine HCl also listed as an active comparator.

The primary outcome was mean movement-related pain intensity measured as a time-normalized AUC over 0-3 days after surgery. The recalculated SABER-Bupivacaine versus SABER-placebo mean difference is -1.27, while the sponsor’s reported model-based estimate is also -1.27. The registry additionally reports secondary opioid-related side-effects findings and adverse-event counts. Important details, including the original sample-size justification, missing-data methods, multiplicity procedures, and analysis-population definitions, are not reported in the registry record.