Postoperative Belladonna and Morphine Suppositories in Vaginal Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Postoperative Belladonna and Morphine Suppositories in Vaginal Surgery (NCT01150474), a randomized phase 4 study. The primary outcome is Pain at Hour 4.

2. Clinical Question

3. Trial Design

The registry record describes a Phase 4, randomized, quadruple-masked, parallel-group trial comparing belladonna and opium suppositories with placebo suppositories after vaginal surgery. The record lists an enrollment of 103. The listed arm-level primary outcome summaries include 41 participants in the belladonna and opium group and 49 in the placebo group; the record does not explain the relationship between these analysis counts and the enrollment figure.

The active suppository contained belladonna (16.2 mg) and opium (60 mg). Both groups were assigned rectal suppositories immediately after surgery and every 8 hours for 16 hours, for a total of 3 doses. The placebo group followed the same administration schedule. The trial’s stated primary aim was to determine whether routine use of the active suppositories would improve pain control following vaginal surgery.

The primary outcome was pain at Hour 4, with the timeframe specified as 4 hours following surgery. The record also identifies secondary outcomes covering pain at Hour 12 and Hour 20, narcotic rescue medication, nausea and vomiting, antiemetic rescue medication, and satisfaction with pain relief. More detail on the reported secondary results and their limits is discussed separately.

The registry record lists the trial as completed. It gives the start as 2011-01 and primary completion as 2013-12. Further details about the randomization procedure, the people masked, concealment of allocation, site count, eligibility criteria, and the original analysis plan are not reported in the registry record. The record identifies a two-sided t-test for the sponsor’s reported primary comparison, but does not describe additional model or population details.

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:

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 at Hour 4, measured over 4 hours following surgery.

The primary endpoint is mean pain at 4 hours following surgery. Pain was recorded using a linear analog pain scale, with 0 meaning no pain and 10 meaning worst pain imaginable. The registry record specifies a mean and standard deviation for this continuous measure. A mean describes the group’s average reported pain, while the standard deviation describes variation in scores among participants; it is not a measure of uncertainty in the mean difference.

Pain is the direct outcome in the trial’s stated primary question: whether routine use of the active suppositories would improve pain control after vaginal surgery. Measuring it at a stated postoperative time gives the comparison a defined timeframe. The scale’s endpoints give readers an interpretation for the direction and bounds of the reported scores, though the registry record does not report a threshold for a difference considered important to patients or clinicians.

The group means were 4.2 for belladonna and opium and 4.1 for placebo. The recalculated mean difference, defined as active treatment minus placebo, was 0.1 units on a scale. That small difference in the observed averages is not, by itself, a precise estimate of the underlying group difference. Its interval and the limits of what can be inferred from it are addressed in the statistical interpretation.

7. Results Posted in the Registry

• Belladonna and Opium Suppositories: mean 4.20 versus 4.10 on control; difference 0.10 (95% CI -0.84 to 1.04), standardized effect d = 0.04; z-test p = 0.835.

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.

Pain at Hour 12

• 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:
  • Belladonna and Opium Suppositories: mean 3.40 versus 3.30 on control; difference 0.10 (95% CI -0.86 to 1.06), standardized effect d = 0.04; z-test p = 0.838.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belladonna and Opium Suppositories and the control. The interval gives the range of effects that remain compatible with the data.

Pain at Hour 20

• 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:
  • Belladonna and Opium Suppositories: mean 2.50 versus 3.40 on control; difference -0.90 (95% CI -1.81 to 0.01), standardized effect d = -0.40; z-test p = 0.053.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belladonna and Opium Suppositories and the control. The interval gives the range of effects that remain compatible with the data.

Narcotic Rescue Medication

• 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:
  • Belladonna and Opium Suppositories: mean 57.00 versus 66.00 on control; difference -9.00 (95% CI -29.66 to 11.66), standardized effect d = -0.17; z-test p = 0.393.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belladonna and Opium Suppositories and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the trial’s questions beyond pain at the primary timepoint. They include pain at later postoperative times, narcotic rescue medication, nausea and vomiting, use of antiemetic rescue medication, and satisfaction with pain relief. The numerical summaries available in the record for pain at Hour 12 and Hour 20 and for narcotic rescue medication offer additional context, but they do not change which outcome was designated primary.

Across the reported continuous secondary comparisons, the observed pattern is not uniform in direction or precision. The later pain comparisons and rescue-medication comparison have estimates with intervals that include zero. One later pain estimate is closer to a conventional statistical threshold than the primary comparison, but its sponsor-reported test does not provide clear evidence of a difference. The secondary results therefore do not form a consistent, decisive pattern that resolves uncertainty in the primary result. Their estimates should be read alongside their intervals and the analysis methods, rather than selected on the basis of a p-value alone.

The registry record lists additional secondary outcomes concerning nausea, vomiting, antiemetic use, and satisfaction. Numerical summaries for those outcomes are not reported in the registry record. Their presence in the outcome list does not establish whether groups differed on them.

Secondary findings usually carry less weight than the primary result when many outcomes are considered, because examining multiple comparisons increases the chance of seeing an apparently notable result by chance. The registry record does not report a multiplicity adjustment or a hierarchy controlling how these outcomes were tested. These results are therefore best treated as supportive or exploratory context, not as independent confirmation of a treatment effect. The record also does not report a prespecified interpretation framework for combining the primary and secondary outcomes.

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

• Pain at Hour 12
• Pain at Hour 20
• Narcotic Rescue Medication
• Number of Subjects With Nausea
• Number of Subjects With Vomiting
• Number of Times Antiemetic Rescue Medication Was Used
• Number of Subjects Who Used Antiemetic Rescue Medications
• Satisfaction With Pain Relief

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent?

The primary outcome is continuous, and the registry record reports a mean and standard deviation for each group. The mean difference compares the two group averages. In the recalculation, the difference is expressed as the belladonna and opium mean minus the placebo mean. A positive value therefore indicates a higher observed average in the active group; a negative value indicates a lower observed average. The primary estimate is 0.1 units on a scale.

The standard deviation describes how spread out individual pain scores are around a group mean. It is different from the standard error, which describes the precision of an estimated mean. The posted arm summaries give standard deviations of 2.4 for the active group and 2.1 for placebo. Variation among individual scores is relevant because a mean difference must be interpreted in relation to the spread and amount of data, not only by comparing the two means.

How should the interval be read?

An interval around an estimated difference gives a range of values compatible with the observed data under the method used. It conveys precision as well as direction: a narrower interval indicates a more precise estimate, while a wider interval leaves greater uncertainty about the size of the difference. The recalculated primary interval extends from -0.841 to 1.041 units on a scale. Since it spans zero, it does not isolate a difference in one direction. The registry record does not give a confidence level for the reported interval, so a particular coverage percentage is not assigned.

What does the p-value add?

A p-value measures how unusual results at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the probability that the null model is true, and it does not measure the probability that a result will replicate. The sponsor reports a two-sided t-test for the primary comparison with p = 0.82. The unadjusted recalculation gives p = 0.835. Neither value should be used alone: the estimated difference and its interval provide information about the scale and uncertainty of the comparison.

A two-sided test considers departures in either direction rather than testing only whether one group has a lower mean. The registry record identifies this test for the sponsor analysis. Details such as whether the test used equal-variance assumptions, how missing measurements were handled, and whether any covariate adjustment was planned are not reported in the registry record.

Why do standard deviations and sample sizes matter?

Uncertainty in a group comparison depends on the amount of information and the variability in the outcome. Greater variation makes it harder to distinguish a group difference from ordinary differences among individuals. More observations can improve precision, all else being equal, but they do not remove bias from missing data, measurement, or design. The arm-level summaries for the primary endpoint report 41 participants in the active group and 49 in the placebo group. The registry record does not state whether the primary analysis followed an intention-to-treat, per-protocol, or other population definition.

The recalculation is a simple unadjusted comparison based on the posted summary statistics. It is not a substitute for an individual-participant-data analysis or for any prespecified model used by the trial. The registry record does not report a fuller statistical analysis plan, including any adjustment variables or model diagnostics.

Why can over-dispersion matter in other outcomes?

General statistical context: for count outcomes, a simple model may assume that the variance follows a particular relationship to the mean. If real data are more variable than that model expects, or over-dispersed, standard errors can be too small and tests can appear more decisive than warranted. Methods that account for over-dispersion can be appropriate when the data support them. This trial’s primary endpoint is a continuous pain score, and the registry record does not report an over-dispersion analysis. The general concept should not be taken to imply that over-dispersion occurred in this trial.

11. Confidence Intervals and Precision

The recalculated primary mean difference is 0.1 units on a scale, with an interval from -0.841 to 1.041. The interval is wide enough to include a negative difference, zero, and a positive difference. In plain terms, the posted summary data do not pin down the underlying difference tightly or establish its direction. The observed means are close, but closeness of the point estimates is not the same as precision.

The standard deviations were 2.4 in the active group and 2.1 in the placebo group. These describe variation among participant scores, not the uncertainty of the mean difference itself. The arm-level primary outcome counts were 41 and 49, respectively. Together, sample size and outcome variability inform the uncertainty of an estimated group contrast, but they do not reveal why a result may be uncertain or whether the endpoint was measured consistently.

The interval’s inclusion of zero is consistent with the unadjusted recalculated p-value of 0.835 and the sponsor-reported p-value of 0.82. These statistics do not demonstrate equivalence: an equivalence conclusion would require an appropriate design and a prespecified margin, neither of which is reported in the registry record. Nor does the interval describe the full range of possible effects with certainty; it is an estimate based on the analysis method.

The registry record does not report an interval for the sponsor’s analysis, its confidence level, or a threshold for clinical importance. Accordingly, the recalculated interval should be understood as an unadjusted analysis of posted summaries, while the sponsor’s reported test is the registry’s own analysis. Both leave substantial uncertainty about whether any underlying difference is small enough to be unimportant or large enough to matter.

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 expressed as participants per arm, not as a total across arms or as total events. They are illustrations computed from the observed effect, not the trial’s original design assumptions. The stated 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 set in turn to the stated fraction of the observed effect.

The 80% power column gives the planned number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is real and the model assumptions apply. The 90% power column gives the corresponding number for a higher chance of detecting that effect. These are planning targets, not guarantees for a future study. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

The planning illustrations use the observed primary difference and smaller fractions of it. Because a smaller effect is harder to distinguish from random variation, the planning figures increase as the target effect is reduced. For the primary outcome, planning for 100% of the observed effect gives 7,886 participants per arm for 80% power and 10,558 participants per arm for 90% power; planning for 75% gives 14,020 and 18,769; planning for 50% gives 31,544 and 42,229. These are illustrations based on the observed estimate, not evidence that the trial had any particular power. This is not observed power.

The observed effect may be a poor basis for future planning, especially when it is estimated imprecisely. A future design would generally need a target difference chosen for scientific or clinical reasons, along with assumptions about variability and the analysis. The registry record does not report the trial’s original justification or the rationale for the assumptions in these illustrations.

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 = 0.100; pooled standard deviation σ = 2.241.
2. n = 2 × (1.96 + 0.842)² × 2.241² / 0.100² = 7,886.0, rounded up to 7,886 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 <- 0.100000000000001                      # observed difference in means
sigma <- 2.24134699759684                     # 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(1150474)
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 = 7,886 (80% power), 10,558 (90% power)
 75% of observed effect: n per arm = 14,020 (80% power), 18,769 (90% power)
 50% of observed effect: n per arm = 31,544 (80% power), 42,229 (90% power)
power.t.test: 7886.9 
Simulated power at n = 7,886 per arm: 0.805 (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 registry record reports the sponsor’s primary analysis as a two-sided t-test with p = 0.82. A simple unadjusted recalculation from the posted group means, standard deviations, and analysis counts gives a mean difference of 0.1 units on a scale, an interval from -0.841 to 1.041, and p = 0.835. The registry record does not report a sponsor-estimated mean difference or interval for this comparison, so the recalculated estimate and interval are not a direct reproduction of a complete sponsor result.

The two p-values are close and lead to the same broad reading: the posted primary comparison does not show a clear statistical separation between the groups. The recalculation is based on summary statistics and cannot account for participant-level features or any analysis choices not reported in the registry record. It should therefore be treated as a check on the scale and uncertainty of the comparison, not as a replacement for the trial’s own analysis.

No discrepancy is flagged in the registry record. Where a recalculation conflicts with the sponsor’s own analysis, the sponsor’s analysis takes precedence. Here, the broad interpretation is similar, while the sponsor’s p-value remains the reported trial analysis and the recalculated estimate provides an unadjusted summary-based perspective.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary pain outcome and multiple secondary outcomes. It does not report whether the investigators adjusted for multiple comparisons, set a testing hierarchy, or otherwise controlled the chance of false-positive findings across the outcome set. When many outcomes are tested, the chance of at least one apparently unusual result can increase even if no underlying group differences exist. This general concern is especially relevant when interpreting an isolated secondary result. Without a reported multiplicity plan, secondary p-values should not be treated as if each were the only test performed.

The registry record reports a two-sided t-test for the primary comparison and identifies two-sided t-tests for the listed continuous secondary comparisons. It does not report whether other analyses were specified for the remaining secondary outcomes, whether any tests were adjusted, or whether the posted analyses were prespecified. The statistical analysis plan is not reported in the registry record.

The analysis population is also not described in sufficient detail. The record does not report whether the primary analysis was intention-to-treat, per-protocol, or based on another population definition. It does not explain how participants with missing outcome data were handled, whether observations were excluded, or whether any imputation or sensitivity analysis was used. The listed enrollment and arm-level outcome counts do not by themselves establish why those figures differ.

These omissions limit assessment of potential bias and of how closely the reported analyses follow the intended design. Randomization helps support a fair comparison when analyzed appropriately, but it does not eliminate uncertainty caused by missing outcomes, selective analysis, or unreported decisions. The registry record does not report interim analyses, stopping rules, or a plan for handling deviations from the assigned schedule. Those details should not be assumed in either direction.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abdominal sepsis (2.4%).

The registry record reports serious adverse events in 1 participant in the belladonna and opium group and 0 participants in the placebo group. The corresponding groups at risk were 41 and 49. The record lists Abdominal Sepsis at 2.4% among the top serious-event terms. These are descriptive safety figures from the registry record; they do not establish that the intervention caused or prevented an event, and the event count is too limited to characterize uncommon harms precisely.

For other adverse events, the record reports 24 affected participants among 41 at risk in the active group and 27 among 49 at risk in the placebo group. The registry information does not provide enough detail to interpret the nature, timing, severity, or causal attribution of those events. Deaths are not reported in the registry record. Absence of a reported figure should not be interpreted as evidence that no deaths occurred.

Safety comparisons depend on how events were defined, collected, and assessed, as well as on the duration and completeness of follow-up. Further details about those procedures are not reported in the registry record. These figures are not a substitute for a full clinical safety assessment.

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

The primary result describes a randomized comparison of postoperative pain scores after vaginal surgery. The observed mean scores were 4.2 with belladonna and opium suppositories and 4.1 with placebo at 4 hours following surgery. The recalculated difference is small in the scale’s units, but its interval includes zero and extends in both directions. The data therefore do not establish a clear difference in mean pain at this timepoint.

That interpretation is narrower than saying the treatments are equivalent, or that one has no effect. The registry record does not report a prespecified equivalence or noninferiority design, a margin defining a negligible difference, or a clinical threshold for interpreting pain-score changes. A non-significant test cannot establish that effects are identical. It indicates that the observed comparison does not provide clear statistical evidence against the null model under the reported test.

The posted secondary results add context but do not settle the primary uncertainty. Several outcomes are listed, while numerical results for some listed outcomes are not reported in the registry record. Secondary comparisons also raise multiplicity concerns because the record does not report an adjustment plan. The sponsor’s reported primary test and the summary-based recalculation point to the same broad reading, while the recalculation adds an interval that makes the uncertainty in the estimated difference more visible.

These findings apply to the trial comparison and the reported postoperative timepoints. The registry record does not provide detailed eligibility information, participant-level data, full follow-up procedures, or enough information to assess generalizability to other settings. The result should not be extended to other operations, treatment schedules, or patient groups without evidence. It is a statistical description of the posted trial data, not medical advice or a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate, a p-value, and an interval answer different questions. The point estimate describes the observed contrast in group means. The p-value summarizes compatibility with a null model under a particular test. The interval conveys how imprecisely the contrast is estimated and which directions remain compatible with the posted data. Reading these together avoids treating a single threshold as the whole result.

It also shows why a small observed difference is not automatically evidence of equivalence. A conclusion of equivalence requires an appropriate design and a prespecified margin, and neither is reported in the registry record. An interval that includes zero can reflect a small underlying difference, uncertainty about direction, or both. The data do not settle which interpretation is correct.

The planning illustrations demonstrate how sample-size needs depend on the target difference. They are based on the observed effect, which is itself uncertain, and are not the trial’s original design justification. A planning exercise should be anchored to a target that matters scientifically or clinically and to transparent assumptions about variability and analysis. Treating an observed result as a fixed truth can produce misleading expectations for future studies.

Finally, the trial raises familiar interpretation issues in clinical research: multiple endpoints, incomplete reporting of analysis populations and missing-data handling, and limits in rare-event safety summaries. These do not invalidate the findings, but they constrain how confidently readers can interpret them. Clear reporting of protocols, analysis plans, intervals, and outcome handling is essential for distinguishing a measured result from the broader claims someone might wish to make.

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.

Several limitations are specific to what the registry record reports. It gives no detailed eligibility criteria, so it is not possible to assess precisely which patients or surgical circumstances the results represent. The record also does not describe the randomization procedure, allocation concealment, or which parties were masked, despite listing quadruple masking. The label alone does not specify how masking was implemented.

The primary group summaries include 41 participants for belladonna and opium and 49 for placebo, while the record gives enrollment as 103. The record does not explain the relationship between enrollment and the endpoint analysis counts. It also does not report the analysis population, reasons for missing outcome data, handling of missingness, or sensitivity analyses. These gaps limit assessment of whether the analyzed participants represent the randomized groups.

The registry record identifies the primary test but does not provide a full statistical analysis plan, including any planned covariates, assumptions, or protocol deviations. It does not report a confidence level for the recalculated interval, a clinically important difference threshold, or an equivalence or noninferiority margin. It also does not report a multiplicity plan for the several secondary outcomes.

The primary endpoint is self-reported pain at a specified postoperative time, and the summary statistics do not show individual score distributions. Numerical secondary results are not reported in the registry record for several listed outcomes. Safety reporting gives limited event summaries, with no additional event-collection or attribution details. Finally, the recalculated comparison uses posted group summaries and cannot reproduce unreported analyses or address participant-level features.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Postoperative Belladonna and Morphine Suppositories in Vaginal Surgery — NCT01150474.
• Registry record last updated 2015-01-07; status last verified 2014-12.
• Results first posted 2015-01-07.
• 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

The registry record describes a completed Phase 4 randomized, quadruple-masked, parallel-group trial of belladonna and opium suppositories versus placebo after vaginal surgery. The listed enrollment is 103. The active regimen was administered rectally immediately after surgery and every 8 hours for 16 hours, for a total of 3 doses; the placebo followed the same schedule.

The primary endpoint was mean pain at 4 hours following surgery, measured on a linear analog scale from 0 to 10. The group means were 4.2 and 4.1, and the unadjusted recalculated mean difference was 0.1 units on a scale, with an interval from -0.841 to 1.041. The sponsor reported a two-sided t-test with p = 0.82; the recalculated p-value was 0.835.

The primary comparison does not show a clear statistical separation, and the interval leaves uncertainty about the direction and size of any underlying difference. The registry record does not report several details needed for fuller assessment, including the analysis population, missing-data handling, and multiplicity plan.