The Use of Belladonna and Opium Suppository in the Treatment of Postoperative Stent Pain: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Use of Belladonna and Opium Suppository in the Treatment of Postoperative Stent Pain (NCT03332056), a randomized phase 4 study. The primary outcome is Global Quality of Life Score on Postoperative Day 1.

2. Clinical Question

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group study. It is listed as phase 4 and completed. The sponsor was the University of Washington. The registry lists a start of 2013-08 and primary completion of 2014-10. Enrollment was 71. Those details describe the trial record; further information about recruitment, sites, eligibility criteria, or participant flow is not reported in the registry record.

Participants were assigned to B&O suppository or placebo suppository. The registry reports 35 participants in the B&O arm and 34 in the placebo arm for the primary outcome. The intervention description specifies a single dose-weight-calculated B&O suppository administered after positioning and before instrumentation. The placebo arm is described as receiving a placebo suppository. The record does not report how the random sequence was generated, how allocation was concealed, or which groups of people were masked under the quadruple-masking label.

The primary outcome was global quality of life on postoperative day 1, measured with the USSQ. Secondary outcomes listed in the record include postoperative complications, unanticipated postoperative visits, and postoperative narcotic use. Numerical results are posted for unanticipated postoperative visits and narcotic use; a numerical result for postoperative complications is not reported in the registry record.

The record gives no account of the original sample-size justification, planned statistical analysis, analysis populations, missing-data procedures, or interim analyses. Those omissions limit what can be concluded about how the trial was designed to answer its question and how the reported comparisons relate to any prespecified plan.

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 Global Quality of Life Score on Postoperative Day 1, measured over postoperative day 1.

The primary endpoint is the global quality-of-life score on postoperative day 1. It was measured with the Ureteral Stent Symptom Questionnaire and reported as a mean with standard deviation. The scale ranges from 1 to 7: lower scores indicate better quality of life than higher scores. The registry describes the scale anchors from delighted at 1 to terrible at 7, with intermediate responses covering satisfaction, mixed feelings, dissatisfaction, and unhappiness.

A patient-reported quality-of-life score can capture the overall experience of symptoms and wellbeing at a defined time point. In this study, the endpoint offers a way to compare the postoperative experience between the B&O and placebo groups, rather than relying only on a single symptom or medication-use measure. Its interpretation depends on the direction of the scale: a lower mean represents a more favorable score, not a worse one.

The endpoint is specific to postoperative day 1. It does not directly describe symptoms at other times or establish how participants felt over the full postoperative period. The registry does not report a threshold for a clinically important score difference, and it does not provide further information about the questionnaire’s administration or handling of missing responses.

7. Results Posted in the Registry

• Belladonna and Opium (B&O) Suppository: mean 4.40 versus 5.40 on control; difference -1.00 (95% CI -1.45 to -0.55), standardized effect d = -1.06; z-test p = <0.001.

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.

Number of Participants With Unanticipated Postoperative Visits

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Belladonna and Opium (B&O) Suppository: 8.6% (3/35) versus 14.7% (5/34) on control; risk difference -6.1 percentage points (95% CI -21.2 to 9.0), risk ratio 0.58 (0.15–2.25); unadjusted two-proportion z-test p = 0.426.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belladonna and Opium (B&O) Suppository and the control. The interval gives the range of effects that remain compatible with the data.

Measurement of Post-operative Narcotic Use

• 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 (B&O) Suppository: mean 55.00 versus 65.00 on control; difference -10.00 (95% CI -46.59 to 26.59), standardized effect d = -0.13; z-test p = 0.592.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belladonna and Opium (B&O) Suppository and the control. The interval gives the range of effects that remain compatible with the data.

Across the posted secondary outcomes, the pattern is less clear than for the primary quality-of-life result. The unanticipated postoperative visit counts are numerically lower in the B&O group, and the mean postoperative narcotic use is also numerically lower in that group. However, the unadjusted comparisons for both outcomes are imprecise and do not provide strong statistical evidence of a group difference. The registry lists postoperative complications as a secondary outcome, but a numerical result for that outcome is not reported in the registry record.

These outcomes address related but distinct aspects of recovery. Unanticipated visits describe healthcare use, narcotic use describes medication consumption over the stated follow-up period, and complications describe adverse postoperative events. They are not interchangeable measures of the primary endpoint, which is a patient-reported global quality-of-life score on postoperative day 1. The secondary pattern therefore neither reproduces nor directly contradicts the primary result.

Unadjusted secondary results carry less weight when several outcomes are examined because the chance of obtaining at least one apparently unusual result can increase across multiple comparisons. A multiplicity adjustment or a prespecified hierarchy can address that concern, but neither is reported in the registry record. No reported analyses are listed for the secondary outcomes. The secondary findings are best treated as exploratory descriptions rather than as independent confirmation of the primary comparison.

The registry does not provide enough detail to determine whether these outcomes were prespecified, how their analyses were planned, or whether data were missing. It also does not report a clinical threshold for meaningful differences in these secondary measures. Their numerical direction can be described, but conclusions about the practical implications or robustness of those differences require information beyond the posted summaries.

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

• Number of Participants With Postoperative Complications as a Result of the Use of B&O Suppository
• Number of Participants With Unanticipated Postoperative Visits
• Measurement of Post-operative Narcotic Use

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a score that can take values across a scale rather than a count of events or a yes/no response. The registry reports a mean and standard deviation for each group. The mean locates the group’s average score; the standard deviation describes how dispersed individual scores are around that average. They answer different questions. Similar means can occur with different spreads, and the spread helps readers understand how much individual responses vary within each group.

What does the mean difference represent?

The reported mean difference compares the B&O group with the placebo group, in that order. Its value is -1.0, calculated as the B&O group mean relative to the placebo group mean. A negative value indicates a lower average score in the B&O group. For this endpoint, lower scores correspond to better quality of life, so the direction of the difference must be interpreted using the scale definition rather than the sign alone.

A mean difference is expressed in the original units of the outcome: in this case, points on the USSQ scale. It is not a percentage change, and it does not mean that every participant’s score changed by that amount. It summarizes a contrast between group averages. The reported comparison is unadjusted; adjustment for other variables is not reported in the registry record.

What does the confidence interval convey?

A confidence interval represents uncertainty around an estimated effect. In general, it describes a range of effect values that are compatible with the data under the method used to construct the interval. A narrower interval indicates greater precision than a wider interval, while an interval that includes no difference leaves a wider range of possible conclusions about direction. The primary outcome’s reported interval lies below zero, consistent with the reported direction of the mean difference.

The registry does not state the confidence level in the posted primary comparison. The confidence interval should therefore be interpreted as reported rather than assigned a level that is not recorded. A confidence interval is not a guarantee that the true effect falls within its bounds, and it does not establish clinical importance. The registry does not report a threshold for a clinically important difference on the score.

How should the p-value be understood?

The unadjusted p-value for the primary comparison is < 0.001. In general, a p-value describes how surprising data at least as incompatible with a specified no-difference model would be if that model and the statistical assumptions held. It is not the probability that the no-difference model is true, nor is it a measure of the size or practical importance of the effect. Here it is one part of the evidence alongside the group means, mean difference, and confidence interval.

The registry labels this p-value unadjusted. It does not report a multiplicity procedure or other adjustment for examining several outcomes. The p-value should not be interpreted as if such adjustment had been made. The record also does not report a detailed statistical analysis plan, the test used, assumptions checked, or any model beyond the posted comparison.

Why do spread and sample size matter?

In general, an estimate is more precise when the outcome is measured with less variability and when more observations contribute information. Standard deviations summarize variability in the posted groups, while the number of participants contributing to each reported outcome describes the available group data. These considerations help explain why a mean difference is read together with its interval rather than alone. They do not establish that the assumptions of a particular test were met.

The registry reports the primary outcome for 35 participants in the B&O group and 34 in the placebo group. It does not report whether these are all randomized participants, whether any participants were excluded from the analysis, or how missing outcome values were handled. The exact analysis population and missing-data method are not reported in the registry record. No conclusion about intention-to-treat analysis or complete-case analysis can be drawn from the posted counts alone.

The secondary outcomes use different statistical summaries. Unanticipated postoperative visits are counts of participants, while postoperative narcotic use is a continuous measure reported as a mean and standard deviation. General statistical interpretation differs by outcome type: an event count compares occurrence, whereas a continuous mean contrast compares average values. The posted secondary estimates are unadjusted, and no reported secondary analyses are listed in the registry record.

General statistical concepts help explain what the summaries can and cannot show, but they do not replace information about the trial’s methods. In particular, a randomized label does not reveal the randomization procedure, masking label does not specify masking roles, and a posted estimate does not reveal whether it was prespecified. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary mean difference is -1.0 points, with a reported confidence interval from -1.45 to -0.550. The interval is entirely below zero, so the range of values reported for the primary comparison points in the same direction as the observed difference. The reported unadjusted p-value is < 0.001. These are complementary summaries: the mean difference gives the estimated contrast, the interval describes its uncertainty, and the p-value summarizes evidence against a no-difference model under the analysis used.

Precision is not the same as importance. The interval indicates statistical uncertainty around the contrast, but the registry does not report what difference patients would consider important or a clinical threshold for the USSQ scale. Without that information, the result can be described as a difference in average scores, but its practical importance cannot be determined from the posted statistics alone.

The secondary comparisons are less conclusive. For unanticipated postoperative visits, the reported risk-difference interval extends across no difference and the unadjusted p-value is 0.426. For postoperative narcotic use, the mean-difference interval also includes values in both directions, with an unadjusted p-value of 0.592. The broad uncertainty in these secondary comparisons means that the data do not pinpoint a direction or magnitude as precisely as the primary outcome comparison.

The confidence level for the posted intervals is not reported in the registry record. The record also does not report the method used to construct each interval, missing-data handling, or adjusted analyses. Those details matter when assessing precision and should not be inferred from the interval endpoints alone.

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 illustrations based on the observed effect, not the trial’s original design assumptions. The registry’s stated calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is varied as a stated fraction of the observed effect. The figures for these outcomes are participants per arm, not total participants or total events. The trial’s own sample-size justification and original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the calculation model were correct. The 90% power column makes the analogous calculation for a 90% chance. These are planning concepts, not guarantees about the result of a future study. They do not say whether a finding is true or important.

The rows consider planning for 100%, 75%, and 50% of the observed effect. The smaller the effect a future study aims to detect, the more participants it generally needs, all else equal. That pattern is visible in the displayed planning figures. For the primary outcome, the estimate is based on the posted mean difference; the secondary outcome calculations similarly use the observed secondary effects. Such figures depend on the observed estimates, which can be uncertain, and they should not be treated as a definitive design recommendation.

This is not observed power. The figures are prospective planning illustrations generated from observed effects, not a measure of the probability that this completed trial detected a true effect.

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 = -1.000; pooled standard deviation σ = 0.944.
2. n = 2 × (1.96 + 0.842)² × 0.944² / -1.000² = 14.0, rounded up to 15 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                      # observed difference in means
sigma <- 0.944425909485473                     # 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(3332056)
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 = 15 (80% power), 19 (90% power)
 75% of observed effect: n per arm = 25 (80% power), 34 (90% power)
 50% of observed effect: n per arm = 57 (80% power), 75 (90% power)
power.t.test: 15 
Simulated power at n = 15 per arm: 0.793 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary outcome and several secondary outcomes. It gives an unadjusted p-value for the primary comparison and unadjusted p-values for the posted secondary comparisons. A procedure for controlling multiplicity, such as an adjustment across outcomes or a prespecified testing hierarchy, is not reported in the registry record. This matters because repeated statistical testing can make isolated small p-values less persuasive than a result assessed under a clearly defined analysis plan.

The record does not report the original statistical analysis plan, whether each endpoint was prespecified, or whether any outcomes were added or changed after the study began. It reports no analyses for the secondary outcomes beyond the posted summaries. The absence of that information means the results cannot be assessed against a documented plan for handling multiple outcomes or selective reporting.

Missing-data procedures and analysis populations are also not reported in the registry record. The posted participant counts show the numbers contributing to the reported outcomes, but do not establish whether all randomized participants were analyzed, whether anyone was excluded, or how missing responses were treated. There is no basis in the record to label the analysis intention-to-treat, per-protocol, or complete-case.

Interim analyses, stopping rules, and the trial’s original sample-size rationale are not reported in the registry record. Their absence from the record should be understood as unavailable information, not evidence that a particular procedure was or was not used. Together, these reporting gaps constrain assessment of the prespecification, multiplicity, and robustness of the posted statistical comparisons.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the B&O group among 35 participants at risk and zero in the placebo group among 34 participants at risk. It reports zero deaths in both groups. These are the serious-event figures recorded for the trial; they do not establish that no possible safety concern occurred or that the treatments have identical safety profiles.

The record also reports other adverse events affecting 3 participants in the B&O group and 5 participants in the placebo group. These counts are separate from the serious adverse event figures. The registry does not list serious adverse event terms, and it does not provide details such as event types, severity beyond the serious/other categorization, timing, or the investigators’ assessment of relatedness. The counts should therefore be read as a limited summary of reported events, not as a complete characterization of safety.

With the numbers of participants recorded in the trial arms, uncommon events may not be represented reliably. The posted figures describe what the registry reports during the study and do not determine risk in other settings or populations.

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

The posted primary result shows a lower average global quality-of-life score on postoperative day 1 in the B&O group than in the placebo group. On the USSQ scale, lower scores indicate better quality of life. The reported mean difference is -1.0, the confidence interval lies below zero, and the unadjusted p-value is < 0.001. This is evidence of a difference between the groups on that measured outcome in this trial.

The result does not establish the clinical importance of the score difference. The registry does not report a threshold for a meaningful difference on the scale, and a statistical comparison does not by itself determine what participants would regard as a worthwhile change. It also does not show that every participant experienced the same effect or that the average contrast applies to all patients undergoing ureteral stent placement.

The primary endpoint is a global quality-of-life score at one postoperative time point. It is not a complete measure of postoperative pain, symptoms, healthcare use, complications, or longer-term experience. The secondary results are less decisive, and the numerical result for the listed postoperative complications outcome is not reported in the registry record. The posted data therefore do not settle questions about the full range of postoperative outcomes.

The registry identifies the study as randomized and quadruple masked, but does not report the detailed procedures needed to evaluate randomization, masking roles, missing data, or analysis populations. The primary statistical result should be interpreted in light of those reporting limits. It is a description of the recorded trial comparison, not medical advice, a guarantee of an individual outcome, or proof of an effect in settings beyond the trial.

17. Why This Trial Matters Statistically

This trial is statistically useful because its primary outcome is a patient-reported score, while its secondary outcomes include healthcare visits and medication use. That contrast illustrates why a trial can show a clear difference on one outcome without producing equally clear findings on all related outcomes. Each endpoint represents a different aspect of postoperative experience, and the statistical summary must be interpreted in the context of what that endpoint measures.

The primary comparison also demonstrates the importance of scale direction. A negative mean difference would be unfavorable on some measures, but on this USSQ scale lower scores indicate better quality of life. Reading the sign together with the scale definition prevents a basic interpretive error. The group means, mean difference, uncertainty interval, and unadjusted p-value offer complementary information rather than interchangeable summaries.

The secondary outcomes illustrate the role of precision and multiplicity. Their estimates are less conclusive than the primary result, and multiple endpoints create a need for transparent prespecification and analysis plans. Such details are not reported in the registry record. The trial therefore highlights not only how posted numerical results can be read, but also why reporting of statistical methods, missing-data handling, and outcome hierarchy matters.

Finally, the planning illustrations show how sample-size needs change when the target effect is smaller, while also making clear that observed effects are uncertain inputs for planning. The registry does not report the trial’s original sample-size justification. Separating retrospective planning illustrations from the original design rationale is essential for sound statistical interpretation.

18. Limitations

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

The registry record leaves several trial-specific questions unanswered. Detailed eligibility criteria and participant characteristics are not reported, limiting assessment of how closely the enrolled population resembles other people undergoing ureteral stent placement. The precise randomization procedure, allocation concealment, and roles covered by quadruple masking are also not reported. Those details would help readers assess possible sources of bias.

The primary endpoint is measured at postoperative day 1, so the result is limited to that time point. The registry does not report a clinically important difference threshold for the USSQ score, questionnaire completion details, or how missing responses were handled. The posted participant counts do not explain whether all randomized participants contributed to each analysis or whether any exclusions occurred.

The statistical analysis plan, original sample-size justification, interim analyses, and multiplicity strategy are not reported in the registry record. This makes it difficult to judge whether the posted comparisons follow a prespecified plan. The secondary results are unadjusted, and a numerical result for postoperative complications is not reported. Safety reporting is also limited: event counts are available, but detailed event descriptions and relatedness assessments are not reported.

These limitations concern what can be assessed from the registry record; they do not establish that a particular method was absent or that an unreported procedure was performed incorrectly. They constrain interpretation of the posted results and the extent to which they can be generalized.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Use of Belladonna and Opium Suppository in the Treatment of Postoperative Stent Pain — NCT03332056.
• Registry record last updated 2023-06-18; status last verified 2023-05.
• Results first posted 2023-06-18.
• 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 phase 4, randomized, quadruple-masked, parallel-group study sponsored by the University of Washington. It enrolled 71 participants with nephrolithiasis undergoing ureteral stent placement. The comparison was a single preemptive B&O suppository versus placebo.

The primary outcome was global quality of life on postoperative day 1, measured with the USSQ on a scale where lower scores indicate better quality of life. The B&O group had a mean score of 4.4 and the placebo group 5.4; the reported mean difference was -1.0, with an unadjusted p-value of < 0.001. Secondary results were less conclusive. The registry also reports adverse event counts, but does not report a numerical result for the listed postoperative complications outcome.

Important details about the original statistical plan, missing data, analysis populations, and multiplicity are not reported in the registry record.