Does IV Ondansetron Prevent Pruritus After Intrathecal Morphine in Pediatric Patients?: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Does IV Ondansetron Prevent Pruritus After Intrathecal Morphine in Pediatric Patients? (NCT03262038), a randomized phase 4 study. The primary outcome is Incidence of Pruritus.

2. Clinical Question

The registry describes a prospective, randomized, double-blind, placebo-controlled study. Its broader stated aim included comparing the incidence and intensity of pruritus and nausea or vomiting, while the posted primary endpoint is the count of participants with any pruritus. These questions are related but not interchangeable: an incidence outcome records whether an event occurred, whereas an intensity outcome requires a measure of severity. The registry lists severity of postoperative nausea or vomiting as a secondary outcome, but does not list a pruritus severity result among the posted outcomes described in the record.

3. Trial Design

The registry record identifies NCT03262038 as a Phase 4, randomized, quadruple-masked, parallel-group trial sponsored by the University of Michigan. It lists an enrollment of 46 and a status of terminated. The start date is 2017-12-07, and the primary completion date is 2019-08-20. The record does not state why the trial was terminated.

The planned comparison was intravenous ondansetron versus placebo for children receiving intrathecal morphine. The ondansetron regimen was one intraoperative administration followed by scheduled administrations every 6 hours for 24 hours postoperatively. The placebo arm received a volume-matched placebo on the corresponding schedule. The brief summary describes the control approach as treating pruritus and postoperative nausea or vomiting with as-needed medications, in contrast to pre-emptive and scheduled ondansetron.

The primary posted outcome is the number of participants with any pruritus during 24 hours. Outcome data list 18 participants in the ondansetron arm and 27 in the placebo arm. The registry's enrollment figure and the arm counts displayed for this outcome are both retained as recorded; the record does not explain their relationship. The analyzed population, exclusions, and handling of missing outcome observations are not reported in the registry record.

The registry lists two secondary outcomes: incidence of postoperative nausea or vomiting and its severity, both with a 24-hour timeframe. It reports analyses for incidence outcomes, but does not provide numerical results for severity in the information described in the record. The original trial's statistical analysis plan, sample-size rationale, interim-analysis plan, and details of the masking procedures are not reported in the registry record. The term quadruple-masked is recorded, but the record does not specify which roles were masked.

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 Incidence of Pruritus, measured over 24 hours.

The primary endpoint is incidence of pruritus over 24 hours, expressed as the number of participants who experienced any pruritus. It is a binary, participant-level outcome: each participant is classified according to whether pruritus occurred during the stated period. The posted counts are 14 participants in the ondansetron arm and 24 in the placebo arm.

This endpoint is useful because it directly describes how commonly the event occurred in each group during the observation window. A count of participants with any event is easier to interpret than a measure of episode frequency when the clinical question is whether pruritus occurred at all. It also keeps the unit of analysis as participants rather than episodes, which avoids treating repeated events in one person as though they came from different people.

Incidence does not capture how severe the itching was, how long it lasted, when it began, or how many episodes occurred. A participant with one mild episode and a participant with persistent severe symptoms both contribute one event to this endpoint. The registry's stated study aim mentions intensity, but the posted primary measure is incidence. The recorded timeframe is 24 hours; results outside that period are not represented by this measure. The record does not report further operational details about how pruritus was assessed or how an event was defined.

7. Results Posted in the Registry

• Ondansetron IV: 77.8% (14/18) versus 88.9% (24/27) on control; risk difference -11.1 percentage points (95% CI -33.7 to 11.5), risk ratio 0.88 (0.66–1.16); unadjusted two-proportion z-test p = 0.314.

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.

Incidence of Post Operative Nausea or Vomiting

• 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:
  • Ondansetron IV: 44.4% (8/18) versus 85.2% (23/27) on control; risk difference -40.7 percentage points (95% CI -67.3 to -14.2), risk ratio 0.52 (0.30–0.90); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Ondansetron IV than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists incidence and severity of postoperative nausea or vomiting as secondary outcomes, each with a 24-hour timeframe. The posted incidence comparison has a different pattern from the primary pruritus comparison: the recalculated result is statistically more distinct from the null, and the registry-reported analysis also gives a smaller p-value than its primary analysis. The incidence result is therefore a notable secondary signal in the posted outcomes, while the primary pruritus comparison remains imprecise. These outcomes concern different events and should not be treated as interchangeable evidence about the primary endpoint.

The registry also lists severity of postoperative nausea or vomiting, but numerical severity results are not reported in the registry record. The record does not describe the severity scale or its analysis. Thus, the overall secondary-outcome pattern cannot be extended to a conclusion about symptom intensity from the incidence results alone.

Secondary outcomes are generally interpreted with more caution than a prespecified primary outcome. When several outcomes are tested, the chance of obtaining at least one apparently notable result can increase unless the analysis plan addresses multiplicity. The registry record does not report a multiplicity adjustment or a hierarchical testing strategy. The unadjusted secondary p-value should therefore not be treated as having the same confirmatory weight as a result from a prespecified primary analysis with an appropriate multiplicity plan. The record does not establish whether these secondary analyses were prespecified.

The secondary incidence finding can be described as an observed group difference in the posted data, but it does not remove uncertainty about the primary result or answer the missing severity question. It also does not establish that the same pattern would recur in another study. The counts, effect estimate, interval, and registry-reported test result for each endpoint remain the appropriate basis for endpoint-specific interpretation; the broader pattern should be read as exploratory unless a prespecified analysis plan says otherwise, and that plan is not reported in the registry record.

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

• Incidence of Post Operative Nausea or Vomiting
• Severity of Post Operative Nausea or Vomiting

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint, each participant is classified as having or not having the event during the specified timeframe. Here, the event is any pruritus within 24 hours. The arm counts describe how many participants were recorded with that event, and the arm sizes describe the participants represented in the outcome results. This kind of endpoint is often summarized as a risk, meaning the proportion of participants in a group who experienced the event. The posted group risks are 0.778 for ondansetron and 0.889 for placebo.

What does a risk difference describe?

The risk difference subtracts the comparator group's risk from the intervention group's risk. Its scale is an absolute difference in proportions. The recalculated estimate is -0.111, so its direction indicates a lower observed risk in the ondansetron group. A value of zero would represent equal observed risks. The estimate is unadjusted: it compares the posted group summaries without adjustment for other variables. The registry record does not report an adjusted primary analysis.

Absolute differences are often straightforward to interpret because they state how far apart the group risks are on the risk scale. However, a point estimate alone does not show how uncertain the estimate is. The confidence interval is needed to describe the range of values compatible with the data under the interval procedure. For the primary risk difference, the interval runs from -0.337 to 0.115, including zero.

How do risk ratios and odds ratios differ?

A risk ratio divides one group's risk by the other's. A ratio of 1 represents equal risks; a value below 1 indicates a lower observed risk in the numerator group, and a value above 1 indicates a higher observed risk. The posted primary risk ratio is 0.875. Its 95% confidence interval, 0.661 to 1.158, includes 1.

An odds ratio compares odds rather than risks. Odds are the event probability divided by the probability of no event. A value of 1 represents equal odds. The primary odds ratio is 0.438, with a 95% confidence interval from 0.085 to 2.246. The interval includes 1 and is wide. When events are common, odds and risks are not close substitutes; an odds ratio can look more extreme than a risk ratio. For that reason, the odds ratio should not be described as a percentage reduction in risk.

What does the p-value test?

A p-value measures how unusual results at least as discrepant as those observed would be under a particular null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it is not the probability that the result occurred by chance. The recalculated unadjusted p-value for pruritus is 0.314. The registry's reported chi-squared p-value is .412. The registry identifies the latter method as chi-squared but does not report additional test details. The record does not say that these analyses were adjusted for other variables.

Statistical significance is often assessed using a threshold chosen before analysis, but crossing or not crossing a threshold does not resolve the magnitude, importance, or precision of an effect. The primary confidence interval includes both a possible reduction and a possible increase in the risk difference. Consequently, the non-significant p-values should not be interpreted as proof of no effect. Nor should the negative point estimate by itself be treated as conclusive evidence of a difference.

Why do the methods and analysis populations matter?

Random allocation is intended to make assigned groups comparable on average, including with respect to characteristics not measured by investigators. In a small trial, chance imbalances can remain, and randomization does not guarantee that every analysis preserves the benefits of allocation. The registry calls the study randomized but does not report sequence generation, allocation concealment, analysis population, or exclusions. It therefore is not possible to determine from this record whether the posted outcome counts follow an intention-to-treat approach or another analysis population.

Missing outcomes can affect a binary comparison if participants with unknown event status are excluded or classified using an assumption. The record does not report missingness or its handling. It also does not report whether the primary analysis used a prespecified statistical plan, whether there were interim analyses, or how the trial's sample size was justified. Those details should not be inferred from the recalculated summaries.

What is the role of the recalculation?

The recalculated values are simple, unadjusted comparisons based on the posted group summaries. They make the direction and uncertainty of the contrast easier to read, but they do not replace the sponsor's own analysis. The registry's primary analysis is reported as a chi-squared test with p = .412, while the recalculated p-value is 0.314. The record does not explain the difference. As the discrepancy indicator is false, the data do not trigger the stated rule that the sponsor's own analysis takes precedence because of a flagged discrepancy. Both results should be kept distinct, with the registry's reported result recognized as the sponsor-reported analysis.

11. Confidence Intervals and Precision

The primary risk-difference estimate is -0.111, and its 95% confidence interval extends from -0.337 to 0.115. The interval includes zero, the value corresponding to no difference on the risk-difference scale. It also includes values in both directions, so the data are compatible with a lower observed risk under ondansetron as well as a higher observed risk under ondansetron. The interval is broad relative to the point estimate, indicating substantial uncertainty about the size and direction of the group difference.

Confidence intervals describe the uncertainty of an estimate under the method used to calculate them. In repeated use, a 95% confidence-interval procedure would contain the true parameter in 95% of intervals if its assumptions held. This is not a statement that there is a 95% probability that the true effect lies inside this particular interval. The registry does not provide a confidence interval for its reported chi-squared analysis.

The relative estimates give a similar caution. The risk ratio is 0.875, with a 95% confidence interval from 0.661 to 1.158; the odds ratio is 0.438, with a 95% confidence interval from 0.085 to 2.246. Each interval includes its no-association value. The odds-ratio interval is especially broad, and its scale should not be confused with the risk scale.

Precision is limited by the amount of outcome information in the posted comparison. The arm counts are modest, and the interval remains compatible with effects in either direction. A wide interval does not mean that every value within it is equally likely, nor does it make the point estimate meaningless. It means that the observed data leave considerable uncertainty about the true contrast. Interpretation should therefore give the interval and observed counts at least as much attention as the p-value.

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 total events. They illustrate how large a future two-arm comparison might need to be under stated assumptions and under different fractions of the observed effect. The registry record does not report the original trial's sample-size justification or design assumptions; the planning assumptions are for the separate illustration, not a reconstruction of the trial's original plan.

The illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, and 50% of that observed effect. The columns for 80% and 90% power describe the number of participants per arm associated with those target probabilities of detecting the specified effect under the assumed model, if that effect were true and the design assumptions held. Power is a design property calculated under assumptions; it is not a guarantee that a study will detect an effect.

The figures are not observed power for this trial. Observed power is not a useful substitute for interpreting the estimate and its confidence interval; the posted interval directly displays the uncertainty in the primary comparison. The planning illustration is also not evidence that the trial was designed to those targets. Its assumptions and effect sizes are separate from the unreported original design rationale.

Smaller effects generally require more participants to distinguish them from no difference with the same target power and significance level. Accordingly, planning for a smaller fraction of the observed effect requires larger per-arm sample sizes than planning for the full observed effect. The curve should be read as showing this relationship across assumed effect sizes, not as a prediction of the outcome of a future trial.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.889; treatment proportion p₁ = 0.778; average p̄ = 0.833.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5270 = 1.0330.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5212 = 0.4386.
4. n = (1.0330 + 0.4386)² / (-0.1111)² = 175.4, rounded up to 176 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
p0 <- 0.888888888888889                          # control proportion
p1 <- 0.777777777777778                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3262038)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 176 (80% power), 235 (90% power)
 75% of observed effect: n per arm = 292 (80% power), 390 (90% power)
 50% of observed effect: n per arm = 608 (80% power), 813 (90% power)
power.prop.test: 175.4 
Simulated power at n = 176 per arm: 0.806 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 reports the sponsor's primary comparison as a chi-squared analysis with p = .412. It does not supply an effect estimate or confidence interval alongside that reported test. The unadjusted recalculation based on the posted counts gives a risk difference of -0.111, a 95% confidence interval from -0.337 to 0.115, and p = 0.314. These are different summaries of the same posted group comparison, and the record does not explain why the two p-values differ.

The discrepancy indicator is false. The stated precedence rule for a flagged discrepancy therefore does not apply. The recalculated comparison should be treated as a supplementary, unadjusted reading of the posted summaries, not as a replacement for the registry's own analysis. The registry's reported chi-squared result remains the sponsor-reported result, while the recalculated estimate and interval add information about direction and precision that the reported p-value alone does not provide.

Neither p-value establishes that the groups are equivalent or that the true difference is zero. Both are above 0.05, and the recalculated confidence interval includes zero while allowing values in either direction. The record does not report further analytic details that would resolve the difference between the test results, such as the exact test implementation or the prespecified analysis plan. No explanation for that difference should be inferred from the registry entry.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary endpoint and secondary outcomes concerning postoperative nausea or vomiting. Testing multiple outcomes creates a multiplicity issue: if each is assessed separately, the chance of at least one apparently positive result can rise. A prespecified strategy might control the overall error rate, prioritize outcomes in an order, or identify secondary analyses as exploratory. The registry record does not report a multiplicity adjustment, a testing hierarchy, or whether the secondary outcomes were prespecified. The secondary p-values should therefore be interpreted cautiously and not as independent confirmation of the primary finding.

The record reports the primary analysis as chi-squared and gives the sponsor-reported p-value, but it does not describe the complete statistical analysis plan. Interim analyses, stopping rules, covariate adjustment, and the original sample-size justification are not reported in the registry record. The terminated status is recorded, but the reason for termination is not reported. Termination alone does not establish that the decision was based on efficacy, safety, recruitment, or any other particular factor.

Missing-data handling and the analysis population are also not reported in the registry record. The outcome counts are listed for the two arms, but the record does not state whether all randomized participants were included, whether any participants lacked outcome assessment, or how such observations were treated. Without this information, it is not possible to assess whether missingness could have affected the group comparison or whether the analysis followed an intention-to-treat principle.

The record gives enrollment of 46 and outcome-arm counts of 18 and 27. It does not explain how the enrollment figure relates to the outcome counts. The figures should be read as separate registry entries rather than reconciled through an assumption about exclusions or missing participants. These omissions do not invalidate the posted counts, but they limit evaluation of the analysis pathway and how closely it followed the trial's intended design.

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 5% reporting threshold.

The serious-adverse-event entries list 0 serious adverse events among 18 participants at risk in the ondansetron arm and 0 among 27 participants at risk in the placebo arm. Deaths are listed as 0 in both groups. The registry also lists 0 other adverse events in each arm, among the same arm-specific numbers reported at risk.

These entries describe what was recorded in the registry for the stated groups; they do not show that no adverse events of any kind occurred outside the categories or reporting process captured in these fields. Zero recorded events in a relatively small trial cannot establish that an event is impossible or exclude uncommon harms. The registry does not provide details about adverse-event definitions, collection procedures, severity grading, or the duration of safety follow-up beyond the entries shown. It also does not list serious adverse-event terms.

The safety figures should be considered alongside the limited size and terminated status of the study, without inferring a reason for termination. They are descriptive counts, not a statistical demonstration that the treatments have identical safety profiles. The record does not report a comparative safety analysis or confidence intervals for adverse events.

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

The posted primary data show that pruritus was recorded in both groups during the 24-hour assessment period. The observed risk was lower in the ondansetron group, and the recalculated risk difference was negative. However, the confidence interval is broad and includes zero, while the registry-reported primary test and the unadjusted recalculated test are both non-significant at the commonly used 0.05 threshold. The results are therefore uncertain about the size and direction of the underlying group difference.

This does not mean that the treatments are equivalent, that there is no possible effect, or that the point estimate is a reliable measure of the true difference. Demonstrating equivalence or non-inferiority requires a prespecified margin and an appropriate design and analysis; these are not reported in the registry record. A non-significant test is not an equivalence test.

The data also do not establish what would happen in a broader pediatric population, in different clinical settings, or over a different observation period. The record describes the population as children receiving intrathecal morphine and specifies a 24-hour primary timeframe. It does not provide additional eligibility details or a complete account of the analysis population. The primary outcome captures whether any pruritus occurred, not its duration, severity, recurrence, or effect on the participant.

The secondary incidence result for postoperative nausea or vomiting has a different statistical pattern, but it is a separate outcome and is subject to the limitations of secondary, potentially multiple testing. The registry does not report numerical severity results. Safety entries list no serious events, deaths, or other adverse events in the recorded fields, but those counts cannot exclude uncommon events or establish identical safety profiles.

Overall, the registry supports a cautious description of the observed counts and their uncertainty. It does not support a definitive claim that ondansetron prevents pruritus, nor does it establish that it has no effect. The missing details about termination, missing data, analysis populations, and the original analysis plan further constrain how confidently the posted comparison can be generalized or interpreted as confirmatory evidence.

18. Why This Trial Matters Statistically

This trial illustrates why a binary endpoint should be read through both its group counts and an effect estimate with an uncertainty interval. The risk difference communicates an absolute contrast, while the risk ratio and odds ratio describe relative contrasts on different scales. These measures can tell complementary stories, particularly when the event is common. Reporting only a p-value would conceal the direction and range of effect sizes compatible with the data.

It also demonstrates that statistical significance and precision are not the same thing. The primary p-values do not cross the commonly used threshold, but that fact alone does not establish no difference. The confidence interval makes the uncertainty more visible by including values on either side of no difference. The trial is therefore a useful example of why an estimate, interval, and clinical context should be considered together.

The registry-reported chi-squared result and the unadjusted recalculation are not identical. Keeping them separate is important: a recalculated summary can aid interpretation but cannot replace the sponsor's analysis or explain undocumented analytic choices. The secondary outcome pattern further illustrates why endpoint hierarchy and multiplicity matter. A notable secondary result may warrant attention, but its evidential weight depends on prespecification and the testing strategy, details not reported in the registry record.

Finally, the record's terminated status and the difference between its enrollment entry and outcome-arm counts underscore the value of transparent reporting about participant flow, missing data, and analysis populations. Without those details, even straightforward comparisons can be difficult to connect to the original trial plan. The statistical lesson is not to overstate either a favorable-looking point estimate or a non-significant test, but to describe what was observed and what remains uncertain.

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 specific to this trial constrain interpretation. The registry lists enrollment of 46, while the primary outcome counts are reported for 18 participants in the ondansetron arm and 27 in the placebo arm. The record does not explain how these figures relate, so participant flow and the analysis denominator cannot be reconstructed from the entry alone. The reason for the terminated status is also not reported, and it should not be inferred from the outcome results.

The primary comparison is based on a binary event over 24 hours. It does not capture the severity, duration, or recurrence of pruritus. Although the study summary refers to incidence and intensity, the primary endpoint is incidence, and the record does not report a numerical pruritus-severity result. The registry also does not describe how pruritus was assessed or define the threshold for recording an event.

The primary confidence interval is broad and includes values in either direction. This limits precision and makes the point estimate an uncertain guide to the underlying difference. The registry-reported chi-squared p-value differs from the unadjusted recalculated p-value, and the record does not explain that difference or provide a full analysis plan. It does not report whether adjustment for covariates was used, how missing data were handled, or which analysis population was used.

Additional limits include the absence of reported multiplicity procedures for the secondary outcomes and the lack of numerical results for the listed severity outcome. The original sample-size justification, interim-analysis plan, masking details, and termination rationale are not reported in the registry record. The serious and other adverse-event entries are zero in both arms, but the record provides limited information about event definitions and ascertainment. These limitations call for a measured interpretation of both efficacy-related outcomes and safety reporting.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Does IV Ondansetron Prevent Pruritus After Intrathecal Morphine in Pediatric Patients? — NCT03262038.
• Registry record last updated 2021-01-19; status last verified 2020-08.
• Results first posted 2021-01-19.
• 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

NCT03262038 is a Phase 4 randomized, quadruple-masked, parallel-group, placebo-controlled trial sponsored by the University of Michigan. The registry lists enrollment of 46 and status as terminated. The study compared scheduled intravenous ondansetron with volume-matched placebo in children receiving intrathecal morphine.

The primary endpoint was the number of participants with any pruritus during 24 hours. The posted outcome counts were 14 of 18 in the ondansetron arm and 24 of 27 in the placebo arm. The recalculated risk difference was -0.111, with a 95% confidence interval from -0.337 to 0.115; the registry-reported chi-squared p-value was .412. The interval includes zero and allows differences in either direction.

The registry lists incidence and severity of postoperative nausea or vomiting as secondary outcomes. It reports a secondary incidence analysis, but numerical severity results are not reported in the registry record. The reason for termination, participant flow, missing-data handling, analysis population, original sample-size rationale, and full statistical analysis plan are not reported.