Safety and Efficacy of Palonosetron IV to Prevent Postoperative Nausea and Vomiting in Pediatric Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Palonosetron IV to Prevent Postoperative Nausea and Vomiting in Pediatric Patients (NCT01395901), a randomized phase 3 study. The primary outcome is Proportion of Patients With Complete Response.

2. Clinical Question

T0 was the time when a patient woke up and was able to show any active reaction after surgery. The registry describes the study as evaluating efficacy through 24 hours and safety and tolerability in pediatric patients. The practical statistical question is about the observed proportions and the uncertainty around their between-group contrast. It is not simply a comparison of whether either group had a high response rate: the randomized comparison is the relevant contrast, and its precision matters when interpreting the observed difference.

3. Trial Design

The study was a phase 3, multicenter, randomized, parallel-group trial. Its official title describes a double-blind, double-dummy, stratified design, while the registry classifies masking as quadruple. The double-dummy approach paired each active drug with a matching placebo: palonosetron with placebo to ondansetron, or ondansetron with placebo to palonosetron. This design allows the comparison to use two intravenous treatments while maintaining the stated masking approach.

The registry reports enrollment of 670. The primary-outcome groups have 331 patients assigned to palonosetron and placebo to ondansetron and 330 assigned to ondansetron and placebo to palonosetron. The endpoint description identifies the analysis population as the Full Analysis Set, which included randomized patients who received the active study drug, general anesthesia, and surgery. In keeping with the stated intent-to-treat principle, patients were assigned to their randomized treatment arm.

The study began in 2011-06, reached primary completion in 2012-03, and is listed as completed. The sponsor was Helsinn Healthcare SA. The record does not report the original sample-size justification, the stratification factors, or the details of sequence generation and allocation concealment. The planned treatment period relevant to the primary endpoint was the first 24 hours after T0; the full follow-up schedule is not reported in the registry record.

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:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) included all randomized patients who received the active study drug, general anesthesia and surgery (evaluable patients). Following the intent-to-treat principle, patients were assigned to the study treatment arm according to their randomized treatment.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Full Analysis Set Population

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Patients With Complete Response, measured over 0-24 hours after T0.

The primary endpoint was the proportion of patients with a complete response during 0-24 hours after T0. A complete response was defined as having no vomiting, no retching, and no use of antiemetic rescue medication during that period. T0 marked the point when the patient woke and could show any active reaction after surgery. The result is therefore a binary outcome: each patient either met the complete-response definition or did not.

This composite definition captures more than vomiting alone. It combines vomiting, retching, and rescue-medication use into one patient-level measure, so a patient must meet all parts of the definition to count as a complete response. That makes the endpoint a way to summarize several clinically relevant postoperative events in a single proportion. The separate secondary outcomes report components or related measures, including no vomiting, no emetic episodes, no rescue medication, and no nausea for patients older than 6 years.

For a binary endpoint, the group proportion communicates how often the defined outcome occurred, while a between-group risk difference estimates the absolute contrast in those proportions. Confidence intervals describe the precision of that contrast. The endpoint is useful for a randomized comparison because it can be assessed in each treatment group over the same stated period. The registry does not report details such as adjudication procedures or how endpoint data were collected when a patient could not provide a response.

7. Results Posted in the Registry

• Ondansetron and Placebo to Palonosetron: 82.7% (273/330) versus 78.2% (259/331) on control; risk difference 4.5 percentage points (95% CI -1.6 to 10.5), risk ratio 1.06 (0.98–1.14); unadjusted two-proportion z-test p = 0.146.

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.

Proportion of Patients With no Vomiting

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ondansetron and Placebo to Palonosetron: 87.6% (289/330) versus 83.1% (275/331) on control; risk difference 4.5 percentage points (95% CI -0.9 to 9.9), risk ratio 1.05 (0.99–1.12); unadjusted two-proportion z-test p = 0.103.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ondansetron and Placebo to Palonosetron and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Patients Without Emetic Episodes

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ondansetron and Placebo to Palonosetron: 83.9% (277/330) versus 80.1% (265/331) on control; risk difference 3.9 percentage points (95% CI -2.0 to 9.7), risk ratio 1.05 (0.98–1.13); unadjusted two-proportion z-test p = 0.194.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ondansetron and Placebo to Palonosetron and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Patients Without Antiemetic Rescue Medication

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ondansetron and Placebo to Palonosetron: 96.4% (318/330) versus 93.1% (308/331) on control; risk difference 3.3 percentage points (95% CI -0.1 to 6.7), risk ratio 1.04 (1.00–1.07); unadjusted two-proportion z-test p = 0.057.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ondansetron and Placebo to Palonosetron and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the descriptive pattern generally favors a higher proportion in the ondansetron group for absence of vomiting, absence of emetic episodes, and absence of antiemetic rescue medication. These outcomes overlap conceptually with the primary complete-response definition, but each captures a different component or aspect of the postoperative experience. The primary endpoint requires meeting all of its component criteria, whereas each secondary measure focuses on a more specific outcome.

This pattern is broadly consistent with the primary group proportions, in which the ondansetron group had a higher complete-response percentage. It does not independently confirm the primary finding: related outcomes can share events and participants, and therefore do not constitute wholly separate replications. The secondary endpoint of no nausea was listed for patients older than 6 years, but no result for it appears among the posted secondary outcomes. Its numerical result is not reported in the registry record.

The simple unadjusted comparisons for the secondary outcomes are not reported by the registry as formal analyses. A set of unadjusted comparisons raises a multiplicity issue: the more outcomes examined, the greater the opportunity for chance patterns to appear. The registry does not report a multiplicity adjustment or identify a prespecified hierarchy among the secondary outcomes. Consequently, the secondary results carry less confirmatory weight than the primary endpoint and should be interpreted as supportive descriptions rather than as stand-alone proof of a treatment difference.

Differences in endpoint definitions also matter. No vomiting is not the same as no emetic episodes, and neither measure includes all parts of the complete-response definition. No rescue medication records a treatment-use outcome, not a direct measure of vomiting alone. Reading the family of outcomes together helps describe the pattern, but it does not erase those distinctions or the uncertainty around each estimate.

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

• Proportion of Patients With no Vomiting
• Proportion of Patients Without Emetic Episodes
• Proportion of Patients Without Antiemetic Rescue Medication
• Proportion of Patients Without Nausea (Patient Aged > 6 Years)

9. Statistical Interpretation

10. Statistical Methods Explained

A binary outcome records whether each participant did or did not meet a defined condition. Here, complete response required no vomiting, no retching, and no antiemetic rescue medication during 0-24 hours after T0. The group percentage is the number meeting that definition expressed as a proportion of the analyzed group. It gives an interpretable summary, but the comparison between groups is usually more informative than either percentage alone in a randomized trial.

What does a risk difference express?

A risk difference subtracts one group's event proportion from the other's. Its sign depends on the order of subtraction, so a positive or negative value has meaning only when the group order is clear. The simple recalculation uses ondansetron compared with palonosetron; its estimated risk difference is 0.045. The registry's reported risk difference is -4.4 and lists the groups in palonosetron-then-ondansetron order. The registry does not report the method used for that analysis, so the official result should be read using its own reported direction and scale rather than treating the two presentations as identical outputs.

What does a confidence interval tell us?

A confidence interval represents uncertainty around an estimate under the statistical procedure used to construct it. A narrower interval indicates greater precision; a wider interval indicates that a broader range of values remains compatible with the observed data and method. For the recalculated primary risk difference, the 95% confidence interval is -0.015 to 0.105. Because zero lies within that interval, it does not exclude no difference. This does not prove the groups are the same: values on either side of zero remain compatible with the interval. The registry's reported interval is -10.5 to 1.7 for its risk difference of -4.4.

Why can the reported and recalculated results differ in presentation?

The registry reports a formal analysis classified as non-inferiority or equivalence. The recalculation is an unadjusted re-analysis based on the posted summary proportions and counts. A formal analysis may use a particular prespecified estimand, analysis population, model, or adjustment; the details of the sponsor's method are not reported in the registry record. The recalculation should therefore be understood as a transparent summary-statistic comparison, not a replacement for the trial's formal analysis. The registry does not report a non-inferiority margin, so the posted estimate and interval alone do not permit an independent assessment against such a margin.

Why does the analysis population matter?

The primary endpoint population is described as the Full Analysis Set. It included randomized patients who received the active study drug, general anesthesia, and surgery, and patients were analyzed according to randomized treatment. This connects the analysis to randomization while also setting eligibility conditions for inclusion. The registry does not report a separate per-protocol analysis or the number of randomized patients excluded from the Full Analysis Set. Those details would help readers assess how closely the analyzed population retained the randomized comparison.

Why can over-dispersion matter in other outcome types?

General statistical context: over-dispersion occurs when variation in observed data is greater than a model assumes. It can make standard errors too small if the model does not account for that extra variation. The primary outcome is a binary patient-level proportion, and the registry does not report a model or over-dispersion assessment. The main interpretation therefore rests on the posted proportions, risk difference, and confidence intervals rather than on an assumption that a particular over-dispersed model was used.

The registry lists one analysis for the primary measure and no analyses for the posted secondary measures. It does not report the statistical analysis plan, missing-data procedures, interim analyses, or adjustments for multiple outcomes. Those omissions limit how much can be inferred about prespecification and the intended handling of uncertainty beyond the reported estimates.

11. Confidence Intervals and Precision

The primary group estimates are 78.2% with a 95% confidence interval of 73.3% to 82.5% for palonosetron, and 82.7% with a 95% confidence interval of 78.1% to 86.6% for ondansetron. These intervals describe uncertainty around each group's proportion. They are not a direct interval for the difference between groups; the risk-difference interval is the relevant interval for that contrast.

The simple unadjusted recalculation estimates a risk difference of 0.045, with a 95% confidence interval from -0.015 to 0.105. The interval includes zero and extends to values on both sides of it. Thus, the observed contrast is not estimated with enough precision to rule out no difference using that interval. The width also indicates that a range of contrasts remains plausible under the recalculation's assumptions. A confidence interval is not a guarantee that the true value lies within its limits, nor does it assign a probability to a particular treatment effect after observing the data.

The registry's formal result reports a risk difference of -4.4 and a 95% confidence interval from -10.5 to 1.7. Because the registry's analysis method and non-inferiority or equivalence margin are not reported, this interval cannot be assessed against a stated margin from the registry record alone. The sponsor result and the recalculation use different reported presentations and should be distinguished rather than combined.

Confidence intervals for the secondary outcomes likewise convey uncertainty around their individual estimates. Looking across several outcomes makes the overall evidence less straightforward than a single interval, particularly when no multiplicity procedure is reported. The intervals are most useful when read alongside the outcome definitions, group sizes, comparison direction, and analysis population, not as isolated indicators of certainty.

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 sample-size figures are planning illustrations based on the observed effect, not the trial's own original design calculation. For these binary outcomes, the figures are participants per arm, rather than a total number of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each illustration is the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column means the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those planning assumptions, if that effect is the true one. The 90% power column uses a higher chance of detecting that same specified effect, so it generally calls for a larger planned sample. These are prospective design calculations, not evidence about what the completed trial was capable of detecting after its results were observed.

Rows that plan for a smaller fraction of the observed effect require more participants per arm, because smaller differences are harder to distinguish from random variation. The sample-size curve expresses the same general relationship between assumed effect size and required enrollment: planning to detect subtler effects calls for more participants. The effect fractions are planning choices, not claims about the true effect. These figures are not observed power.

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 = 0.782; treatment proportion p₁ = 0.827; average p̄ = 0.805.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5604 = 1.0985.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5596 = 0.4709.
4. n = (1.0985 + 0.4709)² / (0.0448)² = 1,227.4, rounded up to 1,228 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 <- 0.782477341389728                          # control proportion
p1 <- 0.827272727272727                          # 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(1395901)
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 = 1,228 (80% power), 1,643 (90% power)
 75% of observed effect: n per arm = 2,231 (80% power), 2,985 (90% power)
 50% of observed effect: n per arm = 5,123 (80% power), 6,858 (90% power)
power.prop.test: 1227.4 
Simulated power at n = 1,228 per arm: 0.802 (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 a formal sponsor analysis for the primary outcome: risk difference -4.4, with a 95% confidence interval from -10.5 to 1.7, classified as a non-inferiority or equivalence analysis. No p-value, analysis method, or non-inferiority margin is reported in the registry record. The formal result should therefore be read as the sponsor analysis recorded for the trial, while recognizing that the information needed to evaluate its non-inferiority or equivalence criterion is incomplete.

The simple recalculation uses the posted group summaries and reports the comparison in the opposite direction, from ondansetron relative to palonosetron: risk difference 0.045, with a 95% confidence interval from -0.015 to 0.105 and an unadjusted p-value of 0.146. These values are not a substitute for the sponsor's analysis. The comparison direction and reporting scale differ, and the registry does not provide enough methodological detail to establish that the two analyses use the same estimand or procedure.

The recalculation is useful as an independent, unadjusted description of the proportions and their contrast. It should not be treated as a correction to the formal result. The registry does not state a discrepancy between the posted and sponsor results; both should be presented with their distinct purposes and limitations.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and four secondary outcomes. The primary outcome is complete response during 0-24 hours after T0. Secondary outcomes include no vomiting, no emetic episodes, no antiemetic rescue medication, and no nausea for patients older than 6 years. The registry reports one analysis for the primary endpoint; it does not list formal analyses for the secondary outcomes. The statistical analysis plan and any prespecified hierarchy among outcomes are not reported in the registry record.

Multiplicity arises when several outcomes or comparisons are examined. Even if each comparison is considered separately, a collection of tests can increase the chance of seeing an apparently notable result by chance. Adjustments or a prespecified testing order can address this issue, but the registry does not report whether any such approach was used. The secondary comparisons should therefore be interpreted cautiously and should not be treated as equivalent to a single prespecified primary test.

The record describes the Full Analysis Set and says patients were assigned according to randomized treatment. It does not provide a detailed account of missing endpoint data, exclusions after randomization, imputation, or sensitivity analyses. The number of randomized participants excluded from the Full Analysis Set and the reasons for any exclusions are not reported in the registry record. Without that information, the effect of missing data or population exclusions on the estimates cannot be assessed from this record.

The registry also does not report interim analyses, stopping rules, or the original sample-size calculation. These omissions do not show that such procedures were absent; they mean their use and details cannot be determined from the registry record. The formal analysis is labeled non-inferiority or equivalence, but its margin and method are not stated. Those elements are necessary context for understanding what claim the formal analysis was designed to evaluate.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: post procedural haemorrhage (1.5%), dehydration (0.6%), ureteric anastomosis complication (0.3%), wound haemorrhage (0.3%), vomiting (0.3%).

The registry reports serious adverse events in 4 of 331 patients in the palonosetron group and 11 of 330 patients in the ondansetron group. Other adverse events are recorded for 234 of 331 and 225 of 330 patients, respectively. These are counts in each treatment group; they are not, by themselves, adjusted comparisons or evidence that an observed difference was caused by treatment. Deaths are not reported in the registry record.

The listed serious adverse event terms include post procedural haemorrhage at 1.5%, dehydration at 0.6%, ureteric anastomosis complication at 0.3%, wound haemorrhage at 0.3%, vomiting at 0.3%, and nausea at 0.3%. The record does not give additional detail about event timing, seriousness criteria, relatedness assessments, or the distribution of each listed term between treatment groups. These figures should be read as recorded safety information, not as a complete account of comparative safety.

Safety counts and efficacy proportions address different questions. The efficacy endpoint concerns complete response during a defined postoperative period; adverse-event counts describe events recorded for safety. A balanced interpretation keeps those outcomes separate and acknowledges that the registry's available safety detail is limited.

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

The results describe complete response after surgery among children in the trial's Full Analysis Set. The reported proportions were 78.2% for palonosetron and 82.7% for ondansetron. The formal registry analysis gives a risk difference of -4.4 with a 95% confidence interval from -10.5 to 1.7; the unadjusted recalculation, using the opposite comparison direction, gives a risk difference of 0.045 with a 95% confidence interval from -0.015 to 0.105. These results communicate the observed group pattern and the uncertainty around the between-group contrast.

The intervals include zero, so the estimates do not rule out no difference. That does not demonstrate that the treatments are equivalent. Equivalence or non-inferiority requires a prespecified margin and an analysis that evaluates the estimate against that margin. Although the registry labels the reported analysis as non-inferiority or equivalence, the margin and method are not reported in the registry record. The posted information is therefore insufficient to independently assess that criterion.

The results do not establish that either treatment is better or worse, and they do not show what would happen for every child or in settings beyond the trial population and observation period. The trial studied pediatric patients undergoing elective surgery requiring general intravenous anesthesia and evaluated the primary outcome through 24 hours after T0. Generalizing beyond that population, procedure context, or time window requires evidence not contained in these results.

The secondary outcomes offer related descriptions, not independent confirmation, and the record does not report a multiplicity procedure. Safety counts are also limited to the events and detail recorded. Statistical interpretation should therefore distinguish the observed proportions, formal sponsor analysis, simple recalculation, secondary outcomes, and safety reporting rather than treating them as one conclusion.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition and comparison direction matter. Complete response is a composite binary outcome that requires no vomiting, no retching, and no rescue medication during a specified postoperative window. Its group percentages are easy to understand, but the between-group risk difference and its confidence interval are needed to assess the comparative estimate and its precision.

It also demonstrates the distinction between a registry's formal analysis and an unadjusted recalculation from posted summaries. The formal result is labeled non-inferiority or equivalence, while the recalculation compares the observed proportions without an adjusted model. Those analyses should not be conflated. In particular, a non-inferiority or equivalence claim depends on a margin and methods that are not reported in the registry record. A confidence interval that includes zero is not, by itself, proof of equivalence.

The results also show why related secondary outcomes and multiple comparisons require context. No vomiting, no emetic episodes, no rescue medication, and complete response are connected but not interchangeable. Their pattern can help describe what was observed, while unreported multiplicity handling limits the weight that should be placed on secondary comparisons as confirmatory evidence.

Finally, the reported confidence intervals make uncertainty visible. A point estimate is not a precise answer on its own; the range of values compatible with the analysis is part of the result. Separating observed findings from what the design and registry record do not establish is central to sound interpretation of clinical trial statistics.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record does not report the sponsor's statistical method, the non-inferiority or equivalence margin, or the original sample-size justification. This makes it difficult to evaluate the formal analysis against its intended decision criterion. The simple recalculation is unadjusted and should not be treated as a substitute for an analysis plan or a full participant-level analysis.

The Full Analysis Set is described, but the record does not report how many randomized patients were excluded from it, why any exclusions occurred, or how missing primary-outcome data were handled. No sensitivity analysis for missing data is reported. As a result, the robustness of the estimates to exclusions or incomplete outcome data cannot be assessed from the registry record.

The record does not report stratification factors, allocation-concealment details, or the complete follow-up schedule. It also does not report interim analyses, stopping rules, or multiplicity adjustments. These are reporting gaps, not evidence that such procedures were absent. The secondary outcome of no nausea is listed, but its result is not reported in the registry record.

The safety information includes serious and other adverse-event counts and selected serious-event terms, but the record does not give event-level timing, relatedness assessments, or enough detail to compare particular event types between groups. The efficacy observation window is limited to 0-24 hours after T0. Results for later postoperative outcomes are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of Palonosetron IV to Prevent Postoperative Nausea and Vomiting in Pediatric Patients — NCT01395901.
• Registry record last updated 2014-07-30; status last verified 2014-07.
• Results first posted 2014-07-30.
• 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

NCT01395901 is a completed phase 3, multicenter, randomized, quadruple-masked, parallel-group study sponsored by Helsinn Healthcare SA. It compared a single intravenous dose of palonosetron with a single intravenous dose of ondansetron, using a double-dummy design, in pediatric patients undergoing elective surgery requiring general intravenous anesthesia.

The primary outcome was complete response during 0-24 hours after T0, defined as no vomiting, no retching, and no antiemetic rescue medication. The reported proportions were 78.2% for palonosetron and 82.7% for ondansetron. The registry reports a risk difference of -4.4 with a 95% confidence interval from -10.5 to 1.7 and classifies its analysis as non-inferiority or equivalence. The margin and method are not reported in the registry record. The unadjusted recalculation gives a risk difference of 0.045 with a 95% confidence interval from -0.015 to 0.105.

Related secondary outcomes and safety counts are recorded, but multiplicity handling, missing-data procedures, and several details needed to interpret the formal analysis are not reported.