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 (NCT00828295), a randomized phase 3 study. The primary outcome is Proportion of Patients With no Emetic Episodes in the Overall Time Period 0-72 Hours Post-operatively.

2. Clinical Question

The registry describes a study of palonosetron’s safety and efficacy for preventing postoperative nausea and vomiting in pediatric patients. The principal efficacy measure focused on whether a patient experienced any emetic episode during the stated post-operative period. It therefore describes the proportion meeting this event-based outcome, rather than the number or severity of episodes among those who experienced one.

The clinical question is dose-comparative, not a comparison with placebo or no treatment. Because both groups received palonosetron, the observed contrast can describe how the two assigned regimens performed relative to one another in the trial population. It cannot, by itself, estimate the difference between palonosetron and receiving no palonosetron.

The registry also lists complete response during 0-24 hours as a secondary outcome. That measure concerns a shorter post-operative period and is distinct in its stated definition from the primary outcome. Details defining “complete response” beyond its registry label are not reported in the registry record.

3. Trial Design

This was a phase 3, multicenter, randomized, double-blind, parallel-group study. The official title describes the study as stratified and quadruple masked. The registry marks the study as completed and lists enrollment as 150. The two randomized groups each have 75 participants in the posted primary results.

The groups received single IV doses of palonosetron at different weight-based doses, with a maximum total dose specified for each regimen. The 1 mcg/kg group had a maximum total dose of 0.075 mg, and the 3 mcg/kg group had a maximum total dose of 0.25 mg. There was no placebo or untreated group in the posted comparison.

The registry lists the study start as 2008-08 and primary completion as 2008-12. Its stated objective was to assess safety and efficacy for prevention of postoperative nausea and vomiting through 72 hours post-operatively. Eligible patients, as described in the study summary, were children aged 28 days up to 16 years inclusive undergoing surgical procedures requiring general endotracheal inhalation anesthesia.

For the primary outcome, the analysis population was the Full Analysis Set. It included randomized patients who received study drug and had general anesthesia and surgery. The record says patients were assigned to the group to which they were randomized, consistent with its stated intent-to-treat principle within that defined population. This is not the same as including every randomized patient regardless of whether they received study drug or proceeded to surgery.

The registry does not report the details of the stratification factors, the allocation sequence, the method used to conceal allocation, or how masking was maintained. The trial’s original sample-size assumptions and its complete statistical analysis plan are 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

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

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 Proportion of Patients With no Emetic Episodes in the Overall Time Period 0-72 Hours Post-operatively, measured over 0-72 hours post-operatively.

The primary endpoint is the proportion of patients with no emetic episodes during 0-72 hours post-operatively. It is a binary, patient-level outcome: each patient either had no emetic episode during the specified period or did not meet that criterion. The registry reports the result as a percentage of patients with a 95% confidence interval.

This measure is used to describe the frequency of patients meeting a clearly stated clinical outcome over a defined observation period. A proportion is straightforward to interpret at the group level, while the binary definition means that it does not convey how many episodes occurred in patients who had any episode, when an episode occurred, or its severity. Those details are not part of the endpoint as named in the registry record.

Patients were included in the Full Analysis Set if they were randomized, received study drug, and had general anesthesia and surgery. Assignment was according to randomized treatment group. This population definition matters because the reported proportion applies to that analysis set, rather than automatically representing every patient enrolled or randomized.

The endpoint can support a comparison between the two palonosetron dose groups over the stated post-operative period. Since both groups received active study drug, the measure does not establish how either dose compares with placebo or no treatment. The registry does not report additional details about endpoint ascertainment or the handling of incomplete observation during the follow-up period.

7. Results Posted in the Registry

• 3 mcg/kg Arm: 84.0% (63/75) versus 88.0% (66/75) on control; risk difference -4.0 percentage points (95% CI -15.1 to 7.1), risk ratio 0.95 (0.84–1.09); unadjusted two-proportion z-test p = 0.480.

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 Complete Response 0-24 Hours

• 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:
  • 3 mcg/kg Arm: 84.0% (63/75) versus 88.0% (66/75) on control; risk difference -4.0 percentage points (95% CI -15.1 to 7.1), risk ratio 0.95 (0.84–1.09); unadjusted two-proportion z-test p = 0.480.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 3 mcg/kg Arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary endpoint: complete response during 0-24 hours. The posted summary-level pattern is consistent in direction with the primary outcome, in that the group contrast does not establish a clear separation between the two dose regimens. The secondary endpoint concerns a shorter period and a separately named response criterion, so it provides related but not identical information.

The secondary outcome’s posted group values and comparison are identical to those listed for the primary outcome. The registry record does not explain why the summaries match or provide further detail about the secondary endpoint’s derivation. This limits interpretation of the secondary result as independent corroboration of the primary result.

Unadjusted secondary findings generally carry less inferential weight when several outcomes or comparisons may be examined. Considering multiple results increases the chance that an apparently notable finding arises by chance, unless the analysis plan accounts for multiplicity. The registry does not report a multiplicity adjustment or a hierarchy for testing the secondary outcome. No reported sponsor analyses are listed for it.

The secondary outcome can therefore be read as additional descriptive context, not as a separate confirmatory conclusion. Its relationship to the primary result is constrained by the shared trial population, the similar outcome context, the identical posted summaries, and the absence of reported analysis details. The registry does not establish whether the secondary measure was intended to support a formal confirmatory claim.

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

• Proportion of Patients With Complete Response 0-24 Hours

9. Statistical Interpretation

10. Statistical Methods Explained

A binary outcome records whether each patient met a specified criterion. For this trial’s primary endpoint, the criterion was having no emetic episodes over 0-72 hours post-operatively. The group percentage describes how common that outcome was among patients in the defined analysis population. A percentage is useful for communicating absolute frequency, but it does not describe the number of episodes or other features not included in the endpoint definition.

The reported risk difference compares the proportion in the 3 mcg/kg arm with the proportion in the 1 mcg/kg arm. Under that direction of comparison, a negative estimate means the observed proportion meeting the outcome was lower in the 3 mcg/kg group. The estimate is -0.04. The confidence interval around that difference extends from -0.151 to 0.071. These values describe uncertainty in the difference on the proportion scale; they are not a separate estimate of the chance that one dose is better.

A confidence interval is a range produced by a statistical procedure that, under its assumptions, is intended to capture the population quantity across repeated applications of the procedure at the stated confidence level. In practical reading, it communicates both the estimate and its precision. It is not a range containing a known proportion of individual patient outcomes, and it does not assign a probability to the true value after the data have been observed.

The unadjusted p-value of 0.48 is a recalculation from the posted summary statistics. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the test assumptions. It is not the probability that the null hypothesis is true. An unadjusted value also does not account for the possibility of multiple comparisons unless an adjustment is made; whether the trial’s sponsor used a different inferential approach is not reported in the registry record.

The posted arm-level confidence intervals describe each group’s proportion separately, while the risk-difference interval addresses the contrast between groups. The latter is the more direct interval for the dose comparison. Separate arm intervals should not be used as a substitute for the interval on the contrast, because uncertainty in the difference depends on both groups and the calculation used for the comparison.

The registry describes the study as randomized, parallel-group, double-blind and quadruple masked. Randomization is generally intended to make treatment groups comparable with respect to measured and unmeasured characteristics on average, although it does not ensure exact balance in a particular trial. Masking is generally intended to reduce the influence of knowledge about assigned treatment on care, reporting, or assessment. The specific procedures and the stratification details are not reported in the registry record.

The stated Full Analysis Set included randomized patients who received study drug and had general anesthesia and surgery, with treatment assignment based on randomized group. This definition retains randomized assignment for included patients, but it also defines eligibility for the analysis set after randomization. The registry does not give a participant flow account or explain how patients who did not meet those conditions were handled in other analyses.

Over-dispersion is a general concern when data vary more than a statistical model expects; it can make standard errors too small if the model assumes less variation than is present. For a simple binary group proportion, the relevant assumptions concern the outcome distribution and sampling procedure rather than count over-dispersion in the manner used for some count models. The registry does not report a model-based primary analysis or an adjustment for over-dispersion, so no such procedure should be assumed.

The sample-size planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It scales the observed effect to illustrate planning for 100%, 75%, or 50% of that observed effect. These are planning assumptions for the illustration, not evidence about the trial’s original design calculations. The original sample-size justification is not reported in the registry record.

The registry lists no reported analyses for the secondary outcome. A result recalculated from summary statistics can be useful for understanding the posted numbers, but it may not reflect a prespecified model, covariate adjustment, stratification, or other details in a full statistical analysis plan. Such details are not reported in the registry record. The recalculated comparison should therefore be read as an unadjusted summary-level analysis, not as a claim about the sponsor’s full statistical methods.

11. Confidence Intervals and Precision

The primary arm estimates are 88.0% and 84.0%, and their respective 95% confidence intervals are 78.4% to 94.4% and 73.7% to 91.4%. These intervals communicate uncertainty around each arm’s proportion. They are broad enough that the underlying group proportions are not pinned down to a narrow range by the posted data.

For the comparison itself, the estimated risk difference is -0.04, with a 95% confidence interval from -0.151 to 0.071. The interval crosses zero and includes both negative and positive values. Thus the data are compatible with a lower proportion in the 3 mcg/kg arm, a higher proportion in that arm, or little difference. The interval’s breadth limits precision about the direction and size of the difference.

Confidence intervals are more informative than a single point estimate because they show the range of values reasonably compatible with the data under the calculation’s assumptions. They do not resolve clinical importance on their own. The registry does not report a threshold for what difference would be clinically important, so the interval cannot be classified against a stated clinical margin.

The group denominators in the primary results are 75 in each arm. The registry does not report additional precision analyses, a prespecified equivalence margin, or a detailed account of missing outcome data. These omissions matter when judging how far the estimates can be generalized beyond the analyzed patients.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total event counts. 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 also considers planning for 75% and 50% of that observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm under the stated planning assumptions for a future study designed to have 80% power to detect the effect used in that row. The 90% power column gives the corresponding estimate for 90% power. In general, higher planned power requires more participants when other assumptions are held constant. These figures are prospective planning illustrations, not a description of what the completed trial achieved.

The illustration reports 1,181 participants per arm for planning around 100% of the observed effect, 2,036 for 75% of the observed effect, and 4,438 for 50% of the observed effect in the 80% power column. The 90% power column reports 1,580, 2,725, and 5,940 participants per arm for those same effect fractions. Smaller effects need more participants to detect under otherwise comparable assumptions, which is why the estimates rise as the effect fraction becomes smaller.

These figures are not observed power. They are not a measure of the probability that the completed study detected a true effect, nor do they show that the trial was or was not adequately planned. The planning calculation is based on the observed effect, which is uncertain, and the original protocol assumptions are not reported in the registry record.

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 = 0.880; treatment proportion p₁ = 0.840; average p̄ = 0.860.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4907 = 0.9618.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4899 = 0.4123.
4. n = (0.9618 + 0.4123)² / (-0.0400)² = 1,180.1, rounded up to 1,181 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 <- 0.88                          # control proportion
p1 <- 0.84                          # 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(828295)
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 = 1,181 (80% power), 1,580 (90% power)
 75% of observed effect: n per arm = 2,036 (80% power), 2,725 (90% power)
 50% of observed effect: n per arm = 4,438 (80% power), 5,940 (90% power)
power.prop.test: 1180.1 
Simulated power at n = 1,181 per arm: 0.805 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators evaluate more than one endpoint, comparison, subgroup, or analysis. In general, the more opportunities there are to find a statistically unusual result, the greater the risk of at least one chance finding. Prespecified testing hierarchies or adjusted significance procedures can address that issue, but the registry record does not report such a plan for this trial.

One secondary outcome is listed, and the registry reports no analyses for it. It does not state whether the secondary endpoint was formally tested, whether an adjustment for multiple testing was planned, or how the primary and secondary outcomes were ordered for inference. Accordingly, the unadjusted recalculated result should not be treated as multiplicity-controlled evidence.

The record defines the primary analysis population as randomized patients who received study drug and had general anesthesia and surgery. It states that patients were analyzed according to randomized group. It does not provide a participant flow account, describe patients excluded from the Full Analysis Set, or report a separate per-protocol analysis population.

Methods for missing outcome data are not reported in the registry record. It is not stated whether all patients had outcome information through 0-72 hours, how incomplete follow-up was handled, or whether any sensitivity analyses assessed missingness. If outcome information is incomplete, the assumptions used to handle it can affect the estimated proportions and their uncertainty.

The registry also does not report the detailed statistical analysis plan, model specification, covariate adjustments, or whether any interim analyses occurred. These items should not be inferred from the randomized design or from the posted summary statistics. Their absence limits assessment of prespecification and of how closely the posted results represent the complete planned analysis.

15. 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 non-serious adverse event terms

The safety results list 74 patients at risk in the 1 mcg/kg arm and 76 in the 3 mcg/kg arm for serious adverse events. The serious adverse event count is listed as 0 in each arm. These figures describe the posted registry entries; they do not establish that no adverse effects of any kind occurred.

The registry lists other adverse events affecting 29 of 74 patients in the 1 mcg/kg arm and 32 of 76 patients in the 3 mcg/kg arm. These are descriptive counts, not a randomized statistical comparison with a reported confidence interval or p-value. The record does not provide the event terms in the serious adverse event listing, and deaths are not reported in the registry record.

Interpretation is limited because the record does not give detailed definitions, severity grading, collection procedures, or follow-up duration for these safety summaries. A zero serious-event count in the posted results is not proof that a regimen has no risk, particularly without fuller information about event ascertainment and the study population.

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

The posted results describe two palonosetron dose groups in a randomized pediatric surgical study. For the primary endpoint, the group proportions with no emetic episodes during 0-72 hours post-operatively were fairly close in the observed sample. The estimated risk difference was -0.04, and its 95% confidence interval crossed zero. The unadjusted recalculated p-value was 0.48.

These results do not establish a statistically clear difference between the two regimens on the primary endpoint. They also do not prove that the regimens are equivalent. Equivalence requires a prespecified margin and an analysis suited to testing whether any difference lies within that margin; neither is reported in the registry record. The interval retains uncertainty about both the direction and size of the difference.

The comparison is between two active doses. It cannot establish how either regimen compares with placebo, no treatment, or another antiemetic approach. It also does not answer questions about outcomes beyond the registry’s specified measure, such as severity or number of emetic episodes among patients who experienced them.

The findings apply most directly to the population and conditions described in the record: children aged 28 days up to 16 years inclusive undergoing surgery requiring general endotracheal inhalation anesthesia, within the defined Full Analysis Set. They should not automatically be generalized to other ages, procedures, anesthesia settings, or patient groups.

The record’s safety entries are descriptive and do not provide a complete account of adverse-event definitions or ascertainment. The posted results therefore support a bounded reading of the observed efficacy proportions and safety counts, not a broad conclusion about all possible benefits or harms. The analysis details and missing-data methods are not reported in the registry record, further limiting certainty about the full evidential picture.

17. Why This Trial Matters Statistically

This trial illustrates why the treatment contrast must be matched to the question. Randomization can support a comparison of the assigned groups, but the groups in this study received different doses of the same active drug. The design therefore addresses a dose-regimen comparison, not whether palonosetron is better than no treatment.

It also shows the value of distinguishing an estimate from its precision. The point estimate alone indicates the observed direction of the difference, while the confidence interval makes clear that the data leave substantial uncertainty about the direction and size of the underlying contrast. A non-significant unadjusted result is not the same as evidence of equivalence.

The endpoint definition matters as much as the numerical result. “No emetic episodes” over 0-72 hours is a specific binary outcome. It does not capture all dimensions of postoperative nausea and vomiting, and it should not be interpreted as a complete account of the patient experience.

Finally, registry summaries are useful but incomplete sources for statistical appraisal. The record supplies the analysis population and group summaries, yet does not report the full analysis plan, missing-data methods, multiplicity procedures, or original sample-size justification. Recognizing the boundary between posted evidence and unreported methods is part of sound 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The comparison includes two active palonosetron regimens and no placebo or untreated group. It cannot isolate the effect of palonosetron relative to no palonosetron. The primary question is limited to comparing the stated dose regimens in the listed study population.

The primary estimate is imprecise enough that its confidence interval includes differences in either direction. The registry does not report a clinical threshold for an important difference, an equivalence margin, or a noninferiority margin. The result therefore cannot be used to declare the regimens equivalent or to judge the clinical importance of every value in the interval.

The eligible population is specific: children aged 28 days up to 16 years inclusive undergoing procedures requiring general endotracheal inhalation anesthesia. Applicability to other settings or patient groups is not established by the posted results. The record does not provide demographic or clinical subgroup results to assess variation in the outcome across patient characteristics.

The registry does not describe endpoint ascertainment in detail, report how missing outcome information was handled, or provide a participant flow account. The details of stratification and masking procedures are also not reported. These omissions constrain assessment of implementation and potential sources of bias.

The record lists one secondary outcome but no reported analyses for it, and its posted summary matches the primary result. The reason for that match is not explained. The statistical analysis plan, multiplicity approach, interim analyses, and original sample-size justification are not reported in the registry record. These limitations make the summary less informative about prespecification and the full set of analyses than a complete protocol and analysis report would be.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety and Efficacy of Palonosetron IV to Prevent Postoperative Nausea and Vomiting in Pediatric Patients — NCT00828295.
• Registry record last updated 2015-04-03; status last verified 2014-07.
• Results first posted 2014-08-15.
• 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

NCT00828295 is a completed phase 3, multicenter, randomized, parallel-group study of single-dose IV palonosetron for preventing postoperative nausea and vomiting in pediatric patients. The official title describes a double-blind, quadruple-masked, stratified study. Enrollment is listed as 150, with the primary results showing 75 participants in each dose arm.

The primary endpoint was the proportion with no emetic episodes during 0-72 hours post-operatively. The posted proportions were 88.0% for 1 mcg/kg and 84.0% for 3 mcg/kg. The estimated risk difference was -0.04, with a 95% confidence interval from -0.151 to 0.071; the unadjusted recalculated p-value was 0.48.

The registry lists complete response during 0-24 hours as a secondary outcome but reports no analyses for it. Detailed missing-data methods, multiplicity procedures, and the original sample-size justification are not reported in the registry record.