Efficacy and Safety of Palonosetron Intravenous in Prevention of Chemotherapy Induced Nausea and Vomiting in Pediatric Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Palonosetron Intravenous in Prevention of Chemotherapy Induced Nausea and Vomiting in Pediatric Patients (NCT01442376), a randomized phase 3 study. The primary outcome is Proportion of Patients With Complete Response 0 to 24 Hours (Acute Phase) in Cycle 1.

2. Clinical Question

The registry describes a study of prevention of chemotherapy-induced nausea and vomiting in pediatric patients. Its primary objective was to evaluate the two palonosetron doses through 120 hours after chemotherapy began, in single and repeated chemotherapy cycles. The posted primary endpoint is narrower: it measures complete response from 0 to 24 hours after T0 in Cycle 1. A secondary endpoint addresses the delayed phase, from more than 24 to 120 hours in Cycle 1.

The central statistical comparison is between each palonosetron dose and ondansetron. The posted primary results also allow the two palonosetron groups to be considered descriptively, but a sponsor-reported formal analysis is available only for specified pairwise comparisons. The registry record does not report the clinical threshold that would make a difference important to patients, nor does it report a prespecified margin for judging the comparisons.

3. Trial Design

This was a Phase 3, randomized, multicenter, parallel-group study with quadruple masking. The official title describes a double-blind study, while the registry’s masking field records quadruple masking. The registry lists an enrollment of 502 and a completed study. The listed start was 2011-09 and the primary completion was 2012-10.

Three groups received either palonosetron 10 mcg/kg, palonosetron 20 mcg/kg, or ondansetron. The arm descriptions also list placebo treatments, consistent with the study’s masking, but further details of how the masking was implemented are not reported in the registry record. The specific randomization procedure, allocation concealment, and whether any stratification was used are not reported in the registry record.

The primary endpoint was assessed in Cycle 1 among the Full Analysis Set population. The analysis counts were 166 for palonosetron 10 mcg/kg, 165 for palonosetron 20 mcg/kg, and 162 for ondansetron. These are the group sizes for the posted primary outcome, not a description of every analysis population. The safety results use different at-risk counts, which are reported with those results.

The registry states that the study also considered repeated chemotherapy cycles and pharmacokinetics in a subset of pediatric patients. Results for those objectives, beyond the posted Cycle 1 outcomes, are not reported in the registry record. The original sample-size justification, the planned analysis details, and the intended handling of repeated observations 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.

Before assignment: A total of 502 patients were enrolled and randomly assigned to treatment. Study drug was not administered to 8 randomized patients, of these patients 2 had also an adverse event and were counted under this category in overall study statement. Therefore 494 patients did receive the study drug and are part of the analysis for the safety population.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) population

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 (FAS) population which included all randomized patients receiving the active study drug and HEC or MEC. Following the intent-to-treat principle, patients were assigned to the study treatment group according to the randomized treatment.

6. Primary Endpoint

The registry lists the primary outcome as Proportion of Patients With Complete Response 0 to 24 Hours (Acute Phase) in Cycle 1, measured over 0 to 24 hours after T0.

The primary endpoint is the proportion of patients with complete response from 0 to 24 hours after T0 in Cycle 1. T0 is the start of administration of the most emetogenic chemotherapy. A complete response required no vomiting, no retching, and no use of antiemetic rescue medication during the acute phase. The endpoint therefore combines several clinically relevant events into one binary outcome: each patient either met all three conditions or did not.

For each group, the reported percentage estimates the share of patients in the Full Analysis Set who achieved that definition of complete response. This outcome is used to summarize prevention of acute nausea and vomiting-related events during a defined window after chemotherapy. It does not measure the severity or duration of symptoms among patients who did not meet the complete-response definition, and it does not by itself describe response during later cycles.

As a general statistical point, a binary endpoint makes group proportions straightforward to compare, but the interpretation depends on the endpoint definition and observation window. Here, the definition includes rescue medication use as well as vomiting and retching. The registry record does not report a separate primary measure of nausea intensity, quality of life, or symptom severity.

7. Results Posted in the Registry

• Palonosetron 20 mcg/kg: 59.4% (98/165) versus 54.2% (90/166) on control; risk difference 5.2 percentage points (95% CI -5.5 to 15.8), risk ratio 1.10 (0.91–1.32); unadjusted two-proportion z-test p = 0.342.
• Ondansetron: 58.6% (95/162) versus 54.2% (90/166) on control; risk difference 4.4 percentage points (95% CI -6.3 to 15.1), risk ratio 1.08 (0.89–1.31); unadjusted two-proportion z-test p = 0.419.

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 >24 to 120 Hours (Delayed Phase) in Cycle 1

• 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:
  • Palonosetron 20 mcg/kg: 38.8% (64/165) versus 28.9% (48/166) on control; risk difference 9.9 percentage points (95% CI -0.3 to 20.0), risk ratio 1.34 (0.99–1.82); unadjusted two-proportion z-test p = 0.058.
  • Ondansetron: 28.4% (46/162) versus 28.9% (48/166) on control; risk difference -0.5 percentage points (95% CI -10.3 to 9.3), risk ratio 0.98 (0.70–1.38); unadjusted two-proportion z-test p = 0.917.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Palonosetron 20 mcg/kg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ondansetron and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome concerns complete response in the delayed phase of Cycle 1, from more than 24 to 120 hours after T0. The broad pattern differs by group: the 20 mcg/kg palonosetron group has a higher observed delayed-phase response proportion than the other two groups, while the ondansetron and 10 mcg/kg palonosetron proportions are close. The delayed-phase estimates are less favorable in absolute terms than the corresponding acute-phase estimates in each group, reflecting that complete response was less common in the later window.

The recalculated comparisons for this secondary endpoint are exploratory and unadjusted. In particular, an unadjusted p-value for a secondary outcome should carry less weight than a prespecified primary analysis when several outcomes, comparisons, or time windows are considered. A collection of tests increases the chance that at least one apparently notable result arises through random variation. The registry record does not report a multiplicity adjustment or a hierarchy assigning confirmatory status to the secondary endpoint.

The secondary pattern can add context to the primary result, but it does not replace it. The primary endpoint addresses acute-phase response; the secondary endpoint addresses the delayed phase. They cover different time periods and should not be treated as repeated measurements of the same outcome. The registry describes objectives involving repeated chemotherapy cycles, but further cycle-specific results are not reported in the registry record.

General statistical explanation: secondary outcomes can be valuable for exploring whether an observed pattern persists across clinically relevant periods. Their evidential weight depends on whether they were prespecified, how many analyses were conducted, how missing data were handled, and whether multiplicity was addressed. Those details are not reported in the registry record. Accordingly, the delayed-phase results are best viewed as supportive descriptive information rather than as a stand-alone confirmatory conclusion.

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

• Proportion of Patients With Complete Response >24 to 120 Hours (Delayed Phase) in Cycle 1

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is binary: a patient either achieved complete response during the defined acute-phase window or did not. The group-level results are expressed as percentages, and the recalculated pairwise comparisons use risk differences. A risk difference is the difference between two group proportions, expressed in the scale used by the calculation. A value of zero corresponds to equal proportions; a value above or below zero indicates the direction of the difference according to the comparison order.

What do the recalculated comparisons represent?

The recalculated comparisons use the posted event proportions and group sizes to estimate unadjusted differences between groups. The palonosetron 20 mcg/kg comparison is against palonosetron 10 mcg/kg, and the ondansetron comparison is also against palonosetron 10 mcg/kg. The reported 95% confidence intervals for these risk differences include zero. The accompanying unadjusted p-values are 0.342 and 0.419, respectively. These calculations do not include an adjustment for multiple comparisons.

Unadjusted means that the comparison is presented without a statistical correction for the fact that more than one comparison or outcome may be examined. It does not mean that the estimate is necessarily biased, but it does mean that the p-values should not be treated as if they came from a single isolated test when several tests are relevant. The method used to calculate these recalculated intervals and p-values is not stated in the registry record.

How do the sponsor analyses differ?

The registry reports two analyses classified as non-inferiority or equivalence analyses. They report risk differences and 97.5% confidence intervals, but no p-values. The analysis method and the non-inferiority or equivalence margin are not reported in the registry record. Those analyses should not be treated as interchangeable with the simple unadjusted recalculations: their confidence level and analytic purpose differ, and the registry does not provide enough methodological detail to reconstruct them.

In general, a non-inferiority analysis asks whether the data rule out a disadvantage larger than a prespecified margin; an equivalence analysis asks whether the data support effects within prespecified bounds in both directions. These are general descriptions, not claims about the particular protocol. Without the margin and method, the registry record does not support a full independent interpretation of the sponsor’s decision criteria.

What do confidence intervals contribute?

A confidence interval represents uncertainty around an estimate under a statistical procedure. General explanation: repeated use of a method with the same stated confidence level would produce intervals containing the true parameter at that rate under the method’s assumptions. An interval should not be read as a probability statement about the particular true effect. For the primary group proportions, the registry reports 95% confidence intervals. The sponsor analyses use 97.5% confidence intervals. The recalculated risk-difference intervals are 95% intervals.

The intervals for group proportions and those for risk differences answer different questions. A group-proportion interval describes uncertainty about a single group’s response proportion. A risk-difference interval describes uncertainty about the contrast between two groups. Overlap between two group-proportion intervals is not itself a formal test of the difference; the risk-difference interval is more directly aligned with that comparison.

Why can binary outcomes have imprecise comparisons?

General statistical explanation: precision depends on the number of observed participants and on how common the outcome is, as well as on the analysis method. Even when each group has a few hundred participants, a difference between proportions can remain uncertain. An interval that includes zero can be compatible with no difference as well as with differences in either direction. The width of the interval matters, not only whether it crosses zero.

The primary results report group sizes and confidence intervals, but they do not give a detailed account of missing outcome data, deviations from random assignment, or the exact statistical procedure. The registry record does not report whether any covariate adjustment was used in the sponsor’s primary analysis. The simple recalculations should therefore be understood as transparent summaries of the posted numbers rather than reproductions of an undocumented model.

What does the planning calculation mean?

The sample-size figures are planning illustrations derived from the observed effect, not the trial’s original design justification. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculations consider effects equal to 100%, 75%, or 50% of the observed effect. They report participants per arm for this binary outcome. General explanation: if the effect to be detected is smaller while other assumptions stay fixed, more participants are generally needed to distinguish that effect from random variation. These planning figures are not observed power and do not show the probability that the completed study detected a true effect.

11. Confidence Intervals and Precision

The primary group estimates have 95% confidence intervals: 46.3% to 61.9% for palonosetron 10 mcg/kg, 51.5% to 66.9% for palonosetron 20 mcg/kg, and 50.6% to 66.2% for ondansetron. These intervals communicate uncertainty in each group’s response proportion. They are broad enough that the exact underlying proportions are not pinned down closely.

For the comparisons, the recalculated risk-difference interval for palonosetron 20 mcg/kg versus palonosetron 10 mcg/kg runs from -0.055 to 0.158. For ondansetron versus palonosetron 10 mcg/kg, it runs from -0.063 to 0.151. Both intervals include zero and extend in both directions. Thus the posted summary data do not tightly distinguish a difference from no difference, and they are also compatible with effects in either direction.

General statistical explanation: a confidence interval is a measure of estimation uncertainty, not a guarantee that the true value lies in the interval or a measure of clinical importance. A narrow interval is more precise than a wide interval, but precision alone does not establish whether an effect matters. Clinical interpretation also depends on the outcome and any meaningful threshold, which is not reported in the registry record.

The sponsor’s 97.5% confidence intervals concern its reported risk-difference analyses and should be read separately from the recalculated 95% intervals. The analysis method and margin are not reported in the registry record, limiting a direct assessment of the sponsor’s stated non-inferiority or equivalence framework.

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 for this binary outcome, not total events. They are illustrative calculations based on the observed effect, rather than the original trial design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculations consider the full observed effect and smaller fractions of that observed effect.

The 80% power column describes the participant count per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect, if that effect and the calculation assumptions were correct. The 90% power column gives the corresponding per-arm count for a higher target probability of detecting that effect. These are planning concepts; they are not claims about the probability that the completed trial detected its actual effect.

The primary comparison illustrates how strongly the assumed effect changes the required sample size: using 100% of the observed effect, the estimates are 1,436 participants per arm for 80% power and 1,922 for 90% power. Planning for 75% of the observed effect gives 2,563 participants per arm for 80% power and 3,430 for 90% power. Planning for 50% of the observed effect gives 5,785 participants per arm for 80% power and 7,744 for 90% power.

Smaller effects require more participants to detect under these assumptions because they are harder to distinguish from random variation. These illustrations use the observed effect as their starting point, so they should not be mistaken for independent evidence that the observed difference is real or for the study’s original sample-size justification. The registry record does not report that original justification. This is 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 = 0.542; treatment proportion p₁ = 0.594; average p̄ = 0.568.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7005 = 1.3730.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6996 = 0.5888.
4. n = (1.3730 + 0.5888)² / (0.0518)² = 1,435.9, rounded up to 1,436 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 <- 0.542168674698795                          # control proportion
p1 <- 0.593939393939394                          # 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(1442376)
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 = 1,436 (80% power), 1,922 (90% power)
 75% of observed effect: n per arm = 2,563 (80% power), 3,430 (90% power)
 50% of observed effect: n per arm = 5,785 (80% power), 7,744 (90% power)
power.prop.test: 1435.9 
Simulated power at n = 1,436 per arm: 0.800 (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 two sponsor analyses classified as non-inferiority or equivalence analyses. For palonosetron 20 mcg/kg compared with ondansetron, the reported risk difference is 0.36, with a 97.5% confidence interval from -11.7 to 12.4. For palonosetron 10 mcg/kg compared with ondansetron, the reported risk difference is -4.4, with a 97.5% confidence interval from -16.4 to 7.6. No p-values are reported for these analyses.

The simple recalculations use the posted summary proportions and group sizes and give unadjusted risk differences with 95% confidence intervals. They are useful as direct contrasts of the posted rates, but they are not a reconstruction of the sponsor’s formal analysis. The sponsor’s method and the margin used to assess non-inferiority or equivalence are not reported in the registry record, so the formal decision criteria cannot be checked from the available record.

The reported estimates and intervals should therefore be read as separate analyses with different stated confidence levels and unspecified methodological details. The registry record does not provide enough information to determine exactly how the sponsor’s calculations relate to the recalculated comparisons.

15. Multiplicity, Missing Data and Analysis Populations

The study includes three treatment groups, a primary endpoint, a posted secondary endpoint, and objectives relating to repeated cycles. The registry record does not report a strategy for controlling multiplicity across treatment comparisons, endpoints, time windows, or cycles. It also does not report a testing hierarchy or which analyses, beyond the named primary outcome, were intended to support confirmatory conclusions. The recalculated p-values are explicitly unadjusted and should be interpreted in that context.

The registry identifies the primary analysis population as the Full Analysis Set, but does not give a detailed operational definition of that population. The numbers analyzed for the primary outcome are reported by group. The record does not explain how participants with incomplete outcome assessments, protocol deviations, or treatment discontinuation were handled. It does not report imputation methods, sensitivity analyses for missing data, or the amount and pattern of missing primary outcome data. These omissions limit assessment of whether the endpoint results could be affected by missingness.

The safety groups have separate at-risk counts, and those counts differ from the primary outcome analysis counts. The registry record does not explain the difference between these analysis populations. The precise populations used for the sponsor’s reported non-inferiority or equivalence analyses are also not reported.

General statistical explanation: multiplicity matters because the chance of at least one false-positive finding can increase when many hypotheses are tested without adjustment. Missing-data methods matter because results can depend on whether participants without an observed outcome resemble those with one. These are general concerns; they do not establish that either issue distorted the results in this trial. The registry record does not report enough detail to assess the extent of either issue.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: febrile neutropenia (18.4%), anaemia (10.2%), thrombocytopenia (8.4%), neutropenia (7.2%), leukopenia (6.0%).

The registry reports serious adverse events among 68 of 167 participants at risk in the palonosetron 10 mcg/kg group, 62 of 163 in the palonosetron 20 mcg/kg group, and 70 of 164 in the ondansetron group. It also reports other adverse events affecting 143 of 167, 130 of 163, and 145 of 164 participants, respectively. These are counts of participants affected and at risk, not rates recalculated.

The listed serious adverse event terms include febrile neutropenia at 18.4%, anaemia at 10.2%, thrombocytopenia at 8.4%, neutropenia at 7.2%, leukopenia at 6.0%, and pyrexia at 4.3%. The registry record does not specify in this summary whether those term frequencies are presented by group or pooled across groups. Death counts are not reported in the registry record.

These summaries describe events recorded during the study; they do not establish that an event was caused by a particular treatment. The registry record does not provide the detailed event-level information, timing, severity breakdown, or statistical comparison needed for a fuller comparative safety assessment.

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

The posted primary outcome shows that a substantial proportion of participants in each group met the acute-phase complete-response definition, with group estimates in a relatively close range. The unadjusted recalculated comparisons are uncertain: their confidence intervals include zero and permit differences in either direction. The data do not establish a clear difference in acute-phase complete response between the compared groups using these simple calculations.

That interpretation is specific to the primary endpoint definition, the first chemotherapy cycle, and the 0-to-24-hour window. It does not describe the full 120-hour period, repeated cycles, nausea severity, or every aspect of treatment experience. The delayed-phase outcome provides additional context, but its secondary and unadjusted status limits the weight it can carry in isolation.

The sponsor also reported analyses classified as non-inferiority or equivalence. Because the method and margin are not reported in the registry record, the basis for interpreting those analyses cannot be fully evaluated from the posted information. The recalculated comparisons are not substitutes for those analyses, and neither set of summaries alone provides every detail needed to judge clinical importance.

General statistical explanation: an uncertain estimate is not proof of no effect, just as a difference in observed percentages is not proof of a real underlying difference. The confidence intervals communicate uncertainty, while the clinical meaning of a given effect would depend on a relevant threshold. Such a threshold is not reported in the registry record. These results are descriptive evidence about the studied participants and outcomes, not medical advice for an individual patient.

18. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison needs to be read at more than one level. The group percentages describe observed response, while the risk differences estimate contrasts between groups. Confidence intervals then show how uncertain those contrasts remain. Considering the point estimates alone would understate that uncertainty; considering only whether a p-value crosses a conventional threshold would also omit information about the range of compatible effects.

The primary outcome is a composite binary definition, combining vomiting, retching, and rescue medication use within a fixed acute-phase window. That makes the outcome interpretable as complete response, but it also means the percentage does not reveal which component most often prevented a patient from meeting the definition. The delayed-phase endpoint addresses another time window and reinforces the importance of keeping estimands and analysis periods distinct.

The registry also demonstrates the limits of reconstructing a formal analysis from summary results. The simple recalculations provide transparent unadjusted contrasts, while the sponsor’s analyses are reported with a different confidence level and a non-inferiority or equivalence classification. Without the sponsor’s method and margin, those analyses cannot be reproduced or fully assessed from the record.

Finally, planning calculations based on an observed effect are not evidence of the study’s original design or of its achieved power. The record does not state the original sample-size rationale. Separating observed results, uncertainty, formal sponsor analyses, planning illustrations, and unreported design details is essential for a calibrated statistical reading.

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.

Several trial-specific limitations arise from the information available in the registry record. The posted primary analysis is restricted to Cycle 1 and the acute phase, although the stated objectives include single and repeated cycles and assessment through 120 hours. Additional results for repeated cycles are not reported in the registry record. Consequently, the primary result cannot by itself characterize outcomes over repeated chemotherapy cycles.

The registry does not report the original sample-size justification, the detailed statistical analysis plan, the method used for the sponsor’s formal comparisons, or the margin for non-inferiority or equivalence. It also does not report how multiplicity was handled or how missing endpoint data were addressed. These omissions limit assessment of the confirmatory status and robustness of the reported comparisons.

The primary endpoint combines three conditions into one complete-response measure. The posted summary does not separate the contributions of vomiting, retching, and rescue medication use, and it does not report a distinct nausea-severity measure. The record also does not provide enough information to assess whether the Full Analysis Set definition or missing observations could influence the results.

Safety information is presented as event counts and selected serious adverse event terms, without detailed timing, attribution, or an explained pooled-versus-group presentation for the listed terms. Death counts are not reported in the registry record. These limitations concern the completeness of the available record; they do not show that the underlying trial did or did not collect additional information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Palonosetron Intravenous in Prevention of Chemotherapy Induced Nausea and Vomiting in Pediatric Patients — NCT01442376.
• Registry record last updated 2014-08-07; status last verified 2014-08.
• Results first posted 2014-07-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed randomized, masked, parallel-group Phase 3 study of intravenous palonosetron at two doses compared with ondansetron in pediatric patients undergoing MEC or HEC. Enrollment was 502. The primary outcome was complete response during the first 24 hours of Cycle 1 in the Full Analysis Set.

The posted acute-phase proportions were 54.2% for palonosetron 10 mcg/kg, 59.4% for palonosetron 20 mcg/kg, and 58.6% for ondansetron. Unadjusted recalculated risk-difference intervals include zero. A delayed-phase endpoint is also reported, along with selected safety counts and sponsor-reported non-inferiority or equivalence analyses. Important details—including the original sample-size justification, multiplicity strategy, missing-data methods, and sponsor analysis method and margin—are not reported in the registry record.