A Study of Aprepitant (MK-0869) in Pediatric Participants Undergoing Surgery (MK-0869-148): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Aprepitant (MK-0869) in Pediatric Participants Undergoing Surgery (MK-0869-148) (NCT00819039), a randomized phase 1 study. The primary outcome is Number of Participants Experiencing Adverse Events (AEs).

2. Clinical Question

The clinical question therefore has two connected but distinct parts: whether a dosing regimen could be informed by pharmacokinetic and safety observations, and how safety outcomes were recorded in the study. The registry also lists secondary outcomes concerning no vomiting, complete response and vomiting frequency in Part II. Those outcomes relate more directly to postoperative vomiting, but the primary endpoint remains the count of participants with adverse events. The study record does not describe a single primary efficacy comparison of aprepitant against ondansetron.

3. Trial Design

The registry describes a completed, multicenter, two-part study in pediatric participants undergoing surgery. It is listed as Phase 1, with randomized allocation and a parallel model. The overall enrollment is recorded as 98. Those design labels apply to the registered study, but the two parts differ in purpose and conduct, so their groups should not be treated as if they all came from one randomized comparison.

Part I was an open-label investigation of a single oral aprepitant dose. Its stated purpose was to assess pharmacokinetic parameters at specified times up to 48 hours after dosing. The arm description says participants aged 6 months to 17 years received aprepitant on Day 1. Part II was the double-blind trial: participants were randomized to a single oral dose of aprepitant or a single intravenous dose of ondansetron on Day 1. The registry does not report further details about sequence generation, allocation concealment, blinding procedures, or the conduct of randomization.

The primary outcome is the number of participants experiencing adverse events up to 21 days after surgery. Its stated population is participants who received at least one dose of study medication. The Part I aprepitant group has 46 participants, the Part II aprepitant group has 27, and the Part II ondansetron group has 25 in the primary outcome data. These are separate group records, not a basis for assuming that every comparison is randomized. In particular, Part I was open-label and served as the reference group in the posted primary comparisons, while randomization is specified for the Part II treatment allocation.

The registry lists 12 outcome measures and five secondary outcomes concerning vomiting-related outcomes. It reports no formal outcome analyses in its analysis listing. The original sample-size justification and detailed statistical analysis plan are not reported in the registry record. Dates recorded for the study are a start of 2009-01-26 and primary completion of 2013-03-12.

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 population consisted of all participants that received at least one dose of study medication and for which AUC0-48 data were available.

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 Number of Participants Experiencing Adverse Events (AEs), measured over Up to 21 Days Post-Surgery.

The primary endpoint counts participants experiencing adverse events up to 21 days after surgery. The registry defines the analysis population as participants who received at least one dose of study medication. The endpoint is a count of participants with an event, rather than a measure of the number of separate adverse-event episodes or their duration. It therefore describes how many participants in each group were recorded as experiencing an adverse event during the stated follow-up window.

In general, adverse-event endpoints are used to characterize safety and tolerability during a study. A count of affected participants can be clinically interpretable as an account of how many people had at least one event, but it does not by itself describe event severity, causality, timing, recurrence, or the full clinical importance of each event. Those details need separate reporting. The registry provides serious and other adverse-event counts, but the primary endpoint title is broader than serious events alone.

The endpoint is also distinct from the study’s vomiting-related secondary outcomes. A participant’s adverse-event status does not directly establish whether vomiting was prevented, and the primary count is not an efficacy measure. The Part I cohort’s purpose was pharmacokinetic assessment and safety monitoring; Part II included the randomized treatment comparison. Because the posted primary comparisons reference the Part I group, their results should not be read as a randomized estimate of the primary endpoint difference between the Part II treatments.

7. Results Posted in the Registry

• Part 2: Oral Aprepitant: 44.4% (12/27) versus 43.5% (20/46) on control; risk difference 1.0 percentage points (95% CI -22.6 to 24.6), risk ratio 1.02 (0.60–1.75); unadjusted two-proportion z-test p = 0.936.
• Part 2: Intravenous Ondansetron: 28.0% (7/25) versus 43.5% (20/46) on control; risk difference -15.5 percentage points (95% CI -38.2 to 7.2), risk ratio 0.64 (0.32–1.31); unadjusted two-proportion z-test p = 0.199.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With No Vomiting Up to 24 Hours Following Surgery in Study Part 2

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Part 2: Intravenous Ondansetron: 80.0% (20/25) versus 80.0% (20/25) on control; risk difference 0.0 percentage points (95% CI -22.2 to 22.2), risk ratio 1.00 (0.76–1.32); unadjusted two-proportion z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part 2: Intravenous Ondansetron and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Complete Response Up to 24 Hours Following Surgery in Study Part 2

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Part 2: Intravenous Ondansetron: 80.0% (20/25) versus 76.0% (19/25) on control; risk difference 4.0 percentage points (95% CI -18.9 to 26.9), risk ratio 1.05 (0.78–1.41); unadjusted two-proportion z-test p = 0.733.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part 2: Intravenous Ondansetron and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With No Vomiting Up to 48 Hours Following Surgery Ini Study Part 2

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Part 2: Intravenous Ondansetron: 80.0% (20/25) versus 72.0% (18/25) on control; risk difference 8.0 percentage points (95% CI -15.6 to 31.6), risk ratio 1.11 (0.81–1.52); unadjusted two-proportion z-test p = 0.508.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Part 2: Intravenous Ondansetron and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address postoperative vomiting more directly than the primary adverse-event endpoint. Across the posted binary outcomes, the observed group counts are generally close, and the risk-difference intervals are broad. The overall pattern does not provide a precise separation between the Part II treatments. The registry also lists vomiting frequency and additional complete-response and no-vomiting outcomes, but numerical results for every listed secondary endpoint are not reported in the registry record.

These outcomes complement rather than replace the primary safety result. The primary endpoint counts participants experiencing adverse events through the stated follow-up; the secondary outcomes concern whether participants had no vomiting or achieved complete response over specified periods. They therefore describe different aspects of the study. A pattern in the vomiting endpoints cannot be used to reinterpret the adverse-event counts as efficacy evidence, and the primary adverse-event result does not settle the question of vomiting prevention.

Unadjusted secondary comparisons carry less weight because multiple endpoints can create more opportunities for chance findings. In general, an analysis plan may address this through a prespecified hierarchy or a multiplicity adjustment, but neither is reported in the registry record. The registry lists no formal analyses for the secondary outcomes. Their estimates can be read descriptively, but isolated p-values should not be treated as confirmatory proof of a treatment difference.

The limitations are not only statistical. The secondary results concern Part II, whereas the primary comparisons use a Part I reference group. The trial record does not provide enough detail to assess missing outcome data or the handling of deviations from assigned treatment. Those omissions further limit how far the secondary patterns can be generalized or attributed. Taken together, the secondary outcomes are useful context for the study’s purpose, but they do not establish superiority, equivalence, or absence of a clinically important difference.

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

• Number of Participants With No Vomiting Up to 24 Hours Following Surgery in Study Part 2
• Number of Participants With Complete Response Up to 24 Hours Following Surgery in Study Part 2
• Number of Participants With No Vomiting Up to 48 Hours Following Surgery Ini Study Part 2
• Number of Participants With Complete Response Up to 48 Hours Following Surgery in Study Part 2
• Number of Participants With Vomiting Frequency in Study Part 2

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant is counted as having experienced an adverse event or not within the stated follow-up. The reported values are numbers of participants, and the comparison summaries express group differences as risk differences. In general, a risk difference is the event proportion in one group minus the event proportion in its reference group. A value of zero corresponds to equal proportions under that contrast. The posted estimates are already expressed as risk differences, so no new calculation is needed to interpret them.

The primary comparison summaries also report risk ratios, odds ratios, confidence intervals, and unadjusted p-values. In general, a risk ratio compares the event proportions, while an odds ratio compares event odds. These are different scales for describing an association and can look different in magnitude, particularly when events are not rare. Neither measure resolves questions about study design: a numerical contrast between groups is not automatically a causal treatment effect. Here, the primary comparisons use the Part I aprepitant group as reference for both Part II groups. Since Part I was an open-label pharmacokinetic investigation and Part II was randomized and double-blind, the cross-part comparisons are not the randomized comparison.

Randomization is useful because it aims to make treatment groups comparable with respect to both measured and unmeasured characteristics, on average. That rationale applies to the Part II allocation of aprepitant or ondansetron. It does not make the Part I cohort interchangeable with a randomized Part II group. The registry does not report details of the randomization method or concealment, so those procedures cannot be assessed from this record.

Confidence intervals describe a range of effect estimates compatible with the data under the analysis assumptions. In general, a narrower interval indicates greater precision, while a broad interval leaves more uncertainty about the size and direction of the effect. An interval containing zero for a risk difference is compatible with no difference, but it may also include nonzero effects. It therefore does not by itself show that two treatments are equivalent. Equivalence or noninferiority requires a defined margin and an analysis designed for that question; such a margin is not reported in the registry record.

The p-values listed for the comparisons are unadjusted. In general, an unadjusted p-value evaluates one contrast without accounting for the fact that multiple outcomes or comparisons may be examined. When many comparisons are considered, the chance of seeing a small p-value by chance can increase. Whether and how to address that issue depends on the prespecified analysis plan and the role of each endpoint. The registry record does not report a multiplicity strategy or a hierarchy for the outcomes, so the secondary p-values should be treated as exploratory rather than as a collection of confirmatory tests.

Part II secondary outcomes include counts for no vomiting and complete response within the stated time windows, as well as vomiting frequency. The available posted comparisons use risk differences for binary outcomes. In general, for a binary outcome a confidence interval around a risk difference conveys uncertainty in the difference in event proportions; it does not describe uncertainty about every possible clinical consequence. The registry does not list formal analyses for these outcomes. The outcome record also does not report a detailed model or adjustment strategy, so adjusted treatment estimates should not be inferred.

For an event-count endpoint, the number of participants with an event is not the same as the total number of events. The primary endpoint is explicitly the number of participants experiencing adverse events. The separate serious and other adverse-event records likewise give participant counts for each group. Those counts do not reveal whether an individual experienced more than one event, or whether events were related to study medication.

The sample-size illustrations use the observed effect as a planning reference and show scenarios based on detecting the stated fraction of that effect. The accompanying assumptions specify a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They are planning calculations, not the study’s original sample-size justification. The original design assumptions and sample-size rationale are not reported in the registry record. These illustrations should therefore be distinguished from evidence about the design process or the study’s achieved ability to detect an effect.

General statistical caution is particularly important when estimates are based on modest group sizes and relatively few events. A change in a small number of observed participants can affect the estimated proportion and its uncertainty. Over-dispersion is more relevant to counts or clustered data than to the simple participant-level binary endpoint; if repeated events or clustering were analyzed, a model that accounts for extra variability could be important. The registry’s primary endpoint is a count of participants with events, and it does not report a repeated-event model. No such model should be assumed.

The analysis population is specified for the primary endpoint as participants who received at least one dose. That is a treated-participant population, not necessarily an intention-to-treat population. The record does not report how participants with missing outcome information were handled, whether all randomized participants were analyzed as assigned, or how protocol deviations were treated. Those details matter because exclusions and missing observations can affect estimates, especially if the reasons for missingness are related to outcomes or treatment.

11. Confidence Intervals and Precision

The primary confidence intervals are wide relative to the point estimates. For Part II aprepitant compared with Part I aprepitant, the risk difference is 0.010 and the interval extends from -0.226 to 0.246. For Part II ondansetron compared with Part I aprepitant, the risk difference is -0.155 and the interval extends from -0.382 to 0.072. Each interval includes zero, so the posted data are compatible with no risk difference under the analysis used. They also include nonzero values in at least one direction, leaving uncertainty about the size of any difference.

In general, a confidence interval is not a guarantee that the true effect lies within its bounds. It summarizes the uncertainty of an estimate under the statistical method and assumptions. A broad interval indicates that the data do not pin down the effect precisely. It is not evidence that the effects are identical, and a nonsignificant p-value is not a substitute for an equivalence analysis. The registry does not report an equivalence margin or a noninferiority objective.

Precision is limited by the group sizes and the number of observed participants with the endpoint. This is especially relevant to the comparisons that use the Part I group as their reference: they cross study parts and do not estimate the randomized Part II contrast. The secondary risk-difference intervals are also broad and include zero. Their uncertainty, together with the absence of a reported multiplicity plan, counsels against treating isolated secondary findings as definitive. The estimates are informative as descriptions of the posted data, but they do not support narrow conclusions about treatment differences.

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 illustrations are planning scenarios based on the observed effect, not a report of the trial’s original design rationale. For these binary outcomes, the entries are participants per arm. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect as the effect to detect. The original study’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under the assumptions. The 90% power column gives the corresponding planning count for a 90% chance. These are design illustrations, not probabilities that the completed study’s result is correct or that a treatment effect exists. They are also not observed power.

Smaller effects require more participants to detect under the same assumptions. Thus, planning for 75% or 50% of the observed effect produces larger per-arm requirements than planning for 100% of that effect. The primary comparison based on the near-zero observed risk difference yields very large planning requirements: for 100% of that effect, the illustrations list 41,426 participants per arm for 80% power and 55,457 for 90% power. The primary comparison using the other reference contrast lists 150 and 200 participants per arm, respectively, for 100% of the observed effect. These figures are highly dependent on the effect chosen as the planning target; they should not be interpreted as evidence about what the original investigators planned.

The curve should be read in the same way as the numerical scenarios: it depicts planning requirements under the stated assumptions as the target effect changes. It does not show observed outcomes or establish that the study was adequately powered. Because the registry does not report the original sample-size justification, these calculations serve only as illustrations of how effect size and desired power relate to planning requirements.

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 = 0.435; treatment proportion p₁ = 0.444; average p̄ = 0.440.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7019 = 1.3758.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7019 = 0.5907.
4. n = (1.3758 + 0.5907)² / (0.0097)² = 41,425.2, rounded up to 41,426 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 <- 0.434782608695652                          # control proportion
p1 <- 0.444444444444444                          # 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(819039)
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 = 41,426 (80% power), 55,457 (90% power)
 75% of observed effect: n per arm = 73,602 (80% power), 98,532 (90% power)
 50% of observed effect: n per arm = 165,505 (80% power), 221,563 (90% power)
power.prop.test: 41425.2 
Simulated power at n = 41,426 per arm: 0.797 (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

The registry lists 12 outcome measures and five secondary outcomes. Multiple outcomes can raise a multiplicity concern: the more comparisons considered, the greater the chance that at least one result may appear notable by chance, even when no corresponding effect exists. This is a general statistical concern, not evidence that any particular finding in this study is false. The registry does not report whether the investigators used a hierarchy, adjusted significance thresholds, or another prespecified strategy to manage multiplicity. The posted p-values are unadjusted.

Without a stated multiplicity plan, the outcomes should not be treated as a set of independent confirmatory tests. Secondary findings are best considered descriptive or exploratory, particularly when their confidence intervals are broad and the outcome analyses are not listed as formal analyses in the registry. The registry’s outcome listing alone does not establish which outcomes were prespecified as key secondary outcomes or how they were intended to support a primary conclusion.

Missing-data handling is also not reported in the registry record. The record does not say how many outcome observations, if any, were missing; what reasons were recorded; whether participants with incomplete follow-up were excluded; or whether imputation or sensitivity analyses were used. It also does not report whether adverse events were collected consistently for all participants through the stated timeframe. Without these details, the potential influence of missing information cannot be evaluated.

The primary endpoint population is described as participants who received at least one dose of study medication. The record does not identify this population as intention-to-treat, nor does it explain how randomized participants who did not receive treatment would be handled. Details on analysis according to assigned treatment, protocol deviations, and adherence are not reported. Those issues matter most for interpretation of the randomized Part II comparison. The registry also does not report a detailed statistical analysis plan, interim analyses, or original sample-size justification. No assumptions about these procedures should be made.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: incision site infection (4.3%), pneumonia (3.7%), anastomotic complication (2.2%).

The serious adverse-event records list 3 affected participants in Part I aprepitant, 2 in Part II aprepitant, and 0 in Part II intravenous ondansetron. The numbers at risk for these records are 46, 27, and 25, respectively. The other-adverse-event counts are 14, 5, and 4 in those same groups. These are participant counts, not totals of separate events. The registry does not report deaths in the provided adverse-event records.

The registry lists Incision Site Infection at 4.3%, Pneumonia at 3.7%, and Anastomotic Complication at 2.2% among the top serious-event terms. The record does not establish from these entries which treatment group each term occurred in, nor do the terms alone indicate causality or severity for an individual participant. Serious events should be read as reported safety observations, not as proof that study medication caused them.

As with the primary comparisons, the Part I cohort is distinct from the randomized Part II groups. Counts across those groups are not a randomized safety comparison. The small group records and lack of detailed event-level context limit conclusions about relative safety.

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

The posted findings describe adverse-event counts and several vomiting-related outcomes in a two-part pediatric surgical study. They do not establish that aprepitant or ondansetron prevented postoperative vomiting, and they do not establish that one treatment is safer than the other. The primary endpoint is a safety measure, while vomiting outcomes are secondary. Keeping those questions separate is essential to interpreting the record.

The Part II aprepitant and ondansetron groups were randomized, but the posted primary comparisons use the open-label Part I aprepitant group as their reference. Those primary contrasts are therefore not the randomized treatment comparison. The results should not be described as a direct randomized comparison of adverse-event risk between Part II aprepitant and ondansetron. The record does not report a primary outcome analysis making that contrast.

The estimates are imprecise, with intervals that include no difference and also allow nonzero differences. This means the data do not establish a clear difference in the reported contrasts; it does not demonstrate equivalence or rule out meaningful differences. The secondary outcomes also have uncertainty, and their unadjusted analysis status and the unreported multiplicity strategy limit the strength of conclusions that can be drawn from them.

The study description emphasizes pharmacokinetics, safety and tolerability as inputs to determining an appropriate dosing regimen for pediatric participants aged 6 months to 17 years. The record offers observations relevant to those aims, but it does not supply all details needed for a full assessment of the analysis, including missing-data methods and the original statistical plan. The results should therefore be read as registry-reported findings from this study, not as a standalone basis for clinical decisions or as a definitive evaluation of treatment efficacy.

17. Why This Trial Matters Statistically

This study illustrates why design structure matters as much as the numerical estimate. A registry can label an overall study randomized while containing more than one part with different purposes and methods. Here, Part I was an open-label pharmacokinetic investigation, and Part II was a randomized, double-blind comparison. A contrast that uses the Part I group as its reference does not inherit the protection against confounding offered by randomization in Part II.

It also illustrates the value of matching the interpretation to the endpoint. The primary outcome counts participants experiencing adverse events, whereas the secondary outcomes concern vomiting and complete response. Those measures answer different questions. A safety count cannot stand in for an efficacy outcome, and a secondary vomiting result does not automatically clarify the safety comparison.

Precision is another central issue. Confidence intervals show that the posted estimates leave substantial uncertainty about the magnitude and direction of differences. A p-value alone cannot convey that uncertainty or establish equivalence. The sample-size illustrations likewise depend strongly on the chosen effect size and planning assumptions; they are not observed power and do not replace the original design rationale, which is not reported in the registry.

Finally, several features needed for a stronger statistical assessment are not reported, including a multiplicity strategy, missing-data handling, and detailed analysis methods. Recognizing these gaps is not a judgment about the investigators’ work; it defines what can reasonably be concluded from the registry record. The study is a useful example of why estimates, intervals, trial structure, endpoint definitions, and reporting completeness must be considered together.

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.

Several limitations specific to this record affect interpretation. First, the primary comparisons use the Part I aprepitant group as reference, while Part I was open-label and Part II was randomized and double-blind. The primary estimates therefore do not provide a randomized comparison between the Part II treatments. The registry does not report an alternative primary analysis directly contrasting the randomized Part II groups.

Second, the endpoint is a count of participants with adverse events up to 21 days after surgery. The record does not provide event-level detail sufficient to assess timing, recurrence, severity for each event, or whether events were attributed to study medication. The serious-event terms and percentages are listed, but their group attribution is not reported in the record.

Third, the registry does not report missing-data handling, a detailed analysis plan, multiplicity procedures, or the original sample-size justification. The analysis population is described for the primary endpoint, but the handling of randomized participants who did not receive treatment and the handling of protocol deviations are not reported. These omissions make it difficult to assess potential analysis biases.

Finally, confidence intervals are broad, and the secondary results are unadjusted. The number of outcome measures and secondary outcomes makes selective emphasis on individual results especially difficult to justify without a prespecified hierarchy. The registry reports no formal analyses in its analysis listing. These limitations constrain the conclusions to descriptive interpretation of the posted data.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Aprepitant (MK-0869) in Pediatric Participants Undergoing Surgery (MK-0869-148) — NCT00819039.
• Registry record last updated 2021-01-26; status last verified 2021-01.
• Results first posted 2014-02-14.
• 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

NCT00819039 is a completed Phase 1, multicenter, two-part study of aprepitant in pediatric participants undergoing surgery. Part I was an open-label pharmacokinetic investigation of a single oral aprepitant dose; Part II was a randomized, double-blind comparison of single-dose oral aprepitant and intravenous ondansetron. The study description identifies pharmacokinetics, safety and tolerability as aims related to determining an appropriate dosing regimen.

The primary endpoint counts participants experiencing adverse events up to 21 days after surgery among those receiving at least one dose. Its posted comparisons use the Part I group as reference and should not be interpreted as the randomized Part II contrast. Secondary outcomes address vomiting-related results, but the registry does not report a multiplicity strategy, missing-data methods, or a detailed analysis plan. The estimates are descriptive and imprecise; they do not establish efficacy, equivalence, or a safety difference.